Author Response

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

Reviewer #1 (Recommendations For The Authors):

Some sentences need to be clarified and some additional data and references could be added.

1) Line 18

SRY is the sex-determining gene

SRY is the testis-determining gene is more accurate as described in line 44

Modification done

2) Line 50

Despite losing its function in early testis determination in mice, DMRT1 retained part of this function in adulthood when it is necessary to maintain Sertoli cell identity.

Losing its function is misleading. The authors describe firstly that Dmrt1 has no obvious function in embryonic testis development but is critical for the maintenance of Sertoli cells in adult mice. The wording "losing its function in early testis" is confusing. Do the authors mean that despite the expression of Dmrt1 in early testis development, the function of Dmrt1 seems to be restricted to adults in mice? A comparison between the testis and ovary should be more cautious since GarciaAlonso et al (2022) have shown that the transcriptomics of supporting cells between humans and mice is partly different.

That’s what we thought, and the sentence has been changed as follow: “Although DMRT1 is not required for testis determination in mice, it retained part of its function in adulthood when it is necessary to maintain Sertoli cell identity.” (line 51 to 53)

3) Line 78

XY DMRT1-/- rabbits showed early male-to-female sex reversal.

Sex reversal indicates that there is no transient Sertoli cell differentiation that transdifferentiate into granulosa cells. This brings us to an interesting point. In the case of reprogramming, the transient Sertoli cells can produce AMH leading to the regression of the Mullerian ducts. In humans, some 9pdeleted XY patients have Mullerian duct remnants and feminized external genitalia. This finding indicates early defects in testis development.

Is there also feminized external genitalia in XY Dmrt1−/− rabbits. Can the authors comment on the phenotype of the ducts?

We proposed to add “and complete female genitalia” at the end of the following sentence: “Secondly, thanks to our CRISPR/Cas9 genetically modified rabbit model, we demonstrated that DMRT1 was required for testis differentiation since XY DMRT1-/- rabbits showed early male-tofemale sex reversal with differentiating ovaries and complete female genitalia.” (line 77 to 80)

Indeed, since the first stage (16 dpc) where we can predict the sex of the individual by observing its gonads during dissection, we always predict a female sex for XY DMRT1 KO fetuses. It is only genotyping that reveals an XY genotype. At birth, our rabbits are sexed by technicians from the facility and again, but now based on the external genitalia, they always phenotype these rabbits as female ones. In these XY KO rabbits, the supporting cells never differentiate into Sertoli, and ovarian differentiation occurs as early as in XX animals. Thus, these animals are fully feminized with female internal and external genitalia. Most of 9p-deleted patients are not homozygous for the loss-offunction of DMRT1, and the remaining wild-type allele could explain the discrepancy between KO rabbits and humans.

4) Line 53

In the ovary, an equivalent to DMRT1 was observed since FOXL2 (Forkhead family box L2) is expressed in female supporting cells very early in development.

Can the authors clarify what is the equivalent of DMRT1, is it FOXL2? DMRT1 heterozygous mutations result in XY gonad dysgenesis suggesting haploinsufficiency of DMRT1. However, to my knowledge, there is no evidence of haploinsufficiency in XX babies. Thus can we compare testis and ovarian genetics?

We agree, the term “equivalent” is ambiguous, and we changed the sentence as follows: “In ovarian differentiation, FOXL2 (Forkhead family box L2) showed a similar function discrepancy between mice and goats as DMRT1 in the testis pathway. In the mouse, Foxl2 is expressed in female supporting cells early in development but does not appear necessary for fetal ovary differentiation. On the contrary, it is required in adult granulosa cells to maintain female-supporting cell identity.” (line 53 to 56)

Regarding reviewer 2's question on haploinsufficiency in humans: the patient described in Murphy et al., 2015 is an XY individual with complete gonadal dysgenesis. But, it has been shown that the mutation carried by this patient leads to a dominant-negative protein, equivalent to a homozygous state (Murphy et al., 2022).

For FOXL2 mutation in XX females, haploinsufficiency does not affect early ovarian differentiation (no sex reversal) but induces premature ovarian failure.

We agree with the reviewer, we cannot compare testis and ovarian genetics considering two different genes.

5) Line 55

In mice, Foxl2 does not appear necessary for fetal ovary differentiation (Uda et al., 2004), while it is required in adult granulosa cells to maintain female-supporting cell identity (Ottolenghi et al., 2005). The reference Uhlenhaut et al (2009) reporting the phenotype of the deletion of Foxl2 in adults should be added.

The reference has been added.

6) Line 64<br /> These observations in the goat suggested that DMRT1 could retain function in SOX9 activation and, thus, in testis determination in several mammals.

Lindeman et al (2021) have shown that DMRT1 can act as a pioneer factor to open chromatin upstream and Dmrt1 is expressed before Sry in mice (Raymond et al, 1999, Lei, Hornbaker et al, 2007). Whereas additional factors may compensate for the absence of Dmrt1, these results suggest that DMRT1 is also involved in Sox9 activation.

Dmrt1 is indeed expressed before Sry/Sox9 in the mouse gonad. However, no binding site for DMRT1 could be observed at Sox9 enhancer 13 in mice. This does not support a role for DMRT1 in the activation of Sox9 expression in this species. Furthermore, in Lindeman et al 2021, the authors clearly state that DMRT1 acts as a pioneering factor for SOX9 only after birth. It does not appear to have this role before. One of the explanations put forward is that the state of chromatin is different during fetal development in mice: chromatin is more permissive and does not require a factor to facilitate its opening. This hypothesis is based in particular on the description of a similar chromatin profile in the precursors of XX and XY fetal supporting cells, where many common regions display an open structure (Garcia-Moreno et al., 2019). Once sex determination and differentiation are established, a sex-specific epigenome is set up in gonadal cells. Chromatin remodeling agents are then needed to regulate gene expression. We hypothesize that in non-murine mammals such as rabbits, the state of gonadal cell chromatin would be different in the fetal period, more repressed, requiring the intervention of specific factors for its opening, such as DMRT1.

7) Figure 1

Most of the readers might not be familiar with the developmental stages of the gonad in rabbits. A diagram of the key stages in gonad development would facilitate the understanding of the results.

Thank you, it has been added in Figure 1.

8) Figure 2

Arrowheads are difficult to spot, could the authors use another color?

Done

9) Line 117: can the authors comment on the formation of the tunica albuginea? Do the epithelial cells acquire some specific characteristics?

The formation of the tunica albuginea begins with the formation of loose connective tissue beneath the surface epithelium of the male gonad. The appearance of this tissue is concomitant with the loss of expression of DMRT1 in the cell of the coelomic epithelium. Our interpretation is that the contribution of the cells from the coelomic epithelium and their proliferation stops when the tunica begins to form because the structure of the tissue beneath the epithelium change, and the cellular interactions between the epithelium and the tissue below remain disrupted. By contrast, these interactions persist in the ovary until around birth for ovigerous nest formation.

10) The first part of the results described DMRT1 expression in rabbits. With the new single-cell transcriptomic atlas of human gonads, it would be important to describe the pattern of expression in this species. This could be described in the introduction in order to know the DMRT1 expression pattern in the human gonad before that of the rabbit.

A comment on the expression pattern of DMRT1 in human fetal gonads has been added in the discussion section: “In the human fetal testis, DMRT1 expression is co-detected with SRY in early supporting gonadal cells (ESCGs), which become Sertoli cells following the activation of SOX9 expression (Garcia-Alonso et al., 2022) » (line 222 to 224)

11) Figure 3 supplement 3

Dotted line: delimitation of the ovarian surface epithelium. Could the authors check that there is a dotted line?

Done

12) Figure 5 and Line 186

Quantification is missing such as the % of germ cells, % of meiotic germ cells.

Quantification is not easy to realize in rabbits because of the size and the elongated shape of the gonad. Indeed, it’s difficult to be sure that both sections (one from WT, the other from KO) are strictly in a similar region of the gonad and that the section is perfectly longitudinal or not. See also our answer to reviewer 3 (point 7) on this aspect. Actually, we are trying to make a better characterization of this XX phenotype and to find a marker of the pre-leptotene/leptotene stage susceptible to work in rabbits (SYCP3 will be the best, but we encountered huge difficulties with different antibodies and even RNAscope probe!). So actually, the most convincing indirect evidence of this pre-meiotic blockage (in addition to HE staining at 18 dpp in the new Figure 6) is the persistence of POU5F1 (pluripotency), specifically in the germinal lineage of KO XX and XY gonads. In addition to the new figure supplement 5, we can show you in Author response image 1: (i) the gonadal section at a lower magnification, where it is evident that there is a big difference between WT and KO germ cell POU5F1-stainings; and (ii) POU5F1 expression from a bulk RNA-seq realized the day after birth at 1 dpp where the difference is also transcriptionally very clear.

Author response image 1.

13) Line 186,

E is missing at preleptoten

Added

14) Figure supplement 7.

A magnification of the histology of the gonads is missing.

This figure is only for showing the gonadal size, and there are the same gonads as in the new Figure 6. So, the magnification is represented in Figure 6.

15)Discussion

Line 201

SOX9, well known in vertebrates,

The references of the human DSD associated with SOX9 mutations are missing. Thank you, references have been added.

16) Line 286

One of the targets of WNT signaling is Bmp2 in the somatic cells and in turn, Zglp1, which is required for meiosis entry in the ovary as shown by Miyauchi et al (2017) and Nagaoka et al (2020). Does the level of BMP pathway vary in DMRT1 mutants?

At 20 dpc, the expression level of BMP2 in XY and XX DMRT1 mutants gonads is similar to the one of XX control which is lower than in XY control (see the TMP values from our RNA-seq in Author response image 2).

Author response image 2.

Reviewer #2 (Recommendations For The Authors):

Here are my minor comments:

1) Line 106- You mention that coelomic epithelial cells only express DMRT1. Please add an arrow to highlight where you refer to.

Done

2) Line 112: In mice, the SLCs also express Sox9 but not Sry apart from Pax8. You mention here that the SLCs are expressing SRY and DMRT1 in addition to PAX8. Could you perhaps explain the difference? Please refer to that in the results or discussion.

We add a new sentence at the end of this paragraph on SLCs: “As in mice, these cells will express SOX9 at the latter stages (few of them are already SOX9 positive at 15 dpc), but unlike mice, they express SRY.” (line 114 to 115)

We already have collaborations with different labs on these SLC cells, and we will certainly come back later on this aspect, remaining slightly off-topic here.

3) Could you please explain why did you chose to target Exon 3 of DMRT1 and not exons 1-2 which contain the DM domain? Was it to prevent damaging other DMRT proteins? Is there an important domain or function in Exon 2?

Our choice was mainly based on technical issues (rabbit genome annotation & sgRNA design), but also we want to avoid targeting the DM domain due to its strong conservation with other DMRT genes. Due to the poor quality of the rabbit genome, exons 1 and 2 are not well annotated in this species. We have amplified and sequenced the region encompassing exons 1 & 2 from our rabbit line, but the software used for sgRNA design does not predict good guides on this region. The two best sgRNAs were predicted on exon 3, and we used both to obtain more mutated alleles.

4) Your scheme in Supp Figure 4 is not so clear. It is not clear that the black box between the two guides is part of Exon 3 (labelled in blue).

The scheme has been improved.

5) Did you only have 1 good founder rabbit in your experiment? Why did you choose to work with a line that had duplication rather than deletion?

Very good point! In the first version of this paper, we’d try to explain the long (around 2 years) story of breeding to obtain the founder animal. Here it is:

During the genome editing process, we generate 6 mosaic founder animals (5 males and 1 female), then we cross them with wild-type animals to isolate each mutated allele in F1 offspring used afterward to establish and amplify knockout lines. Unexpectedly, we observe a very slow ratio of mutated allele transmission (5 on 129 F1 animals), and only one mutated allele has been conserved from the unique surviving adult F1 animal. It consists of an insertion of the deleted 47 bp DNA fragment, flanked by the cutting sites of the two RNA guides used with Cas9.<br /> The main hypothesis to explain this mutation event is that in the same embryonic cell, the deletion occurs on one allele then the deleted fragment remains inserted into the other allele. Under this scheme, the embryonic cell carries a homozygous DMRT1 knockout genotype, albeit heterogeneous, with a deleted allele (del47) and the present allele (insertion of a 47 bp fragment leading to an in sense duplication). This may explain the very low frequency of transmission since all germ cells carrying a homozygous DMRT1-/- genotype will probably not be able to enter the meiotic process as suggested by our results on XX and XY DMRT1-/- ovaries. Finally, and under this hypothesis, the way we obtained this unique founder animal remains a mystery!

6) Figure 4- real-time data- where does it say what is a,b,c,d of the significance? It should appear on the figure itself and not elsewhere.

Modification done.

7) If I understand correctly, you were able to get the rabbits born and kept to adulthood (you show in supp figure 7 their gonads). What was the external phenotype of these rabbits? Did the XY mutant gonads have the internal and external genitals of a female (oviduct, uterus, vagina etc.)?

See our answer to Reviewer 1 on this question (point 3).

8) Line 20: It is more correct to write 46, XY DSD rather than XY DSD

Modification done.

9) Line 21: you can remove the "the" after abolished

Modification done.

10) Line 31: consider replacing the first "and" by "as well as" since the sentence sounds strange with two "and".

Modification done.

11) Line 212- Please check with the eLife guidelines if they allow "data not shown" in the paper.

This is unspecified.

Reviewer #3 (Recommendations For The Authors):

The following points should be addressed.

1) The in situ's in Fig 1 and 2 are very clear. Fig 1 and Fig 2, In situ hybridisation in tissue sections, it looked like DMRT1 could be expressed in some cells where SRY mRNA is absent @ E13.5dpc and 14.5 dpc. Do you think this is real, or maybe Sry is turned off now in those cells?

Based on the results of in situ hybridizations, DMRT1 appears to be expressed by both coelomic epithelium and genital crest medullar cells in a pattern that is actually broader than that of SRY. Moreover, in rabbits, SRY expression seems to start in the medulla of the genital ridge rather than in the surface epithelium, as described in mice (see Figure 1 at 12 and 13 dpc). Nevertheless, more detailed analyses are needed to ensure the lineage of cells expressing SRY and/or DMRT1, such as single-cell RNAseq at these key stages of sexual determination in rabbits (from 12 to 16 dpc).

2) It is curious that SRY expression is elevated in the DMRT1 KO (Knockout) rabbit gonads. Does this suggest feedback inhibition by DMRt1, or maybe indirect via effect on Sox9 (as I believe Sox9 feeds back to down-regulate Sry in mouse, for example).

The maintenance of SRY expression in the DMRT1 -/- rabbit testis seems to be linked to the absence of SOX9 expression. We believe that, as in mice, SOX9 would down-regulate SRY (even if, in rabbits, SRY expression is never completely turned off).

3) I suggest the targeting strategy and proof of DMRT1 knockout by sequencing etc. be brought out of the suppl. Data and shown as a figure in the text.

See also our answer to reviewer 2 (point 5). It has needed huge efforts to obtain these DMRT1 mutated rabbit line, and of course, it constitutes the basis of the study. But regarding the title and the main message of the article, we are not convinced that the targeting strategy should be moved into the main text.

4) Unless there are limitations imposed by the journal, I also feel that Suppl Fig 5 (the immunostaining) deserves to be in the paper text too. The Fig showing loss of DMRt1 by immunostaining is important.

We include the figure supplement 5 in the main text. So, Figure 4E and figure supplement 5 have been combined into a new Figure 5.

5) The RT-qPCR data should have the statistics clarified on the graphs. (e.g., it is stated that, although Sox9 mRNA is clearly down, there is a slight increase compared to control on KO XX gonads. Is this statistically significant? Figure legend states that the Kruskal-Wallis test is used, and significance is shown by letters. This is unclear. It would be better to use the more usual asterisks and lines to show comparisons.

Modification done.

6) Reference is made to DMRT1+/- rabbits having aberrant germ cell development, pointing to a dosage effect. This is interesting. Does the somatic part of the gonad look completely normal in the het knockouts?

DMRT1 heterozygous male rabbits have a phenotype of secondary infertility with aging, and we are trying now to better characterize this phenotype. The problem is complex because, as we cannot carry out conditional KO, it remains difficult to decipher the consequence of DMRT1 haploinsufficiency in the Sertoli cells versus the germinal ones. Anyway, the somatic part is sufficiently normal to support spermatogenesis since heterozygous males are fertile at puberty and for some months thereafter.

7) Can the authors indicate why meiotic markers were not used to explore the germ cell phenotype? It would be advantageous to use a meiotic germ cell marker to definitely show that the germ cells do not enter meiosis after DMRT1 loss. (Not just H/E staining or maintenance of POU). Example SYCP3, or STRA8 (as pre-meiotic marker) by in situ or immunostaining. Even though no germ cells were detected in adult KO gonads.

The expression of pre-meiotic or meiotic markers is currently under study in DMRT1 -/- females. Transcriptomic data (RNA-seq) are also being analyzed. We are preparing a specific article on the role of DMRT1 in ovarian differentiation in rabbits. We felt it was important to reveal the phenotype observed in females in this first article, but we still need time to refine our description and understanding of the role of DMRT1 in the female.

8) What future studies could be conducted? In the Discussion section, it is suggested that DMRT1 could act as a pioneering factor to allow SRY action upon Sox9. How could this be further explored?

To explore the function of DMRT1 as a pioneering factor, it now seems necessary to characterize the epigenetic landscapes of rabbit fetal gonads expressing or not DMRT1 (comparison of control and DMRT1-/- gonads). Two complementary approaches could be privileged: the study of chromatin opening (ATAC-seq) and the analysis of the activation state of regulatory regions (CUT&Tag). The study of several histone marks, such as H3K4me3 (active promoters), H3K4me1 (primed enhancers), H3K27ac (enhancers and active promoters), and H3K27me3 (enhancers and repressed promoters), would be of great interest. However, these techniques are only relevant for gonads that can be separated from the adjacent mesonephros, which is only possible from the 16 dpc stage in rabbits. To perform a relevant analysis at earlier stages, a "single-nucleus" approach such as ATAC-seq singlenucleus or multi-omic single-nucleus combining ATAC-seq and RNA-seq could be used.

Author Response

The following is the authors’ response to the previous reviews

Reviewer #1:

Comment on revised manuscript: Thank you for your responses - they have addressed most of my concerns.

We thank the reviewer again for their assistance in improving our manuscript.

Reviewer #2:

Additional context:

The sex differences between the samples are interesting as effects of sex are commonly found in AAC tasks. It would be interesting to look at the main model comparison with sex included as a covariate.

Firstly, we thank the reviewer for their re-evaluation of our manuscript.

To the reviewer’s comment, we apologise for the lack of clarity. The analyses included in our revision were indeed based on the main logistic regression model of choice, including sex and age as covariates. We have clarified this in the manuscript as follows:

While sex was significantly associated with choice in the hierarchical logistic regression in the discovery sample (β = 0.16 ± 0.07, p = 0.028) with males being more likely to choose the conflict option, this pattern was not evident in the replication sample (β = 0.08 ± 0.06, p = 0.173), and age was not associated with choice in either sample (p > 0.2).

As it is difficult to include sex as a covariate in the reinforcement learning models in the classical sense as in a linear regression, we assessed sex effects on the individual parameters produced by these models instead, as follows:

Comparing parameters across sexes via Welch’s t-tests revealed significant differences in reward sensitivity (t289 = -2.87, p = 0.004, d = 0.34; lower in females) and consequently reward-punishment sensitivity index (t336 = -2.03, p = 0.043, d = 0.22; lower in females i.e. more avoidance-driven). In the replication sample, we observed the same effect on reward-punishment sensitivity index (t626 = -2.79, p = 0.005, d = 0.22; lower in females). However, the sex difference in reward sensitivity did not replicate (p = 0.441), although we did observe a significant sex difference in punishment sensitivity in the replication sample (t626 = 2.26, p = 0.024, d = 0.18).

Could the authors double check the mean/SD of approach in each group for typos? The numbers are identical.

Thank you for spotting this – the means were indeed similar (discovery: 0.521, replication: 0.516), but the standard deviations were marginally different (discovery: 0.140, replication: 0.148). We have amended the manuscript to reflect this, as follows:

Across individuals, there was considerable variability in overall choice proportions (discovery sample: mean = 0.52, SD = 0.14, min/max = [0.03, 0.96]; replication sample: mean = 0.52, SD = 0.15, min/max = [0.01, 0.99]).

Reviewer #3:

The revised paper commendably adds important additional information and analyses to support these claims. The initial concern that not accounting for participant control over punisher intensity confounded interpretation of effects has been largely addressed in follow-up analyses and discussion.

I commend the authors on their revisions. My initial concerns have been largely addressed. Minor suggestions below.

We thank the reviewer again for their assistance in improving our analyses and manuscript.

Changing the visualisation of the logistic regression model in Figure 2 to tertiles instead of quartiles seems expedient, and does not properly address the points raised by the other reviewers. The argument that non-linear trends in the extreme bins are due to less data is plausible, but unsatisfying given how reliable the pattern seems to be (across samples, with small standard error) and . It is possible, albeit perplexing, that the influence of punishment probability on choice is non-linear. I think the current figure with tertiles is acceptable, but I would suggest including the figures with non-linear data as a supplementary figure, for sake of transparency and reader interest.

We agree that this is likely more complex than a simple linear effect (in the logistic space), especially given the concurrent reward probabilities which also fluctuate in the task. We also agree that the non-linear figures should be made available in the interests of transparency, and have included them in the Supplementary Materials.

We direct interested readers to the relevant section from the figure legend as follows:

"Figure 2. Predictors of choice in the approach-avoidance reinforcement learning task. … We show linear curves here since these effects were estimated as linear effects in the logistic regression models, however the raw data showed non-linear trends – see Supplementary Figure 15."

We have included the non-linear figures in Supplementary Section 9.11 Effects of outcome probabilities on choice in the task: non-linear effects as Supplementary Figure 15.

As an aside, the argument that approach-avoidance joystick tasks do not have a non-human counterpart misconstrues the translational root of these tasks, which was (at least in part) an attempt to model (successfully or not) general approach/avoidance processes measured in non-human tasks, e.g. appetitive/aversive runway tasks using rodents.

Our aim in this manuscript was to develop a task that was closely matched to non-human counterparts in both the experimental procedure (choice over reward/punishment outcomes) and cognitive process involved (simultaneous reward/punishment learning). With this in mind, we wanted to convey that non-human and human measures of approach/avoidance processes were historically distinct in terms of the procedures (e.g. using a joystick vs navigating a runway, due to ethological differences), and that this was potentially problematic with respect to computational validity. However, at this early point in the introduction, it was unnecessary to make a strong distinction between these tasks, which as the reviewer duly notes, follow similar approach/avoidance principles and share similar experimental roots. Therefore, we have opted to omit the reference to translational similarity in the relevant text, as follows:

In humans, on the other hand, approach-avoidance conflict has historically been measured using questionnaires such as the Behavioural Inhibition/Activation Scale (Carver and White 1994), or cognitive tasks that rely on motor/response time biases, for example by using joysticks to approach/move towards positive stimuli and avoid/move away from negative stimuli (Guitart-Masip, Huys et al. 2012, Phaf, Mohr et al. 2014, Kirlic, Young et al. 2017, Mkrtchian, Aylward et al. 2017).

Author Response

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

Reviewer #1 (Public Review):

This manuscript by He et al. explores the molecular basis of the different stinging behaviors of two related anemones. The freshwater Nematostella which only stings when a food stimulus is presented with mechanical stimulation and the saltwater Exaiptasia which stings in response to mechanical stimuli. The authors had previously shown that Nematostella stinging is calcium-dependent and mediated by a voltage-gated calcium channel (VGCC) with very pronounced voltage-dependent inactivation, which gets removed upon hyperpolarization produced by taste receptors.

In this manuscript, they show that Exaiptacia and Nematostella differing stinging behavior is near optimal, according to their ecological niche, and conforms to predictions from a Markov decision model.

It is also shown that Exaiptacia stinging is also calcium-dependent, but the calcium channel responsible is much less inactivated at resting potential and can readily induce nematocyte discharge only in the presence of mechanical stimulation. To this end, the authors record calcium currents from Exaipacia nematocysts and discover that the VGCCs in this anemone are not strongly inactivated and thus are easily activated by mechanical stimuli-induced depolarization accounting for the different stinging behavior between species. The authors further explore the role of the auxiliary beta subunit in the modulation of VGCC inactivation and show that different n-terminal splice variants in Exaiptacia produce strong and weak voltage-dependent inactivation.

The manuscript is clear and well-written and the conclusions are in general supported by the experiments and analysis. The findings are very relevant to increase our understanding of the molecular basis of non-neural behavior and its evolutionary basis. This manuscript should be of general interest to biologists as well as to more specialized fields such as ion channel biophysics and physiology.

Some findings need to be clarified and perhaps additional experiments performed.

1) The authors identify by sequencing that the Exaiptacia Cav is a P-type channel (cacna1a). However, the biophysical properties of the nematocyte channel are different from mammalian P-type channels. The cnidarian channel inactivation is exceedingly rapid and activation happens at relatively low voltages. These substantial differences should be mentioned and commented on.

First, we thank Reviewer 1 for thoughtful and detail-oriented comments, as well as their shared appreciation for the molecular basis of unique behaviors. Indeed, Nematostella and rat CaV channels exhibit striking differences in inactivation (both fast and steady-state). We previously described this in Weir et al., 2020 and added additonal text to ensure that this result is clear.

2) The currents from Nematostella in Figure 3d seem to be poorly voltage-clamped. Poor voltage-clamp is also evident in the sudden increase of conductance in Figure 3C and might contribute to incorrect estimation of voltage dependence of activation and if present in inactivation experiments, also to incorrect estimation of the inactivation voltage range. This problem should be reassessed with new data.

Because it is necessary to use small-tipped pipettes to get recordings from small and technically challenging nematocytes, there is imperfect voltage clamp that is evident in the steep activation curves. This issue should have little effect on the inactivation curves determined with 1s pre-pulses because poor voltage control occurs transiently at the beginning of the pre-pulse. In our case, current is measured in response to a brief maximally activating pulse followed by a nearly 1s period. Thus, error should be minimal in inactivation curves if the test pulse is a maximally activating voltage. We ensured that these protocols are clearly described in the Methods to address this issue. In addition, we are confident in the described inactivation values because they are generally consistent with channel properties measured in a heterologous expression system in which we do not have this problem and see the same differences in inactivation (also see Weir et al., 2020).

3) While co-expression of the mouse Cav channel with the beta1 isoform from Exaiptacia indeed shifts inactivation to more negative voltages, it does not recapitulate the phenotype of the more inactivated Ca-currents in nematocytes (compare Figures 4d and 5d). It should be explained if this might be due to the use of a mammalian alpha subunit. Related to this, did the authors clone the alpha subunit from Exaiptacia? Using this to characterize the effect of beta subunits on inactivation might be more accurate.

While the cnidarian CaVβ subunits indeed shift inactivation consistent with native properties, we agree that using the Exaiptasia alpha subunit would be more accurate. We were unable to successfully clone and heterologously express this subunit, however, we did express all subunits from Nematostella and made chimeric channels in which alpha, alpha2d, or CaVβ were swapped between Nematostella and mammalian channels. These experiments demonstrated the requirement and sufficiency of the CaVβ subunit in altering inactivation (Weir et al., 2020). Furthermore, we were able to express CaVβ subunits from a variety of other cnidarians, all of which affected inactivation properties. Thus, we are confident in the conclusion that CaVβ subunits are major contributors to molecular tuning of cnidarian CaV channels. Future studies aim to incorporate describing properties of the alpha subunit from Exaiptasia and other cnidarians.

4) The in situ shown in Figure 4b are difficult to follow for a non-expert in cnidarian anatomy. Some guidance should be provided to understand the structures. Also, for the left panels, is the larger panel the two-channel image? If so, blue would indicate co-localization of the two isoforms and there seems to be a red mark in the same nematocyte.

We thank the reviewer for this important comment and have modified the figure to enhance visual guidance. We more clearly highlighted the nematocyte in the single and two-channel images and selected the clearest representative images. For additional reference, previous studies beautifully illustrate the unusual morphology of nematocytes, including the relative localization of the nematocyst and nucleus in the context of cnidarian tissues (Babonis and Martindale, 2017).

Reviewer #2 (Public Review):

This manuscript links the distinctive stinging behavior of sea anemones in different ecological niches to varying inactivation properties of voltage-gated calcium channels that are conferred by the identity of auxiliary Cavbeta subunits. Previous work from the Bellono lab established that the burrowing anemone, Nematostella vectensis, expresses a CaV channel that is strongly inactivated at rest which requires a simultaneous delivery of prey extract and touch to elicit a stinging response, reflecting a precise stinging control adapted for predation. They show here that by contrast, the anemone Exaiptasia diaphana which inhabits exposed environments, indiscriminately stings for defense even in the absence of prey chemicals, and that this is enabled by the expression of a CaVbeta splice variant that confers weak inactivation. They further use the heterologous expression of CaV channels with wild type and chimeric anemone Cavbeta subunits to infer that the variable N-termini are important determinants of Cav channel inactivation properties.

1) The authors found that Exaiptasia nematocytes could be characterized by two distinct inactivation phenotypes: (1) nematocytes with low-voltage threshold inactivation similar to that of Nematostella (Vi1/2 = ~ -85mV); and (2) a distinct population with weak, high-voltage threshold inactivation (Vi1/2 = ~ -48mV). What were the relative fractions of low-voltage and high-voltage nematocytes? Do the low-voltage Exaiptasia nematocytes behave similarly to Nematostella nematocytes with respect to requiring both prey extract and touch to discharge?

We thank Reviewer 2 for thoughtful comments and questions. Nematocyte patch clamp is technically challenging due to small size, large nematocyst, and, notably, the explosive discharge involved in stinging! Therefore, we only patch clamped a small number of cells. Despite this limitation, we were able to observe two distinct nematocyte populations based on physiological properties. Yet, we did not observe a correlation with morphology and cannot make broad comments on relative fractions. Because morphology was generally similar and Exaiptasia nematocytes discharge even from touch alone, it remains unclear whether the low-voltage population behaves similarly to Nematostella nematocytes that only discharge in response to chemicals and touch. Future in vivo approaches could be used to address this question.

2) The authors state in Fig 3 legend and in the results that Exaiptasia nematocyte voltage-gated Ca2+ currents have weak inactivation compared with Nematostella. This description is imprecise and inaccurate. Figure 3 in fact shows that Exaiptasia nematocyte voltage-gated Ca2+ currents display a faster rate of inactivation compared to Nematostella Ca2+ currents. A sub-population of Exaiptasia nematocytes does display less resting state (or steady-state) inactivation compared to Nematostella Ca2+ currents. The authors need to be more accurate and qualify what type of inactivation property they are talking about.'

We thank Reviewer 2 for this attention to detail and have defined this phrasing early in the text.

3) In a similar vein, the authors need to be more accurate when referring to 'rat beta' used in heterologous expression experiments. It should be made explicit throughout the manuscript that the rat beta isoform used is rat beta2a. Among the distinct beta isoforms, beta2a is unique in being palmitoylated at the N-terminus which confers a characteristic slow rate of inactivation and a right-shifted voltage-dependence of steady-state inactivation consistent with the data shown in Fig. 4D. Almost all other rat beta isoforms do not have these properties.

We used the rat CaVβ2a for comparison because it shares the highest homology with Nematostella CaVβ (Weir et al., 2020). We have now more clearly defined the rat subunit in the text and legends.

4) The profiling of the impact of different Cnidarian Cavbeta subunits on reconstituted Ca2+ channel current waveforms is nice (Fig 5 and Fig 5S1). The N-terminus sequence of EdCaVβ2 is different from palmitoylated rat beta2a, though both have similar properties in showing slow inactivation and a right-shifted voltage-dependence of steady-state inactivation. Does EdCaVβ2 target autonomously the plasma membrane when expressed in cells? If so, this would reconcile with what was previously known and provide a rational explanation for the observed functional impact of the distinct Cavbetas.

As far as we understand the question, our data support that Exaiptasia CaVβ2 targets the plasma membrane for a number of reasons: 1) Expressing Exaiptasia CaVβ2 produces consistent properties in comparison with other CaVβs, suggesting a homogenous population of channel complexes; 2) Distinct cnidarian-Exaiptasia CaVβ2 chimeras produce distinct and internally consistent properties; and 3) Expressing P/Q-type CaV alpha + alpha2d subunits without CaVβ in cell lines does not produce robust measurable voltage-gated currents. We further tested this in our case and found the same result: at an equivalent maximally activating step using the same protocol, we measured 458.68 ± 179.88pA average current amplitude for +Exaiptasia CaVβ2 (n = 6) and 43.03 ± 17.64pA average current amplitude for -CaVβ2 (n = 4).

Reviewer #3 (Public Review):

Summary:

The present article attempts to answer both the ultimate question of why different stinging behaviours have evolved in Cnidiarians with different ecological niches and shed light on the proximate question of which electro-physiological mechanisms underlie these distinct behaviours.

Account of major methods and results:

In the first part of the paper, the authors try to answer the ultimate question of why distinct dependencies of the sting response on internal starvation levels have evolved. The premise of the article that Exaiptasia's nematocyte discharge is independent of the presence of prey (Artemia nauplii) as compared to Nematostella's significant dependence of the discharge on the presence of actual prey, is shown be a robust phenomenon justified by the data in Figure 1.

The hypothesis that defensive vs. predatory stinging leads to different nematocyte discharge behaviours is analysed in mathematical models based on the suitable framework of optimal control/decision theory. By assuming functional relations between the:

1) cost of a full nematocyte discharge and the starvation level.

2) probability of successful predation/avoidance on the discharge level.

3) desirability/reward of the reached nutritional state.

Based on these assumptions of environmental and internal influences, the optimal choice of attack intensity is calculated using Bellman's equation for this problem. The model predictions are validated using counted nematocytes on a coverslip. The scaling of normalised nematocyte discharge numbers with scaled starvation time is qualitatively comparable to what is predicted from the models. The abundance of nematocytes in the tentacles was, on the other hand, independent of the starvation state of the animals.

Next, the authors turn to investigate the proximate cause of the differential stinging behaviour. The authors have previously reported convincing evidence that a strongly inactivating Cav2.1 channel ortholog (nCav) is used by Nematostella to prevent stinging in the absence of prey (Weir et al. 2020). This inactivation is released by hyperpolarising sensory inputs signalling the presence of prey. In this article, it is clearly shown by blocking respective currents that Exaiptasia, too, relies on extracellular Ca2+ influx to initiate stinging. Patch clamp data of the involved currents is provided in support. However, the authors find that in addition to the nCav with a low-inactivation threshold, Exaiptasia has a splice variant with a higher inactivation threshold expressed (Figure 3D).

The authors hypothesise that it is this high-threshold nCav channel population that amplifies any voltage depolarisation to release a sting irrespective of the presence of prey signals. They found that the β subunit that is responsible for Nematostella's unusually low inactivation threshold exists in Exaiptasia as two alternative splice isoforms. These N-terminus variants also showed the greatest variation in a phylogenetic comparison (Figure 5), rendering it a candidate target for mutations causing variation in stinging responses.

Appraisal of methodology in support of the conclusions:

The authors base their inference on a normative model that yields quantitative predictions which is an exciting and challenging approach. The authors take care in stating the model assumptions as well as showing that the data indeed does not contradict their model predictions. The interesting comparative nature of the modelling part of the study is complicated by slightly different cost assumptions for the two scenarios. Hence, Figure 2 needs to be carefully digested by readers.

We thank the reviewer for their careful revision of our work and excellent comments. We simplified Figure 2 considerably to make it easier to digest. We now compare the stinging response for predation vs defense under the same exact definition of cost per nematocyte for both models. You can find examples 1 and 2 in Figure 2 and examples 3 and 4 in Supplementary Figure 3 (see response below).

It would be even more prudent to analyse the same set of cost-of-discharge vs. starvation scenarios for both species. Specifically, for Nematostella the complete cost-of-discharge vs starvation-state curves as for Exaiptasia (Figure 2E, example 2-4) could be used. It is likely that the differential effect size of Nematostella and Exaiptasia behaviour is the strongest if only the flat cost-of-discharge vs starvation is used (Figure 2A) for Nematostella. But as a worst-case comparison the other curves, where the cost to the animal scales with starvation would be a good comparison. This could help the reader to understand when the different prediction of Nematostella's behaviour breaks down. In addition, this minor change could shed light on broader topics like common trade-offs in pursuit predation.

The results hold even when the cost increases moderately with starvation: Figure 2 now shows results with the same cost for predatory and defensive stinging (cost defined in Figure 2A, former examples 1 and 4). Predatory stinging robustly increases with starvation and defensive stinging remains constant or decreases. Interestingly, the fit between theory and data for both anemones improves by using the increasing cost (open circles in Figure 2E right). For other choices of increasing cost functions, defensive stinging will always decrease, and even more so if the cost increases dramatically (like for the former Examples 2 and 3). In contrast, predatory stinging will switch behavior if the cost increases too much with starvation (results with former Examples 2 and 3, now in Supplementary Figure 3 and theoretical arguments in Supplementary Information). Note however that these assumptions are less realistic because they necessitate that the cost of stinging for well-fed animals is negligible with respect to the cost for starved animals. A formal proof of the asymptotic solution for predatory stinging with varying cost is beyond the scope of this work and is subject of ongoing work where we consider implications for Markov Decision Processes in continuous space state.

The qualitatively similar scaling of the model-derived relation between starvation and sting intensity with the counted nematocytes for different feeding pauses is evidence that feeding has indeed been optimised for the two distinct ecological niches. To prove that Exaiptasia uses a similar Ca2+ channel ortholog as well as a different splice variant, the authors employed both clean electrophysiological characterisaiton (Figure 3) as well as transcriptomics data (Figure 4S1).

To strengthen the authors' hypothesis that variation in the N-termini leads to changes in Ca2+ channel inactivation and hence altered stinging, the response sequence variability of 6 Cnidaria was analysed.

Additional context:

Although, the present article focuses on nematocytes alone, currently, there has been a refocus in neurobiology on the nervous systems of more basal metazoans, which received much attention already in the works of Romanes (1885). In part, this is driven by the goal to understand the early evolution of nervous systems. Cnidarians and Ctenophors are exciting model organisms in this venture. This will hopefully be accompanied by more comparative studies like the present one. Some of the recent literature also uses computational models to understand mechanisms of motor behaviour using full-body simulations (Pallasdies et al. 2019; Wang et al. 2023), which can be thought of as complementary to the normative modelling provided by the authors.

Comparative studies of recent Cnidarians, such as the present article, can shed light on speculative ideas on the origin of nervous systems (Jékely, Keijzer, and Godfrey-Smith 2015). During a time (the Ediacarium/Cambrium transition) that has seen the genesis of complex trophic foodwebs with preditor-prey interaction, symbioses, but also an increase of body sizes and shapes, multiple ultimate causes can be envisioned that drove the increase in behavioural complexity. The authors show that not all of it needs to be implemented in dedicated nerve cells.

References:

Jékely, Gáspár, Fred Keijzer, and Peter Godfrey-Smith. 2015. "An Option Space for Early Neural Evolution." Philosophical Transactions of the Royal Society B: Biological Sciences 370 (December): 20150181. https://doi.org/10.1098/rstb.2015.0181.

Pallasdies, Fabian, Sven Goedeke, Wilhelm Braun, and Raoul-Martin Memmesheimer. 2019. "From Single Neurons to Behavior in the Jellyfish Aurelia Aurita." eLife 8 (December). https://doi.org/10.7554/elife.50084.

Romanes, G. J. 1885. Jelly-Fish, Star-Fish and Sea-Urchins: Being a Research on Primitive Nervous Systems. Appleton.

Wang, Hengji, Joshua Swore, Shashank Sharma, John R. Szymanski, Rafael Yuste, Thomas L. Daniel, Michael Regnier, Martha M. Bosma, and Adrienne L. Fairhall. 2023. "A Complete Biomechanical Model of hydra Contractile Behaviors, from Neural Drive to Muscle to Movement." Proceedings of the National Academy of Sciences 120 (March). https://doi.org/10.1073/pnas.2210439120.

Weir, Keiko, Christophe Dupre, Lena van Giesen, Amy S-Y Lee, and Nicholas W Bellono. 2020. "A Molecular Filter for the Cnidarian Stinging Response." eLife 9 (May). https://doi.org/10.7554/elife.57578.

We appreciate the excellent suggestion to further discuss non-neuronal adaptations in the context of studying the evolution of behavior. We have added additional text to the Discussion to cover this interesting field.

Author Response

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

First and foremost, we would like to thank all the editors and reviewers for their thoughtful and thorough evaluations of our manuscript. We greatly appreciate their assessment about the novelty and strength in this study and have revised the manuscript according to their recommendations. Below are our detailed responses and revisions based on the reviewer recommendations.

Reviewer #1 (Recommendations For The Authors):

1) It is unclear the rationale for choosing the P35-42 adolescent window for stimulating the mesofrontal dopamine system.

The dopaminergic innervation in the mesofrontal circuit exhibits a protracted maturation from P21 to P56 (Kalsbeek, Voorn et al. 1988, Niwa, Kamiya et al. 2010, Naneix, Marchand et al. 2012, Hoops and Flores 2017). P35-42 is in the center of this period and captures the mid-adolescent stage in rodents (Spear 2000). We have previously shown that increasing dopamine neuron activity by wheel running or optogenetic stimulation during this period, but not adulthood, can induce formation of mesofrontal dopaminergic boutons and enhance mesofrontal circuit activity in wild-type mice (Mastwal, Ye et al. 2014). We therefore chose the P35-P42 adolescent window to stimulate the mesofrontal dopamine circuit and test the long-term effect of this intervention on the frontal circuit and memory-guided decision-making deficits in mutant mice. We have detailed this rationale in the revised manuscript when we first introduced this intervention.

2). Please provide a justification for choosing the optical recording M2 neuronal activity instead of the prelimbic prefrontal cortex, which has been known to show the highest levels of dopamine terminals.

While the prelimbic area has the highest level of dopamine terminals among frontal cortical regions, a robust presence of dopaminergic terminals and dopamine release in the M2 frontal cortex have been well documented (Berger, Gaspar et al. 1991, Mastwal, Ye et al. 2014, Aransay, Rodriguez-Lopez et al. 2015, Patriarchi, Cho et al. 2018). The M2 cortex plays an important role in action planning, generating the earliest neural signals among frontal cortical regions that are related to upcoming choice during spatial navigation (Sul, Kim et al. 2010, Sul, Jo et al. 2011). Our chemogenetic inactivation experiments (Supplementary Fig 1) has further confirmed the involvement of M2 in the memory-guided Y-maze navigation task used in this study. Technically, M2 has the advantage of being more amendable to optical recording of neuronal activity without the tissue damage caused by implanting a lens, which would be necessary for deeper areas such as the prelimbic cortex. We have provided this justification in the revised manuscript.

3). What was the rationale for using the 3-day chemogenetic stimulation paradigm?

Our previous work in wild-type adolescent mice showed that a single optogenetic stimulation session or a 2-hr wheel running session is sufficient to induce bouton formation in mesofrontal dopaminergic axons (Mastwal, Ye et al. 2014). In this study, we sought to rescue existing structural and functional deficits in the mesofrontal dopaminergic circuits due to genetic mutations. Because previous studies suggested that an optimal level of dopamine is important for normal cognitive function (Arnsten, Cai et al. 1994, Robbins 2000, Floresco 2013), we elected to do multiple stimulation sessions to boost the potential rescue effects. We tested both a 3-day and a 3-week stimulation paradigm, and found that the 3-day, but not the 3-week paradigm led to robust functional improvement (Fig. 5). These results indicate that moderate but not excessive stimulation of dopamine neurons can provide functional improvement of a deficient mesofrontal circuit. We have revised our text to clarify the rationale for these experiments.

4). A major maturational event occurring in the prefrontal cortex is the gain of local GABAergic transmission, which is crucial for sustaining proper levels of Y-maze tasks. I am wondering if the authors have any thoughts about what is really happening at the postsynaptic level following adolescent dopamine stimulation.

The developmental increases in dopaminergic innervation to the frontal cortex and local GABAergic transmission are likely synergistic processes, which both contribute to the maturation of high-order cognitive functions supported by the frontal cortex (Caballero and Tseng 2016, Larsen and Luna 2018). Previous electrophysiological studies have suggested that dopamine can act on five different receptors expressed in both excitatory and inhibitory postsynaptic neurons (Seamans and Yang 2004, Tseng and O'Donnell 2007, O'Donnell 2010). At the network level, dopaminergic signaling can increase the signal-to-noise ratio and temporal synchrony of neural activity during cognitive tasks (Rolls, Loh et al. 2008, Vander Weele, Siciliano et al. 2018, Lohani, Martig et al. 2019). As the frontal GABAergic inhibitory network undergoes major functional remodeling during adolescence (Caballero and Tseng 2016), adolescent stimulation of dopamine neurons may interact with this maturational process to promote a network configuration conducive for synchronous and high signal-to-noise neural computation (Porter, Rizzo et al. 1999, Murty, Calabro et al. 2016, Mukherjee, Carvalho et al. 2019). The microcircuit mechanisms underlying adolescent dopamine stimulation induced changes, particularly in the GABAergic inhibitory neurons, will be an exciting direction for future research. We have extended our discussion about these points in the revised manuscript.

5). A change in the density of dopamine boutons is unlikely to be limited to the M2 region in Arc-/- mice. The authors should provide some data illustrating that similar changes are widespread across the medial prefrontal cortex, and that the optical recording in the M2 region was preferred for technical limitations and to avoid damaging areas in the frontal cortex.

As discussed above, this study focused on the M2 region of the frontal cortex because it is functionally required for memory-guided Y-maze navigation, generates behavioral choice-related neural signals during spatial navigation, and is optically most accessible. The medial prefrontal regions (anterior cingulate, prelimbic and infralimbic) ventral to M2 also receive dense dopaminergic innervation and can act in concert with M2 in decision making (Sul, Kim et al. 2010, Sul, Jo et al. 2011, Barthas and Kwan 2017). As dopaminergic innervations to the frontal cortical regions progress in a ventral-to-dorsal direction during development (Kalsbeek, Voorn et al. 1988, Hoops and Flores 2017), how the changes induced by adolescent dopamine stimulation may proceed spatial-temporally across different frontal subregions requires more extensive investigation in the future. We have added this discussion into the revised manuscript.

Reviewer #2 (Public Review):

The manuscript by Mastwal and colleagues explores how transient adolescent stimulation of ventral midbrain neurons that project to the frontal cortex may help to improve performance on certain memory tasks. The manuscript provides an interesting set of observations that DREADD-based activation over only 3 days during adolescence provides a fast-acting and long-lasting improvement in performance on Y-maze spontaneous alternation as well as aspects of neuronal function as assessed using in vivo imaging methods. While interesting, there are several weaknesses. First and foremost, it is not clear that the effects the authors are observing are mediated by dopamine. It has been clearly documented that the DAT-Cre line provides a better representation of midbrain dopamine cells in the mouse, particularly near the midline of the ventral midbrain (Lammel et al., Neuron 2015). This is precisely where the cells that project to the frontal cortex are located. Therefore, the selection of TH-Cre is problematic. It is very likely that the authors are labeling a substantial number of non-dopaminergic cells.

We agree with Review 2 that the DAT-Cre line can provide specific labeling of midbrain dopamine neurons, particularly those projecting to the striatum, as discussed in the cited study (Lammel, Steinberg et al. 2015). DAT transports the extracellularly released dopamine back into presynaptic terminals, but it is not essential for dopamine synthesis and release (Sulzer, Cragg et al. 2016). Mesocortical dopamine neurons in the ventral tegmental area (VTA) express very little DAT (Sesack, Hawrylak et al. 1998, Lammel, Hetzel et al. 2008, Li, Qi et al. 2013), which limits the use of the DAT-Cre line to target these neurons (Lammel, Steinberg et al. 2015). Because mesocortical dopamine neurons have strong expression of TH, a key enzyme involved in dopamine synthesis, TH-Cre lines have been extensively used to study the mesocortical pathway (Lammel, Lim et al. 2012, Gunaydin, Grosenick et al. 2014, Ellwood, Patel et al. 2017, Vander Weele, Siciliano et al. 2018, Lohani, Martig et al. 2019). We provide more details below about our rationales for using TH-Cre rather than DAT-Cre mice in our study and the revisions we made in response to the reviewer’s specific recommendations.

Reviewer #2 (Recommendations For The Authors):

1). The authors should rigorously demonstrate that there is a reasonable midbrain DA projection to the coordinates that they are assessing and that their effects are due to DA release from these cells. It is not clear that there is a VTA dopaminergic projection to M2 - it does not appear for example in the Allen Mouse Brain Connectivity Atlas (https://connectivity.brainmap.org/projection/experiment/siv/160540751? imageId=160541123&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=17321&y=15284&z=3). Though there is a projection to the mPFC, at the coordinates the authors report, there does not appear to be any signal from DAT-Cre mice. However, there is much more signal when expression is not restricted to dopamine cells (https://connectivity.brain-map.org/projection/experiment/siv/165975096? imageId=165975158&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=17950&y=11504&z=3). The argument that these cells may express less TH is not relevant for this particular issue. Therefore, it is possible that the vast majority of observed effects are not in fact mediated by dopamine but another neurotransmitter such as glutamate. While the experiment using SCH23390 does suggest DA receptors may be involved, this result in isolation doesn't alleviate this caveat - there can be, for example, DA release from NE cells (e.g., Takeuchi et al., Nature 2016). While this does not entirely invalidate the authors' results, as their effects of stimulation of ventral midbrain cells to the forebrain don't necessarily have to occur via dopamine - the mechanism by how this is occurring needs to be clear.

While the prelimbic area has the highest level of dopaminergic terminals among frontal cortical regions, a robust presence of midbrain dopaminergic projections and dopamine release in the M2 frontal cortex have been well established by immunostaining, viral labeling, single-cell axon-tracing, and in vivo imaging of recently developed dopamine biosensors (Berger, Gaspar et al. 1991, Mastwal, Ye et al. 2014, Aransay, Rodriguez-Lopez et al. 2015, Ye, Mastwal et al. 2017, Patriarchi, Cho et al. 2018). It has also been reported repeatedly that mesocortical dopamine neurons in the VTA express very little DAT, which is different from mesostriatal dopamine neurons (Sesack, Hawrylak et al. 1998, Lammel, Hetzel et al. 2008, Li, Qi et al. 2013). This limitation in the use of the DAT-Cre line to target mesocortical dopamine neurons has been acknowledged in previous studies (Lammel, Steinberg et al. 2015) and is consistent with the reviewer’s observation of DAT-Cre labeling in the Allen Brain Mouse Connectivity atlas. Additionally, and interestingly, recent extensive evaluation of the DAT-Cre line reported ectopic labeling of multiple non-dopaminergic neuronal populations (Soden, Miller et al. 2016, Stagkourakis, Spigolon et al. 2018, Papathanou, Dumas et al. 2019). Our own evaluation of the DAT-Cre line’s utility for cortical imaging also revealed sparse axonal labeling and sporadic ectopic labeling of cortical cell somas. We have included representative DAT-Cre images in Author response image 1 to highlight the limitations of this line in the study of the dopaminergic mesocortical circuit.

Author response image 1.

Example images from DAT-Cre/Ai14 mice. Left most panel shows little axonal labeling in Layer 5/6 of M2. The center panel shows sparse axonal label in Layer 1/2 of M2, but also ectopic labeling of cell soma. The right panel shows a lack of labeling in L1/2 of prelimbic cortex as well. Scale bars 50um.

We as well as others have confirmed that TH immunoreactivity in the frontal cortex can label dopaminergic axons originated from the VTA, and ablation of VTA dopaminergic neurons removes this labeling (Niwa, Jaaro-Peled et al. 2013, Ye, Mastwal et al. 2017). Because mesocortical dopamine neurons have much stronger TH expression than DAT expression (Sesack, Hawrylak et al. 1998, Lammel, Hetzel et al. 2008, Li, Qi et al. 2013, Lammel, Steinberg et al. 2015), TH-Cre lines have been frequently used to label these neurons and study the mesocortical pathway (Lammel, Lim et al. 2012, Gunaydin, Grosenick et al. 2014, Ellwood, Patel et al. 2017, Vander Weele, Siciliano et al. 2018, Lohani, Martig et al. 2019). While TH-Cre expression itself is not restricted to dopaminergic neurons, we targeted our viral injections to the VTA and optogenetic stimulation to the cortical dopaminergic projection target area in M2 (Patriarchi, Cho et al. 2018) to specifically modulate mesofrontal dopaminergic axons. In addition, we tested D1 antagonist’s effects in our manipulations. Although we targeted dopamine neurons in our adolescent stimulation, the final behavioral outcome likely includes contributions from co-released neurotransmitters such as glutamate and non-dopaminergic neurons via network effects (Morales and Margolis 2017, Lohani, Martig et al. 2019), which will be interesting directions for future research. We have revised our results and discussion sections to highlight our rationales for using the TH-Cre line and the open mechanistic questions for future studies.

2) SSFOs don't increase excitability like DREADDs, but rather, cause long-lasting hyperactivity through continuous passage of cations. What the actual firing properties are of these cells over a long period of time is not clear.

We did not measure the precise firing patterns of the dopaminergic neurons targeted by SSFOs but evaluated the effects of SSFO activation on the frontal cortex. Similar to our DREADD-Gq mediated activity changes in the mesofrontal circuit, we found increased frontal cortical activity post-light stimulation of frontal dopamine axons in our SSFO treated animals (Fig 6a-c, S6e). While quantitatively the firing patterns of DREADD-Gq and SSFO activated dopaminergic neurons likely differ, qualitatively both of these manipulations lead to increased mesofrontal circuit activity and improvements in cognitive behaviors. In our previous work with wild-type adolescent mice, both wheel running and a single 10-min session of phasic optogenetic stimulation of the VTA resulted in dopaminergic bouton outgrowth in the frontal cortex (Mastwal, Ye et al. 2014). Taken together, these results suggest that adolescent dopaminergic mesofrontal projections are highly responsive to neural activity changes and a variety of adolescent stimulation paradigms are sufficient to elicit lasting changes in this circuit. We have added this discussion of the limitations and implications of our study into the revised manuscript.

3) It is not clear what the increase in boutons means, given that DA release is thought to largely occur via non-synaptic release.

Although many of dopamine boutons are not associated with defined postsynaptic structures, these axonal boutons and the active zones they contain are the major release sites for dopamine (Goldman-Rakic, Leranth et al. 1989, Arbuthnott and Wickens 2007, Sulzer, Cragg et al. 2016, Liu, Goel et al. 2021). Past studies have established a consistent association between increased dopaminergic innervation in the frontal cortex and an increase in dopamine levels (Niwa, Kamiya et al. 2010, Naneix, Marchand et al. 2012). Our previous work also found that increasing dopaminergic boutons through adolescent VTA stimulation led to prolonged frontal local field potential responses with high-frequency oscillations (Mastwal, Ye et al. 2014), which is characteristic of increased dopaminergic signaling (Lewis and O'Donnell 2000, Gireesh and Plenz 2008, Wood, Kim et al. 2012, Lohani, Martig et al. 2019). Importantly, in our quantification of the structural changes in this study, we evaluated boutons which were labeled with synaptophysin, a molecular marker indicating the presence of synaptic vesicle release machinery (Li, Tasic et al. 2010, Oh, Harris et al. 2014). Thus, our study, taken in the context of the previous work, suggests the increased number of boutons signifying an increase in dopaminergic signaling within the mesofrontal circuit. We have added this discussion into the revised manuscript.

4) The use of Arc and DISC mutants as models of schizophrenia is perhaps a bit overstated - while deficits in prefrontal innervation certainly occur, there are many differences between these models and the human disease states. Language should be toned down accordingly, particularly in the introduction.

We strived to avoid overstating the extent to which the mouse lines are models for specific diseases, but we can appreciate that this may not have been clear in our original writing. We have adjusted our language to better distinguish between the utility of the animal models for the purposes of our study and their relationship to specific human disease states. Particularly in the introduction, we stated that: “Genetic disruptions of several genes involved in synaptic functions related to psychiatric disorders, such as Arc and DISC1, lead to hypoactive mesofrontal dopaminergic input in mice (Niwa, Kamiya et al. 2010, Niwa, Jaaro-Peled et al. 2013, Fromer, Pocklington et al. 2014, Purcell, Moran et al. 2014, Wen, Nguyen et al. 2014, Manago, Mereu et al. 2016). Although there are many differences between these mouse lines and specific human disease states, these mice offer opportunities to test whether genetic deficits in frontal cortex function can be reversed through circuit interventions.”

5) Some experiments are missing proper controls, e.g., Figure 3g-I where a WT mouse should be used as a positive control.

The goal of this experimental design (Fig 3g-i) was to evaluate the potential effects of chemogenetic VTA stimulation in the Arc-/- mice. We used Arc-/- mice with mCherry injections to control for the potential effects of CNO administration. While WT mice could be used to determine if adolescent VTA stimulation would lead to long-lasting enhancement of VTA-to-Cortical transmission, this wouldn’t necessarily be a positive control for our experiments, but rather a separate line of inquiry. As dopamine’s effects often display an inverted-U dose-response curve (Vijayraghavan, Wang et al. 2007, Floresco 2013), evaluating the effects adolescent VTA stimulation in the absence of underlying dopamine deficiency could be an interesting future research direction. We have added this discussion into the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

1) Did the SSFO stimulation of the TH+ axons in PFC during adolescence lead to the same long-term change in DA bouton number the authors saw with DREADDs?

We did not examine the degree of bouton growth in the SSFO cohort, which is a limitation of this study. Accurate quantification of dopamine boutons requires the co-injection of another AAV vector encoding Synaptophysin-GFP to label the boutons. Because we used light to directly stimulate SSFO-labeled dopaminergic axons in the frontal cortex, we were concerned that co-injecting another AAV vector may dilute SSFO-labeling of axons and reduce the efficacy of optogenetic stimulation. Given the behavioral benefits we observed, we would expect an increase in bouton density after optogenetic stimulation. A systematic optimization of viral co-labeling and optogenetic stimulation protocols will facilitate examination of the impact of SSFO stimulation at the structural level in future studies. We have added a discussion of the limitation of this study in the revised manuscript.

2) The DISC1 section is far less detailed than the Arc section, and it was not completely clear to me that the mechanisms of dysfunction and rescue were the same in these mice compared with the Arc mice. For example, there was no mention of DA bouton density or the patterned firing of the PFC neurons at the time of decision making.

The initial motivation of this study was to test if adolescent dopamine stimulation can rescue the deficits in the mesofrontal dopaminergic circuit and cognitive function of Arc-/- mice, which were identified in our previous studies (Manago, Mereu et al. 2016). We first conducted multiple levels of analyses including viral tracing, in vivo calcium imaging, and behavioral tests to establish the coherent impacts of adolescent dopamine neuron stimulation on circuits and behaviors. We then examined a range of stimulation protocols to assess the efficacy requirements for cognitive improvement, which is our primary goal. Finally, we included DISC1 mice in our study to test if adolescent dopamine stimulation can also reverse the cognitive deficit in another genetic model for mesofrontal dopamine deficiency. By demonstrating a similar cognitive recuse effect of adolescent VTA stimulation in an independent mouse model, this study provides a foundation for future research to compare the detailed cellular mechanisms that underlie the functional rescue in different genetic models. We have added the discussion of the scope and limitation of this study to the revised manuscript.

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Author Response

We thank the editors for their care in handling our manuscript. We also thank the reviewers, especially reviewer 2, for their thorough comments. We will work to address their concerns in a revised version and provide some initial comments below.

A major concern of two reviewers was that odour profiles were not quantified rigorously. We acknowledge that our study does not achieve the level of quantitative rigour standard in most chemical ecology work. We plan to conduct a few additional analyses to help address this shortcoming. We will also adjust the text to clarify the semi-quantitative nature of the data.

Reviewers also suggested using several different analytical approaches (e.g., different column, different sorbent) to broaden the type and number of detectable compounds. The reviewers rightly point out that such choices strongly affect which compounds we are likely to sample. No single approach is comprehensive, and ours is no exception. We will work to ensure that the appropriate caveats are included prominently in the text.

However, we believe this concern in fact underscores a special strength of our study: analysing the odour of a large number of species in a single study using the same analytical approach, so that the inherent biases of different approaches do not complicate cross-species comparisons. We are aware of very few such large-scale studies in any system and welcome suggestions from reviewers or readers of any we might have overlooked.

In general, we believe many of the reviewers’ methodological concerns reflect standards in the field of chemical ecology established for studies that aim to describe the odour of one or a few species as comprehensively as possible with a high level of quantitative rigour. This was not our goal, and we will temper our language in the revised paper to make that clear. Instead, we aimed to sample as broadly as possible across species to gain insight into the general statistics of a large 'odour landscape' or 'odour space' — an endeavour that, to our knowledge, is less common in the chemical ecology literature. In doing so, we prioritized breadth over depth. We believe the resulting dataset provides solid evidence for our major conclusions, though we will revisit our analyses and conduct a small number of additional experiments to further substantiate our claims.

Author Response:

We thank the reviewers and editors for their constructive and encouraging feedback on our manuscript. We have carefully studied the reviewer comments and found that we agree with almost all of them; we will implement these suggestions and prepare a revised submission. In particular, we will aim to address the reviewers’ valid concerns regarding metagenomic detection limits via a high-sensitivity re-analysis of the data based on metagenomic read mapping, orthogonal to our current analyses based on read mapping to mOTU single copy marker genes. Moreover, we will revise the manuscript text for clarity and streamline the phrasing on some observations and claims. We are confident that our work will improve as a result and look forward to future feedback and interactions.

Sincerely, for the authors,

Sebastian Schmidt & Peer Bork

Author Response

Joint Public review

The manuscript by Mitra and coworkers analyses the functional role of Orai in the excitability of central dopaminergic neurons in Drosophila. The authors show that a dominant-negative mutant of Orai (OraiE180A) significantly alters the gene expression profile of flight-promoting dopaminergic neurons (fpDANs). Among them, OraiE180A attenuates the expression of Set2 and enhances that of E(z) shifting the level of epigenetic signatures that modulate gene expression. The present results also demonstrate that Set2 expression via Orai involves the transcription factor Trl. The Orai-Trl-Set1 pathway modulates the expression of VGCC, which, in turn, are involved in dopamine release. The topic investigated is interesting and timely and the study is carefully performed and technically sound; however, there are several major concerns that need to be addressed:

1) In Figure S2E, STIM is overexpressed in the absence of Set2 and this leads to rescue. It is presumed that STIM overexpression causes excess SOCE, yet this is rarely the case. Perhaps the bigger concern, however, is how excess SOCE might overcome the loss of SET2 if SET2 mediates SOCE-induced development of flight. These data are more consistent with something other than SET2 mediating this function.

Our statement that STIM overexpression overcomes deficits in SOCE is based on the following published work:

1. Studies of SOCE in wildtype cultured larval Drosophila neurons demonstrated that overexpression of STIM raised SOCE to the same extent as co-expression of STIM and Orai in the WT background (Chakraborty et al, 2016; Figure 1D).

2. Both Carbachol-induced IP3-mediated Ca2+ release and SOCE (measured by Ca2+ add back after Thapsigargin-induced store depletion) were rescued in primary cultures of IP3R hypomorphic mutant (itprku) Drosophila neurons by overexpression of STIM (Agrawal et al., 2010; Figure 8A-G).

3. Deb et al., 2016 (Supplementary Figure 2h,i) reaffirmed that overexpression of STIM significantly improves SOCE after Thapsigargin-induced passive store-depletion in Drosophila neurons expressing IP3RRNAi.

4. Consistent with the cellular rescue of SOCE, defects in flight initiation and physiology observed in the heteroallelic IP3R hypomorphic background (itprku) could be rescued by overexpression of STIM (Agrawal et al., 2010; Figure 3A-E) as well as Orai (Venkiteswaran and Hasan, 2009; Figure 3).

5. In Figure S2E, we show that flight deficits arising from THD’> Set2RNAi are rescued upon overexpression of STIM (i.e. THD’>Set2RNAi; STIMOE). Here and in another recent publication (Mitra et al., 2021) we show that neurons expressing Set2RNAi exhibit reduced expression of the IP3R and reduced ER-Ca2+ release presumably leading to reduced SOCE. As mentioned above we have consistently found that STIM overexpression raises both IP3-mediated Ca2+ release and SOCE in Drosophila neurons.

In this study, we propose that Ca2+ release through the IP3R followed by SOCE are part of a positive feedback loop driving expression of Set2 which in turn upregulates expression of mAChR and IP3R (Figure 3F) to regulate dopaminergic neuron function. Our observation that loss of Set2 (THD’>Set2RNAi) can be rescued by STIM overexpression is consistent with this model because:

1. Loss of Set2 (THD’>Set2RNAi) results in downregulation of several genes including mAChR and IP3R leading to decreased SOCE.

2. As evident from our previous studies increased STIM expression in the Set2RNAi background (THD’>Set2RNAi; STIMOE) is expected to enhance SOCE which we predict would rescue Set2 expression leading to rescue of other Set2 dependent downstream functions like flight (Figure 2D).

2) In Figure 3, data is provided linking SET2 expression and Cch-induced Ca2+ responses. The presentation of these data is confusing. In addition, the results may be a simple side effect of SET2-dependent expression of IP3R. Given that this article is about SOCE, why isn't SOCE shown here? More generally, there are no measurements of SOCE in this entire article. Measuring SOCE (not what is measured in response to Cch) could help eliminate some of this confusion.

We will re-write this section in the revised version for better clarity and explain how Set2-dependent IP3R expression is an important component of Orai-mediated Ca2+ entry in fpDANs. Here, we propose that IP3-mediated Ca2+ release and SOCE, through Orai, are together part of a positive feedback loop driving transcription of Set2 which in turn upregulates mAChR and IP3R expression (Figure 3F). We hypothesized that the observed loss of CCh-induced Ca2+ response in the Set2RNAi background (Figure 3B-D; THD’>Set2RNAi) results from decreased itpr and mAChR expression and verified this in Figure 3E. This is further validated by the rescue of CCh-induced Ca2+ response and itpr/mAChR expression in the OraiE180A background upon Set2 overexpression (Figure 3B-E; THD’>OraiE180A; Set2OE). We were constrained to measure CCh-induced Ca2+ responses in OraiE180A expressing neurons for the following reasons:

1. SOCE measurements through Tg mediated store Ca2+ release followed by Ca2+ add back require a 0 Ca2+ environment that can only be achieved in culture. The Drosophila brain is bathed in hemolymph which contains Ca2+ and there do not exist any methods to readily deplete Ca2+ from the tissue to create a 0 Ca2+ environment without also effecting the health of the neurons.

2. Cultures of the subset of dopaminergic neurons (THD’) we have focused on in this study were not feasible due to the small number of neurons being studied from the total number of dopaminergic neurons in the brain (~35/400). In previous studies we have shown that SOCE post-Tg induced store depletion is abrogated in cultured dopaminergic neurons from Drosophila upon expression of OraiE180A (Pathak et al., 2015).

Furthermore, Carbachol-induced IP3-mediated Ca2+ release is tightly coupled to SOCE in Drosophila neurons (Venkiteswaran and Hasan, 2009) and Ca2+ release from the IP3R is physiologically relevant for flight behavior in THD’ neurons (Sharma and Hasan, 2020).

3) A significant gap in the study relates to the conclusion that trl is a SOCE-regulated transcription factor. This conclusion is entirely based on genetic analysis of STIMKO heterozygous flies in which a copy of the trl13C hypomorph allele is introduced. While these results suggest a genetic interaction between the expression of the two genes, the evidence that expression translates into a functional interaction that places trl immediately downstream of SOCE is not rigorous or convincing. All that can be said is that the double mutant shows a defect in flight which could arise from an interruption of the circuit. Further, it is not clear whether the trl13C hypomorph is only introduced during the critical 72-96 hour time window when the Orai1E180E phenotype shows up. The same applies to the over-expression of Set2 and the other genes. If the expression is not temporally controlled, then the phenotype could be due to the blockade of an entirely different aspect of flight neuron function.

The idea that Trl functions downstream of Orai-mediated Ca2+ entry in THD’ neurons is based on the following genetic evidence:

1. In Figure 4D, we show evidence of genetic interaction between trl-STIM and trl-Set2. The rescue of trl13c/STIMKO with STIM overexpression in THD’ neurons indicates that excess SOCE (driven by STIMOE) may activate the residual Trl (there exists a WT Trl copy in this genetic background) to rescue THD’ flight function. This is further supported by the rescue of trl/STIMKO with Set2 overexpression in THD’ neurons, which is consistent with the feedback loop model proposed in Figure 5C - where we propose that reduced SOCE leads to reduced ‘activated’ Trl and thus reduced Set2 expression, and the latter is rescued by SET2OEThe manner in which SOCE ‘activates’ Trl is the subject of ongoing investigations.

2. The trl hypomorphic alleles (including trl13C) exist as genetic mutants and they affect Trl function in all tissues throughout development. While we concede that these mutant alleles would affect multiple functions at other stages of development, which may impinge on the phenotypes noted in Figure S4B, we have used a targeted RNAi approach to validate Trl function specifically in the THD’ neurons (Figure 4C).

3. Overexpression mediated rescues (including Set2) were not induced only during the critical 72-96 hrs APF developmental window. Having established that Orai function drives critical gene expression during this window (Figure 1), it is reasonable to assume that Set2 rescue of loss of flight in OraiE180A occurs in the same time window where flight is disrupted.

4- In Figure 4, data is shown that SOCE compensates for the loss of Trl, the presumed mediator of SOCE-dependent flight. The fact that flight deficits are rescued by raising SOCE in the absence of Trl is very inconsistent with this conclusion.

We apologise for this confusion and will clarify in the revision. trl13c is a recessive allele of Trl and should be written as such throughout the text and in the figures (i.e trl13c and NOT Trl13c). In all cases of Trl mutant rescue by STIMOE and Set2OE there exists residual Trl that can be activated by excess SOCE thus leading to the rescue. This is true for trl13C/ STIMKO where each mutant is present as a heterozygote (the complete genotype of this strain is STIMKO/+; trl13c/+; this will be corrected in the revision). Similarly, for TrlRNAi we expect reduced levels (but not complete loss) of Trl. Thus the SOCE rescue of loss of Trl occurs in conditions where Trl levels are reduced but NOT absent. Homozygous trl null mutants are lethal.

5- In Figure 5 (A-C), data is provided that Trl transcripts are unaffected by loss of SOCE and that overexpression cannot rescue flightlessness. From this, the authors conclude that this gene "must" be calcium responsive. While that is one possibility, it is also possible that these genes are not functionally linked.

The idea that Trl is functionally linked to SOCE is based on the following evidence:

1. In Figure 4C we show that flight defects caused by partial loss of Trl (THD’>TrlRNAi) were rescued by STIM overexpression (THD’>TrlRNAi; STIMOE). As mentioned above we have found that STIM overexpression raises SOCE.

2. Heteroalleles of the trl13C hypomorph exhibit a strong genetic interaction with a single copy of the null allele of STIMKO as shown by the flight deficit of trl13c/+; STIMKO/+ (trl13C/STIMKO ) flies (Figure 4D). The genotypes will be corrected in the revision.

3. Flight defects in trl13C/STIMKO flies could be rescued by STIM overexpression in the THD’ neurons (trl13C/STIMKO; THD’>STIMOE)

4. In Figure 4E, we show that partial loss of Trl in THD’ neurons (THD’>TrlRNAi) leads to decreased expression of the Ca2+ responsive genes mAChR, itpr, and Set2 genes indicating that Trl is a constituent of the SOCE-driven transcriptional feedback loop (Figure 5C).

Since we could not detect a well-defined Ca2+ binding domain in Trl, we hypothesize that it could be activated by a Ca2+ dependent post-translational modification. Phosphoproteome analysis of Trl demonstrated that it does indeed undergo phosphorylation at a Threonine residue (T237; Zhai et al., 2008), which lies within a potential site for CaMKII. Independently, CaMKII has been identified as a binding partner of Trl from a Trl interactome study (Lomaev et al., 2018). Past work from our group (Ravi et al., 2018) identified a role for CaMKII in THD’ neurons in the context of flight. We are currently testing if CaMKII functions downstream of SOCE in THD’ neurons to mediate flight and will update this information in the next version of the manuscript.

6) There is no characterization of SOCE in fpDANs from flies expressing native Orai or the dominant negative OraiE180A mutant. While the authors refer to previous studies, as the manuscript is essentially based on Orai function thapsigargin-induced SOCE should be tested using the Ca2+ add-back protocol in order to assess the release of Ca2+ from the ER in response to thapsigargin as well as the subsequent SOCE.

The fpDANs consist of 16-19 neurons in each hemisphere (PPL1 are 10-12 and PPM3 are 6-7 cells; Pathak et al., 2015). Measuring SOCE from these neurons in vivo is not possible due to the presence of abundant extracellular Ca2+ in the brain. Given their sparse number, it proved technically challenging to isolate the fpDANs in culture to perform SOCE measurements using the Ca2+ add back protocol. Due to these reasons, we have relied upon using Carbachol to elicit IP3-mediated Ca2+ release and SOCE as a proxy for in vivo SOCE. In previous studies we have shown that Carbachol treatment of cultured Drosophila neurons elicits IP3-mediated Ca2+ release and SOCE (Agrawal et al., 2010; Figure 8). Moreover, expression of OraiE180A completely blocks SOCE as measured in primary cultures of dopaminergic neurons (Pathak et al., 2015; Figure 1E). Hence we have not repeated SOCE measurements from all dopaminergic neurons in this work. In the revised version we will explicitly state this weakness of our study and the reasons for it.

7) In the experiments performed to rescue flight duration in Set2RNAi individuals the authors overexpress STIM and attribute the effect to "Excess STIM presumably drives higher SOCE sufficient to rescue flight bout durations caused by deficient Set2 levels.". This should be experimentally tested as the STIM:Orai stoichiometry has been demonstrated as essential for SOCE.

The assumption that STIM overexpression drives higher SOCE is based upon previously published work from Drosophila neurons (Agrawal et al., 2010; Chakraborty et al, 2016; Deb et al., 2016) which demonstrates that excess WT STIM overcomes IP3R deficiencies (RNAi or hypomorphic mutants) to rescue SOCE. We agree that STIM-Orai stoichiometry is essential for SOCE, and propose that the rescue backgrounds possess sufficient WT Orai, which is recruited by the excess STIM to mediate the rescue. We will reference the earlier work to validate our use of STIMOE for rescue of SOCE.

Here, we propose that Set2 is part of a positive feedback loop driving transcription of mAChR and IP3R (Figure 3F). In keeping with this hypothesis, we posit that the phenotypes observed in the Set2RNAi background (Figure 2D) result from decreased itpr and mAChR expression (validated in Figure 3E). This is further validated by the Set2 overexpression mediated rescue of OraiE180A (Figure 2D) and rescue of itpr/mAChR expression in the OraiE180A background (Figure 3B-E; THD’>OraiE180A; Set2OE).

8) The authors show that overexpression of OraiE108A results in Stim downregulation at a mRNA level. What about the protein level? And more important, how does OraiE108A downregulate Stim expression? Does it promote Stim degradation? Does it inhibit Stim expression?

We hypothesize that changes in STIM mRNA observed in the THD’ > OraiE180A neurons stems from an overall reduction in IP3-mediated Ca2+ release and SOCE due to loss of Trl-Set2 driven gene expression detailed in our transcriptional feedback loop model (Figure 5C). We will attempt to explain this aspect more clearly in the next version of the manuscript. While we agree that measuring levels of STIM protein would be helpful, estimation of protein levels from a limited number of neurons (~35 cells per brain) is technically challenging. The STIM antibody does not work well in immunohistochemistry. In the absence of any experimental evidence we cannot comment on how expression of OraiE180A might affect STIM protein turnover.

9) Lines 271-273, the authors state "whereas overexpression of a transgene encoding Set2 in THD' neurons either with loss of SOCE (OraiE180A) or with knockdown of the IP3R (itprRNAi), lead to significant rescue of the Ca2+ response". This is attributed to a positive effect of Set2 expression on IP3R expression and the authors show a positive correlation between these two parameters; however, there is no demonstration that Set2 expression can rescue IP3R expression in cells where the IP3R is knocked down (itprRNAi). This should be further demonstrated.

The rescue of IP3R expression by Set2 overexpression in itprRNAi was demonstrated in a different set of Drosophila neurons in an earlier study (Mitra et al., 2021) and has not been repeated specifically in THD’ neurons. Similar to the previous study, here we tested CCh stimulated Ca2+ responses of THD’ neurons with itprRNAi and itprRNAi; SetOE (Fig S3), which are indeed rescued by SET2OE.

10) The data presented in Figure 3E should be functionally demonstrated by analyzing the ability of CCh to release Ca2+ from the intracellular stores in the absence of extracellular Ca2+.

CCh-mediated Ca2+ release from the intracellular stores in the absence of extracellular Ca2+ has been described in primary cultures of Drosophila neurons in previously published work (Venkiteswaran and Hasan, 2009; Agrawal et al., 2010) This work focuses on a set of 16-19 dopaminergic neurons in a hemisphere of the Drosophila central brain. It is technically challenging to generate a 0 Ca2+ environment in vivo, which is essential for measuring store Ca2+ release. Given their meagre numbers, primary cultures of these neurons is not readily feasible.

11) The conclusion that SOCE regulates the neuronal excitability threshold is based entirely on either partial behavioral rescue of flight, or measurements of KCl-induced Ca2+ rises monitored by GCaMP6m in DAN neurons. The threshold for neuronal excitability is a precise parameter based on rheobase measurements of action potentials in current-clamp. Measurements of slow calcium signals using a slow dye such as GCaMp6m should not be equated with neuronal excitability. What is measured is a loss of the calcium response in high K depolarization experiments, which occurs due to the loss of expression of Cav channels. Hence, the use of this term is not accurate and will confuse readers. The use of terms referring to neuronal excitability needs to be changed throughout the manuscript. As such, the conclusions regarding neuronal excitability should be strongly tempered and the data reinterpreted as there are no true measurements of neuronal excitability in the manuscript. All that can be said is that expression of certain ion channel genes is suppressed. Since both Na+ channels and K+ channel expression is down-regulated, it is hard to say precisely how membrane excitability is altered without action potential analysis.

The claim that SOCE influences neuronal excitability is based on the following observations:

1. Interruption of the transcriptional feedback loop involving SOCE, Trl, and Set2 through loss of any of its constituents, results in the downregulation of VGCCs (Figure 5G, 6H), which are essential components of action potentials.

2. OraiE180A mediated loss of SOCE in THD’ neurons abrogates the KCl-evoked depolarization response (Figure 6B, C) measured using GCaMP6m. We verified that this response requires VGCC function using pharmacological inhibition of L-type VGCCs (Figure 6E, F).

3. SOCE deficient THD’ neurons, which were presumably compromised in their ability to evoke action potentials could be rescued to undergo KCl-evoked depolarisation by expression of NachBac, which lowers the depolarization threshold (Figure 7C, D) or through optogenetic stimulation using CsChrimson (Figure 7F).

We agree that ‘neuronal excitability threshold’ is a precise electrophysiological parameter that has not been directly investigated here by measurement of action potentials. Therefore, references to neuronal excitability will be tempered throughout the revised manuscript and be replaced with a more generic reference to ‘neuronal activity’. In this context we propose to include further evidence supporting reduced excitability of THD’ neurons upon loss of SOCE in the revision.

Since one of the key functional outcomes of activity during critical developmental periods such as the 72-96 hrs APF developmental window identified in this study, is remodelling of neuronal morphology, we decided to investigate the same in our context. Neuronal activity can drive changes in neurite complexity and axonal arborization (Depetris-Chauvin et al., 2011) especially during critical developmental periods (Sachse et al., 2007). To understand if Orai mediated Ca2+ entry and downstream gene expression through Set2 affects this activity-driven parameter, we investigated the morphology of fpDANs, and specifically measured the complexity of presynaptic terminals within the 2’1 lobe MB using super-resolution microscopy. We found striking changes in the neurite volume upon expression of OraiE180A which could be rescued by restoring either Set2 (OraiE180A; Set2OE) or by inducing hyperactivity through NachBac expression (OraiE180A ; NachBacOE). These data will be included in the revised manuscript.

12) Related, since trl does not contain any molecular domains that could be regulated by Ca2+ signaling, it is unclear whether trl is directly regulated by SOCE or the regulation is highly indirect. Reporter assays evaluating trl activation upon Ca2+ rises would provide much stronger and more direct evidence for the conclusion that trl is a SOCE-regulated TF. As such the evidence is entirely based on RNAi downregulation of trl which indicates that trl is essential but has no bearing on exactly what point of the signaling cascade it is involved.

We agree that luciferase Trl reporters would provide a direct method to test SOCE-mediated activation. Future investigations will be targeted in this direction. Regarding possible mechanisms of Trl activation - since we could not detect a well-defined Ca2+ binding domain in Trl, we hypothesize that it may be phosphorylation by a Ca2+ sensitive kinase. Phosphoproteome analysis of Trl indicates that it does indeed undergo phosphorylation at a Threonine reside (T237; Zhai et al., 2008), which may be mediated by the Ca2+ sensitive kinase-CaMKII based on binding partners identified in the Trl interactome (Lomaev et al., 2018). Past work (Ravi et al., 2018) has indeed demonstrated a requirement for CaMKII in THD’ neurons for flight. We are currently testing whether CaMKII functions downstream of SOCE in these neurons to mediate flight, and will be updating this information in the next version of the manuscript.

13) Are NFAT levels altered in the Orai1 loss of function mutant? If not, this should be explicitly stated. It would seem based on previous literature that some gene regulation may be related to the downregulation of this established Ca2+-dependent transcription factor. Same for NFkb.

As mentioned in the text in lines (307-309), Drosophila NFAT lacks a calcineurin binding site and is therefore not sensitive to Ca2+ (Keyser et al., 2007). In the past we tested if knockdown of NF-kB in dopaminergic neurons gave a flight phenotype and did not observe any measurable deficit. From the RNAseq data we find a slight downregulation of NFAT (0.49 fold, p value=0.048) and NF-kb (0.26 fold, p value =0.258) the significance of which is unclear at this point. We did not find any consensus binding sites for these two factors in the regulatory regions of downregulated genes from THD’ neurons.

14) Does over-expression of Set2 restore ion channel expression especially those of the VGCCs? This would provide rigorous, direct evidence that SOCE-mediated regulation of VGCCs through Set2 controls voltage-gated calcium channel signaling.

Set2 overexpression in the OraiE180A background indeed restores the expression of VGCC genes (Figure 6H).

15) All 6 representative panels from Figure 3B are duplicated in Figure 4G. Likewise, 2 representative panels from Figure 5H are duplicated in Figure 6D. Although these panels all represent the results from control experiments, the relevant experiments were likely not conducted at the same time and under the same conditions. Thus, control images from other experiments should not be used simply because they correspond to controls. This situation should be clarified.

We regret the confusion caused by the same representative images for the control experiments. These will be replaced by new representative images for Figure 5H in the next updated version of the manuscript.

16) The figures are unusually busy and difficult to follow. In part this is because they usually have many panels (Fig. 1: A-I; Fig. 2, A-J, etc) but also because the arrangement of the panels is not consistent: sometimes the following panel is found to the right, other times it is below. It would help the reader to make the order of the panels consistent, and, if possible, reduce the number of panels and/or move some of the panels to new figures (eLife does not limit the number of display items).

The image panels will be rearranged for ease of reading in the next updated version of the manuscript.

17) As a final recommendation, the reviewers suggest that the authors a- Reword the text that refers to membrane excitability since membrane excitability was not directly measured here. b-Explain why STIM1 rescues the partial loss of flight in Set2 RNAi flies (Fig. S2E); and c- Explain how/why trl is calcium regulated and test using luciferase (or other) reporter assays whether Orai activation leads to trl activation.

a. Textual references to membrane excitability will be appropriately modified.

b. We have provided a detailed explanation for how STIM overexpression might rescue the phenotypes caused by Set2RNAi in Point 1. In short, these phenotypes depend upon IP3R mediated Ca2+ entry driving a transcriptional feedback loop. We relied upon past reports that STIM overexpression upregulates IP3R-mediated Ca2+ release and SOCE in Drosophila itpr mutant neurons (Agrawal et al., 2010; Chakraborty et al, 2016; Deb et al, 2016). We therefore propose that STIM overexpression in the Set2RNAi background rescues IP3R mediated Ca2+ release followed by SOCE, which drives enhanced Set2 transcription, counteracting the effects of the RNAi. We will explain this more clearly with past references in the next revision.

c. We have provided a detailed response to this comment in Point 12. Briefly, we agree that building luciferase reporters for Trl could be an ideal strategy to test for its responsiveness to SOCE and needs to be done in future. As an alternate strategy, we have looked at data from existing studies of interacting partners of Trl (Lomaev et al., 2017) and identified CamKII, which is both Ca2+ responsive (Braun and Schulman, 1995; Yasuda et al., 2022), and thus might activate Trl through a phosphorylation-switch like mechanism. Moreover, a previous publication identified a requirement for CamKII in THD’ neurons for Drosophila flight (Ravi et al., 2018). We are testing the ability of a dominant active version of CamKII to rescue THD’>E180A flight deficits and will include this information in the next version of the manuscript.

References

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2. Braun AP, Schulman H. A non-selective cation current activated via the multifunctional Ca(2+)-calmodulin-dependent protein kinase in human epithelial cells. J Physiol. 1995. 488:37-55. doi:10.1113/jphysiol.1995.sp020944
3. Chakraborty S, Deb BK, Chorna T, Konieczny V, Taylor CW, Hasan G. Mutant IP3 receptors attenuate store-operated Ca2+ entry by destabilizing STIM-Orai interactions in Drosophila neurons. J Cell Sci. 2016. 129:3903-3910. doi:10.1242/jcs.191585
4. Deb BK, Pathak T, Hasan G. Store-independent modulation of Ca2+ entry through Orai by Septin 7. Nat Commun. 2016. 7:11751. doi:10.1038/ncomms11751
5. Depetris-Chauvin A, Berni J, Aranovich EJ, Muraro NI, Beckwith EJ, Ceriani MF. Adult-specific electrical silencing of pacemaker neurons uncouples molecular clock from circadian outputs. Curr Biol. 2011. 21:1783-1793. doi: 10.1016/j.cub.2011.09.027.
6. Keyser P, Borge-Renberg K, Hultmark D. The Drosophila NFAT homolog is involved in salt stress tolerance. Insect Biochem Mol Biol. 2007. 37:356-362. doi:10.1016/j.ibmb.2006.12.009
7. Kilo L, Stürner T, Tavosanis G, Ziegler AB. Drosophila Dendritic Arborisation Neurons: Fantastic Actin Dynamics and Where to Find Them. Cells. 2021. 10:2777. doi:10.3390/cells10102777
8. Lomaev D, Mikhailova A, Erokhin M, et al. The GAGA factor regulatory network: Identification of GAGA factor associated proteins. PLoS One. 2017. 12:e0173602. doi:10.1371/journal.pone.0173602
9. Mitra R, Richhariya S, Jayakumar S, Notani D, Hasan G. IP3/Ca2+ signals regulate larval to pupal transition under nutrient stress through the H3K36 methyltransferase dSET2. Development. 2021. 148:dev199018. doi:10.1101/2020.11.25.399329
10. Pathak T, Agrawal T, Richhariya S, Sadaf S, Hasan G. Store-Operated Calcium Entry through Orai Is Required for Transcriptional Maturation of the Flight Circuit in Drosophila. J Neurosci. 2015. 35:13784-13799. doi:10.1523/jneurosci.1680-15.2015
11. Ravi P, Trivedi D, Hasan G. FMRFa receptor stimulated Ca2+ signals alter the activity of flight modulating central dopaminergic neurons in Drosophila melanogaster. Barsh GS, ed. PLOS Genet. 2018. 14:e1007459. doi:10.1371/journal.pgen.1007459
12. Sachse S, Rueckert E, Keller A, Okada R, Tanaka NK, Ito K, Vosshall LB. Activity-dependent plasticity in an olfactory circuit. Neuron. 2007. 56:838-50. doi: 10.1016/j.neuron.2007.10.035.
13. Sharma A, Hasan G. Modulation of flight and feeding behaviours requires presynaptic IP3Rs in dopaminergic neurons. Elife. 2020;9. e62297.doi:10.7554/elife.62297
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16. Zhai B, Villén J, Beausoleil SA, Mintseris J, Gygi SP. Phosphoproteome Analysis of Drosophila melanogaster Embryos. J Proteome Res. 2008. 7:1675-1682. doi:10.1021/pr700696a

Author Response

Reviewer #1 (Public Review):

This manuscript describes conditions under which "Self-inactivating Rabies" (SiR) can be grown to limit mutations that would allow the virus to replicate in the absence of TEV protease. It is also shown that neurons directly infected with a non-mutated virus remain healthy and that the virus does not mutate in the brain in vivo. Remarkably there is nothing in the manuscript to address the obvious question that is raised by the observation that such mutations were occurring around the time of the initial description of circuit tracing with this virus. Can the transsynaptic tracing experiments in the absence of TEV expression (as described in their original Neuron paper) be replicated with SiR that is not mutated? This obvious omission suggests that the authors might have conducted such experiments and were unable to replicate their published results. It is imperative that the authors be forthcoming about whether they have conducted such experiments and what were the results. If they have not conducted such experiments, they should do them and include the results here. Regardless of the outcome, the results should be published. If they cannot replicate their results, then the reliability of the Neuron paper is in doubt.

How do the results presented here relate to the results published in the Neuron paper and why are they not definitive with respect to the utility of SiR? The original publication in Neuron presents results that do not appear to be plausible and are best explained by the possibility that some experiments described in that manuscript were conducted using mutated SiR. This became most apparent when shortly after the Neuron publication, the Tripodi lab shared SiR as well as TEV expressing cell lines for propagation with other labs. Several of those groups observed that when they progagated the SiR received from the Tripodi lab, there was a mutation that removed the linkage of the PEST targeting sequence to N. This would be expected to allow the virus to replicate and spread without the need for TEV protease to remove the PEST sequence - precisely the phenotype observed in the trans-synaptic tracing experiments described in the Neuron paper. In the Neuron paper, culture experiments showed that the N-PEST (SiR) rabies could not replicate in the absence of TEV. And additional experiments showed that the virus is not toxic to neurons directly infected. These are the same experiments that are replicated in this submission. But then (in the Neuron paper) comes the unlikely report that this virus can spread trans-synaptically in vivo, in the absence of TEV expression. An alternative explanation would be that the virus used for those experiments was mutated and that is why TEV expression was not needed. There are no experiments in the original Neuron paper that address this possibility. Specifically, the experiments in Neuron describing cell survival during trans-synaptic tracing are not adequate to rule this out. This is because the two timepoints during which neurons were counted correspond to an early time when labeled neurons would be expected to still be accumulating and a later time that might be past the peak and represent a time when many neurons have died. To quantify proportions of neurons that survive, it is necessary to follow the same neurons over time, as has been done to demonstrate that only about half of neurons infected with G-deleted rabies die (half survive). Until tests are conducted testing whether TEV expression is required to obtain trans-synaptic labeling with an SiR that is known to not be mutated, it is irrelevant whether mutations can be prevented under particular culture conditions. The utility of this virus depends on whether it can be used for trans-synaptic tracing without toxicity and this manuscript presents no experiments to address that. Further, the omission of such experiments is glaring, as it is difficult to imagine that they have not been attempted.

We thank the reviewer for giving us the opportunity to improve on this point. We have performed additional experiments to confirm the ability of revertant-free SiR virus to spread transsynaptically in vivo. Our data shows that non-mutated SiR spreads transsynpatically in the mouse brain when complemented with G. In addition, we also tested the effect of the addition of TEVp to the starter neuronal population and found that it can significantly improve spreading efficiency. These data confirm the transsynaptic spreading capabilities of unmutated SiR in line with our original report. Furthermore, the data show the enhancing effect on the spreading efficacy of supplementing TEVp to the starter cells, broadly in line with what was recently reported by Jin et al., 2023. We have discussed the implications of these findings and suggested future directions in the main text and discussion.

Additionally, for completeness, we also assessed the spread efficiency of the recently generated SiR-N2c (based on the CVS-N2c rabies strain) in presence and absence of TEVp. We found that SiR-N2c spreads significantly better in the BLA-> NAc circuit than the original SiR (based on the SAD-B19 strain), and that the same spreading efficiency is not achieved by complementing SiR-B19 with the G from CVS_N2c Rabies strain. Interestingly, we found only a very small effect of the addition TEVp to the starting cells on the number of transsynaptically labelled cells with SiR-N2c. We have discussed the implications of these findings in the main text and discussion.

Changes in the manuscript: We have updated Figure 1 with the addition of a 6-month time point and update the main text accordingly. The updated paragraph is provided here:

"Results, SiR transsynaptic spreading.

We then tested the ability of revertant-free SiR to trace neural circuits transsynaptically in the mouse brain. ΔG-Rabies vectors can be pseudotyped with the chimeric EnvA glycoprotein to selectively infect neurons expressing the TVA receptor, which is not endogenously expressed by mammalian cells (Wickersham et al., 2007b). We injected the nucleus accumbens (NAc) of CRE-dependent tdTomato reporter mice with an AAV expressing either TVA and the rabies G or TVA only. After 3 weeks, we re-injected the NAc with EnvA-pseudotyped revertant-free SiR-CRE or EnvA-pseudotyped SiR-G453X-CRE and assessed the CRE-dependent tdTomato expression presynaptically, in the basolateral amygdala (BLA). At 1 month post SiR injection, we detected no tdTomato+ cells in the BLA in TVA-only-injected animals, confirming the G-dependency for SiR transsynaptic spreading (Fig 5B-C). In contrast, as expected, transsynaptic spreading was apparent in the TVA+G condition. We observed similar numbers of presynaptically traced neurons in both SiR-CRE and SiR-G453X-CRE injected brains (169 ± 24 and 190 ± 36 tdTomato+ neurons, respectively; two-tailed t-test, P = 0.64; Fig 5B-C). However, tdTomato+ microglial cells were only detected in the SiR-G453X-CRE condition indicating the re-emergence of toxicity of the revertant mutants (Fig 5B). We also tested the effect of supplying TEV protease to the starting cells, as this has been suggested to be a necessary step to ensure transsynapitc spreading. While the previous experiments unambiguously show that TEVp is not necessary for the transsynaptic spreading of SiR, the injection of an AAV expressing TEVp in the NAc did lead to an increase in the number of transsynaptically labelled BLA neurons (366 ± 69 tdTomato+ neurons; two-tailed t-test, P = 0.04; Fig 5C), indicating that TEVp-dependent SiR reactivation in starter cells can improve its spreading (Jin et al., 2023).

We recently showed that a novel SiR-N2c vector, derived from the neurotropic CVS-N2c Rabies strain, displays enhanced transsynaptic spreading and improved peripheral neurotropism over the original SAD B19-derived SiR (Lee et al., 2023). Hence, for completeness, we compared the transynaptic spreading efficacty of EnvA-pseudotyped revertant-free SiR-N2c and the original SiR. SiR-N2c labelled a greater number of BLA neurons at 1 month p.i. than what was detected with SiR (1691 ± 112 tdTomato+ neurons traced by SiR-N2c; two-tailed t-test, P = 2x105; Fig 5D-E). Additionally, TEVp expression in the starter cells in SiR-N2c tracing experiments had a negligible effect on the overall transsynaptic spreading (1934 ± 135 tdTomato+ neurons traced by SiR-N2c in presence of TEVp; two-tailed t-test, P = 0.24; Fig 5D-E). Since the use of G from the CVS-N2c Rabies strain (G_N2c) has been shown to improve ΔG-Rabies (SAD-B19) retrograde tracing (Zhu et al., 2020), we tested if complementing EnvA-pseudotyped SiR with G_N2c in the NAc could increase its spreading. While we detected more BLA tdTomato+ neurons than in our previous experiments, complementing SiR with G_N2c still labelled less neurons than SiR-N2c, even when TEVp was provided to the starter cells (487 ± 164 and 844 ± 14 tdTomato+ neurons traced by SiR in absence or presence of TEVp, respectively; Fig 5D-E)."

Discussion

"ΔG-Rabies vectors are powerful tools for the dissection of neural circuit organization thanks to their ability to spread retrogradely to synpatically-connected neurons. Here, we show that EnvA-pseudotyped revertant-free SiR vectors effectively spread transsynpatically in the mouse brain. Importantly, the co-delivery of an AAV expressing TEVp in addition to G increase the number of traced neurons in presynaptic areas, likely due to the TEVp-dependent reactivation of SiR in vivo (Ciabatti et al., 2017), in line with recent results (Jin et al., 2023). This should be considered when planning transsynaptic tracing experiments using SiR. To improve SiR spreading efficiency, further studies should investigate the use of inducible TEVp, as we previously showed (Ciabatti et al., 2017), that could maximise spreading efficiency while minimising possible side effects of prolonged protease expression.

Interestingly, we found that the recently developed SiR-N2c vector, generated by applying the same proteasome-targeting modification to the genome of the CVS-N2c ΔG-Rabies strain (Lee et al., 2023), show a higher number of retrogradely labelled neurons compared to the original SiR (SAD-B19) (Fig 5). Additionally, the co-delivery of TEVp had a smaller effect on the number of neurons transsynaptically-traced by SiR-N2c. Interestingly, the gap in trassynaptic spreading efficacy between SiR (SAD-B19) and SiR-N2c could not be filled by complementing the SiR with the neurotropic G_N2c. This could be linked to a more efficient packaging of SiR-N2c by G_N2c (Reardon et al., 2016; Sumser et al., 2022) or by the particularly high speed of CVS-N2c strain propagation (~12hrs)(Callaway, 2008; Hoshi et al., 2005). These results point to SiR-N2c as the vector of choice for transsynaptic experiments."

Other comments:

"A recently developed engineered version of the ΔG-Rabies, the non-toxic self-inactivating (SiR) virus, represents the first tool for open-ended genetic manipulation of neural circuits." It is not clear what the authors intend to be claiming with respect to "open-ended genetic manipulation of neural circuits" but it is clear that this assertion is overblown. There are numerous tools that are available for genetic manipulation of neural circuits. This is not the first, won't be the last, and it is arguably not the best.

We have rephrased this sentence.

Changes in the manuscript: The updated paragraph and figure panel is provided here:

Abstract

"A recently developed engineered version of the ΔG-Rabies, the non-toxic self-inactivating (SiR) virus, allows the long term genetic manipulation of neural circuits."

"Interestingly, a fraction of tdTomato+ neurons survived in ΔG- Rab-CRE-injected brains, differing from what we observed when injecting ΔGRab-GFP, where no cells were detected at 3 weeks p.i. (Fig 3CD) (Ciabatti et al., 2017). " This is a known result (same as Chatterjee et al., 2018) with a known mechanism. GFP expression is not observed because the rabies virus transitions from transcription to replication resulting in the termination of GFP expression. But Cre-recombination of the genome permanently labels cells with TdTomato. This is how Chatterjee et al. demonstrated that half of the neurons infected with G-deleted rabies survive. They imaged cells and saw that the GFP disappeared but the cells marked by Cre-recombination and RFP expression remained healthy indefinitely. The consideration of this in the Introduction is strange. There is no reason to suppose that Cre expression would somehow protect cells from rabies infection and there is no need to propose any such mechanism to explain the observed results.

This consideration is a response to the suggestion, proposed in Matsuyama et al 2019, that the toxicity reduction observed in ΔG-Rab-CRE could be linked to the expression of Cre recombinase compared to a cytosolic protein.

"Here we show that revertant-free SiR-CRE efficiently traces neurons in vivo without toxicity in cortical and subcortical regions for several months p.i.."

This wording is disingenuous and appears to be intentionally misleading. "Trace" implies that circuits were traced by transynaptic labeling, which they were not.

To avoid any misunderstanding, we have now changed trace to infect.

Changes in the manuscript: The updated sentence is provided here:

Abstract

"Here we show that revertant-free SiR-CRE efficiently infect neurons in vivo without toxicity in cortical and subcortical regions for several months p.i.."

Reviewer #2 (Public Review):

The study by Ciabatti et al examined the mutation issue for self-inactivating rabies (SiR), which was found by other labs. The authors identified the mutations in the rabies genome and showed that this mutation occurred more frequently after multiple passage of production cell lines with suboptimal TEVp expressions. The authors further showed that such mutation did not accumulate in vivo and that SiR-labeled cells remained alive across longitudinal imaging in vivo.

In this study, the rabies genome is rigorously examined by sequencing many viral particles from independent preparations. The rabies with point mutation in the PEST domain is directly engineered for sequencing and infection test. Overall, the mutation issue is well addressed by the authors and the conclusions are well supported, but some more aspects of discussion and data analysis need to be extended for an easier production of SiR in a condition not that optimal.

1) The authors stated that one should produce SiR from cDNA in order to avoid the potential mutation in SiR. From a practical point of view, it would be much better to amplify the rabies from a stock virus directly in the production cell lines. Any discussion or exploration on this direction would be appreciated in the field.

We thank the reviewer for giving us the opportunity to improve on this point. We have added in the discussion a paragraph suggesting the number of passages to be used during production for the packaging cells and viral stocks, referring to the equivalent passage in our experiments.

Changes in the manuscript: The updated paragraph is provided here:

Discussion

"Notably, we found that TEVp activity inevitably decreases after several passages of amplification of HEK-TTG, thus fresh low passage packaging cells should always be used to produce SiR preparations. Our results suggest that stock for packaging cells should be made within a couple of passage after selection is established, and then used freshly defrosted to produce SiR viruses (equivalent to P0 cells in Fig 2B-C). Similarly, SiR supernatant stocks should be made directly from cDNA transfection and amplified for a maximum of 2 passages (equivalent to SiR P0 in Fig 2E) before being used for large scale SiR productions."

2) 6 passages of production cell lines are not that extensive. In Fig.2C, there was already some level of TEVp activity reduction at 2nd passage. It is not clear to me that how the TEVp activity reduction naturally happens. Is there some room to play around puromycin concentration to maintain high TEVp activity?

As mentioned in the previous point, we have added in the discussion a paragraph describing the recommended number of passages to be used during production of the packaging cells and viral stocks, referring to the equivalent passage in our experiments. We clarified that our starting P0 conditions for packaging cells and stock SiR viruses were equivalent to already amplified stocks ready for viral production, which would add only 1-2 passages.

Reviewer #3 (Public Review):

This paper is a response to the report by Lin et al., bioRxiv 2022 (DOI: https://doi.org/10.1101/550640) that mutations in the genome of SiR were identified, which could result in a canonical G-deleted Rabies virus.

Strengths:

First, the authors found that SiR production from cDNA leads to revertant-free viruses by analyzing a total of 400 individual viral particles obtained from 8 independent viral productions with Sanger sequencing. Next, they identified the molecular mechanisms of mutations in the SiR; they found that extensive amplification of packaging cells HEK-TGG leads to the selection of clones with suboptimal TEVp expression level, which leads to the accumulation of revertant mutants, where, as the authors discuss, the revertant mutants have a specific replication advantage. Based on these observations, the authors recommend producing SiR freshly from cDNA with low passage packaging cells. Lastly, the authors observed that SiR-infected hippocampal and cortical neurons can survive for longer periods of time than the neurons infected with revertant mutants or a canonical G-deleted Rabies virus by combining next-generation sequencing of RNAs isolated from infected tissue and 2-photon in vivo longitudinal imaging of infected cortical neurons. Together, these findings support the idea that the degradation of N by PEST-mediated cellular mechanism results in the self-inactivation of SiR as suggested in the original SiR manuscript (Ciabatti et al., Cell 2017). Thus, SiR remains a powerful viral tool for the chronic investigation of neuronal circuitry and function as long as the virus is prepared in a way the authors recommend.

Weaknesses:

While most of the findings are solid, some conclusions are not fully supported by the data presented. The authors need to address the following points: Reviewer #3

1) In Figure 3B-D, the authors concluded that SiR-CRE -infected cells did not show cell death in contrast to Rab-CRE and SiR-G453X, but it cannot be fully supported only by this experiment. The authors should consider the potential variance in infection efficiency in each experimental animal and show evidence of suppressed cell death. In addition, it needs to be confirmed that SiR-Cre is diminished in infected cells at later times. The authors should explain and address these concerns by conducting additional experiments, for example, cleaved caspase-3 staining and quantification of virus RNA levels in each time point as performed in their previous study Ciabatti et al., Cell 2017 (DOI: 10.1016/j.cell.2017.06.014).

We thank the reviewer for the suggestion and give the opportunity to strengthen our work. We have added an analysis of the rabies transcripts over time in SiR-infected hippocampi (Fig S4). The drastic decrease of SiR RNA, along with the finding that the numbers of tdTomato-positive cells remain comparable at each time points support the reduction in mortality in SiR infected cells. We have added this data and clarified this point in the text..

Changes in the manuscript: The updated paragraph is provided here:

Results: Difference in cytotoxicity between ΔG-Rabies, PEST-mutant SiR and SiR

"We detected no decrease of tdTomato+ neurons in SiR-infected hippocampi (4109 ± 266 tdTomato+ neurons at 1 week p.i.; 4458 ± 739 tdTomato+ neurons at 2 months p.i.; one-way ANOVA, F = 0.08, p = 0.92, Fig 3C-D) while only 44% of tdTomato+ neurons were detected in Rabies-targeted and 60% in SiR-G453X-targeted hippocampi at 2 months p.i. (1422 ± 184 at 1 week versus 624 ± 114 at 2 months p.i. for ΔGRab; one-way ANOVA, F = 11.55, p = 0.003; 3052+508 at 1 week versus 1829+198 at 2 months p.i. for SiR-G453X; one-way ANOVA, F = 4.27, p = 0.05; Fig 3C-D). Additionally, we confirmed inactivation of revertant-free SiR by analysing the decrease of Rabies transcripts in the infected hippocampi over times (Fig S4). These results support the lack of toxicity of SiR on the infected neurons, in line with our previous findings (Ciabatti et al., 2017). Moreover, these data confirm the requirement for an intact PEST sequence to sustain the self-inactivating behaviour of SiR and suggest that PEST-targeting mutations do not occur in vivo."

2) In Figure 3E-F, to ensure the long-term stability of SiR-Cre in the vivo mouse brain, authors conducted SMRT sequencing 1 week after the virus infection. To test the potential slow accumulation of mutations at 1-month and 2-month, the authors should perform the same experiment at these time points. Only when SiR-Cre was undetected at 1-month and 2-month, would it be reasonable to show only 1-week data, however, such data is not presented.

We thank the reviewer for the suggestion. We have added an analysis of the Rabies transcript in the infected Hippocampi showing a drastic decrease of SiR RNA over time. This result, along with the finding that similar numbers of tdTomato-positive cells are detected in the infected hippocampi over time, support our choice of an early time point to find emergence and accumulation of revertant mutations.

3) In figure 4, the authors used only 2 mice for this experiment, although this is one of the most important experiments to ensure SiR-infected cells stay alive for the long term in vivo animals. It should be confirmed whether the conclusion remains the same by increasing the number of animals.

While we understand why the reviewer put forward this suggestion, we believe that our choice of number of animals is appropriate as the investment in time and resources to adding further animals would not strengthen our conclusion (which we have indirectly assessed previously (Ciabatti et al 2017) and here in Fig 3). For completeness, we have added a Fig4_S1with the images of all the ROI at every time points used in Fig 4.

4) The legend in Table 3 doesn't match the contents.

We thank the reviewer for pointing this out, in response we have now updated Table 3.

Author Response

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

Thank you for reviewing our manuscript " Energy Coupling and Stoichiometry of Zn2+/H+ Antiport by the Cation Diffusion Facilitator YiiP". After carefully considering the reviewer's comments, we have made substantial changes to the manuscript, which we believe is now much improved. In addition to clarifying various points raised by the reviewers, we have also added a variety of new data from both experimental and computational studies. We hope that these changes will satisfy the reviewers such that we can move forward towards finalizing the publication process.

New data added to this revision includes

• SEC profiles comparing D287A and D287/H263A before and after complex formation with Fab to illustrate formation of higher order oligomerization (Suppl. Fig. 6).

• Control trace from MST using Mg2+ to illustrate reproducibility (Suppl. Fig. 6).

• Results from MD simulation of D72A mutant to explore the Asp72-Arg210 salt bridge as a stabilizing element (Fig. 4)

• Analysis of cavities in WT and D70A_asym structures to illustrate occlusion of site A (Suppl. Fig. 13).

• In addition, we have redone MD simulations for YiiP with site B empty. These simulations were originally done (3 x 1 μs) with a modified version of the zinc dummy model and we have redone them (6x1 μs) using our previously published zinc dummy model to be strictly consistent with other simulations on holo, apo and D72A structures. The new results are qualitatively consistent with the previous simulations and our conclusions remain unchanged.

In addition, the text has been modified and several figures have been updated to address concerns of the reviewers as described below.

Although figures will ultimately be renumbered to conform with eLife formatting, they have retained their original numbers for this revision to prevent confusion, except that Suppl. Fig. 13 is a new figure added at the request of reviewer 2.

Reviewer #1 (Recommendations For The Authors):

I have only a few comments that might need clarification from the authors:

• If the unbinding of Zn2+ to site B triggers the occlusion (and maybe the OF state) and the external pH does not affect that binding, how is it prevented from being always bound to Zn2+ and thus occluded also while it should be transporting protons (B to C panels in Figure 5)? Are there some other factors that I am missing?

Our data shows that the affinity of site B is low (micromolar), especially relative to the concentration of free Zn within the cytosol (picomolar - nanomolar). Therefore, we would expect that site B is normally empty and that the resting state would be represented by panel D in Figure 5. An elevation of Zn concentration, or delivery of Zn to the transporter by some as yet uncharacterized binding protein, would initiate the cycle starting with panel E.

It is notable that the TM2/TM3 loop adopts a novel conformation in the occluded state, in which it extends to interact with the CTD (panel G in Figure 5). In this conformation, the Zn binding site is disrupted, thus preventing binding of additional Zn ions to the TM2/TM3 loop. Although we do not know how this loop behaves as the protein transitions to the outward-facing state (panels A & B), it is tempting to speculate that it retains the extended conformation until the protein returns to the inward-facing, resting conformation in panel D. This idea has been added to the revised manuscript (line 464).

In addition, we have added a sentence (line 507) to explicitly state our assumption that Zn only binds to site B in the IF state.

• I am not an expert on experiments, but the results for mutants that abolish site C are difficult to understand. For D287A/H263A, the SEC columns data suggest a population of higher oligomers. Still, for the D70A/D287A/H263A and D51A/D287A/H263A, they showed a native dimer. I understand your suggestion that the Fab induces the domain swap, but how do you explain the double mutant SEC column result? Please elaborate.

The unexpected behavior of site C mutants certainly introduces complexity into our study. Considering all the ins and outs of our analyses, we are confident that site C is a high-affinity site that is constitutively occupied and serves as a structural site to stabilize the architecture of the native homodimer. In the original submission, we included SEC profiles for D287A and D287A/H263A in Suppl. Fig. 4 as well as profiles for D70A/D287A/H263A and D51A/D287A/H263A in Suppl. Fig. 6. The former in Suppl. Fig. 4 characterize the complex between mutant YiiP and Fab (for cryo-EM), whereas the latter in Suppl. Fig. 6 represent YiiP in the absence of Fab (for MST). In the absence of Fab, the mutations do not alter the elution volume at ~12 ml, consistent with the conclusion that the native YiiP homodimer remains unperturbed. In the presence of Fab, mutations affect the SEC profile in two ways: a shift in the main peak to ~11 ml, and appearance of a subsidiary peak at ~10 ml. The shift of the main peak can be explained by formation of a complex between YiiP and Fab. Presence of the subsidiary peak - seen for D70A, D287A, and D287A/H263A mutants - can be explained by formation of a dimer of dimers (4 YiiP + 4 Fab), which could be isolated as a subpopulation of particles during the processing of cryo-EM images. For D70A and D287A, the individual dimers were unperturbed in this dimer-of-dimers. In fact, we used masking and signal subtraction to isolate the individual dimers and included them in the final reconstruction together with the more prevalent dimeric species (2 YiiP + 2 Fab).

The D287A/H263A-Fab complex behaved differently. The main peak of the SEC profile was shifted to 10 ml, indicating that a dimer of dimers was the prevalent complex; absence of a peak at 11 ml indicated that isolated dimeric complexes were no longer present in the solution. Furthermore, the subsidiary peak was at ~9 ml, indicating an even larger complex not seen in the other preparations. The appearance of particles in cryo-EM images were distinct from the other mutants (e.g., compare 2D classes shown in panels C and D in Suppl. Fig. 4). 3-D structures revealed dimer-of-dimers with the domain swap as well as larger linear oligomers. Although not well resolved due to preferred orientation, it appears that these linear oligomers consist of a propagated domain swap.

We have included some new data to bolster our conclusion that, although the D287A/H263A mutant destabilized site C, Fab binding was responsible for inducing the domain swap. The new data, presented in Suppl. Fig. 6, shows an SEC profile for a preparation of D287A/H263A both before and after formation of the complex with Fab. In addition to including this new data, we have amplified our description of these SEC profiles under the heading "Zn2+ binding affinity" in the paragraph starting on line 289 to try to clarify this complex issue for the reader.

• Since in the D287A mutant, you are disrupting the preferred tetrahedral coordination of Zn2+, but it still binds, do you observe any waters that compensate for the missing aspartate? Maybe in the MD simulations?

Unfortunately, the resolution of the cryo-EM maps are not high enough to resolve water molecules that we assume are present at sites B and C. For the MD simulations, we did not use mutants, but simply removed Zn from each of the sites. So we are unfortunately not able to answer this question with the available data.

Reviewer #2 (Recommendations for The Authors):

1) It is no doubt that cryo-EM structures of four types of zinc-binding site mutants of a bacterial Zn2+/H+ antiporter YiiP provide important insight into distinct structural/functional roles of each of the binding sites. However, overall resolution of the cryo-EM maps presented in this paper is not high enough to address the Zn2+ coordination structures, the kinked TM5 segment seen in a D51A mutant, and the extended conformation of TM2/TM3 loop seen in the D70A asymmetric dimer. It would be better to highlight the density of the above regions and discuss the vitality of their structure models. Similarly, the presence of additional water molecules at sites B and C (line 117) do not seem convincing.

We are completely sympathetic with the recommendation of illustrating the map quality as thoroughly as possible. We hope that interested readers will download map and model from the respective PDB and EMDB repositories and see for themselves. Nevertheless, we have provided several new figure panels to illustrate explicitly the densities associated with the kinked TM5 segment in the D51A mutant (Suppl. Fig. 2) and the extended TM2/TM3 loop in the D70A mutant (Suppl. Fig. 5) and have referred to them at appropriate places in the text (line 128 and line 151). In Suppl. Fig. 5, we also included figure panels to show densities for this loop in WT and D287A/H263A mutants.

It is true that the maps are generally of insufficient resolution to clearly define the coordination of Zn. The relevant densities are shown for all sites in all mutants in Suppl. Fig. 2. Despite this shortcoming, the coordination geometry is well established by the previous, higher resolution X-ray crystal structure as well as by MD simulations. Each site is shown in the insets of Fig. 1b, c and d. The new cryo-EM densities and resulting models are consistent with this coordination, which we have now pointed out in the legend to Fig. 1. The important point is that the new cryo-EM maps document the occupancy of ions at the individual sites as well as the large scale conformational changes associated with this occupancy, which was the main goal of the study.

Finally, we agree that the presence of additional water molecules at the sites is not well supported; because this issue has little bearing on our analysis, these comments have been removed.

2) Identification of the occluded state in D70A asymmetric dimer is exciting, hence this reviewer recommends the authors to highlight the structure of this state more effectively in comparison with the IF/OF states. It would be better to show the side views of the superimposition between the occluded and IF/OF states, and the pore profile and radius in the TM domain of these three states. The authors should also show the density map of site A (including M2 and M5) in the occluded protomer of the asymmetric dimer in Suppl. Fig. 2. Additionally, the authors should include information regarding the cytosolic or periplasmic view in the legend of Figure 3A, B, D, F, G, and H.

As suggested, we have prepared a new supplemental figure juxtaposing the IF and occluded states and depicting differences in pore radius and accessibility of site A (Suppl. Fig. 13, initially referred to on line 152 and various other locations in the manuscript with methods described on line 680). However, we unfortunately do not have a structure in the OF state to complete this comparison.

The density map for site A including M2 and M5 of the occluded protomer is shown in Suppl. Fig. 2 in which density thresholds have been adjusted to show the helices.

We have updated the figure legend for Figure 2 (referred to as Figure 3 by the reviewer) with the orientation of view, which are all from the cytoplasm looking toward the membrane.

3) MST analyses using the YiiP mutants with a single Zn2+-binding site at different pH are useful, and the data interpretation in combination with computational approaches of CpHMD and MST inference are nice challenges, indeed. However, it may, in a sense, appear that the MD simulations have been carried out intentionally and/or forcibly so that the outcomes are compatible with the experimental MST data. Although this is not unusual or unacceptable, this reviewer is concerned that the determined pKa values of some residues, especially Asp residues at Site A, are unusually high. The validity of this outcome should be discussed from physicochemical viewpoint; what factors raise the pKa of Asp51 and Asp159 so high. In this context, the MST inference titration curve seems unusually steep for D159 (and H155), of which validity needs to be discussed. This reviewer is also concerned about the large variations per measurement in the MST experiments (Suppl. Fig 6 E, F, and G). Are such large variations common to this experiment? Optimization of the measurement conditions such as protein concentration, and/or increase of AlexaFluor-488 labeling efficiency might greatly improve the reproducibility per measurement. The authors should include information on which residue(s) is labeled with AlexaFluor 488 in YiiP (line 641).

One of the outcomes of our so-called MST-inference algorithm was the conclusion that protonation states for H155 and D159 were coupled. The basis for this conclusion is described in some detail in the Methods section (paragraph starting on line 1025) and results in cooperativity in the protonation state of these two residues. This cooperativity explains the unusually steep binding curve in Suppl. Fig. 10e. We added a couple of sentences to explain this result in the Results under "Zn2+ binding affinity", line 352.

There is indeed precedent for increased pKas of acidic residues based on experimental measurements for Glu and inferred for Asp, both in membrane proteins. Computational approaches similar to the ones we use (including some of our own earlier work) have also pointed to elevated pKas by 1-3 units for Asp residues. We included a paragraph in the Discussion of Stoichiometry and energy coupling (line 537) citing these references and explaining that such pKa shifts reflect strong Coulomb interactions of titratable residues in close proximity in the low dielectric environment of the membrane.

We believe there is a misunderstanding about our presentation of raw data for the MST experiments in Suppl. Fig. 6. Panels E, F and G show an overlay of data from the entire Zn titration, which is therefore expected to change according to the Zn concentration in each capillary. We have revised the corresponding legend to clarify the plots. We have also included traces from a Mg2+ titration as a negative control that better illustrates the reproducibility of these measurements.

The AlexaFluor dye contained the reactive NHS group which preferentially targets the N-terminus of the polypeptide chain. Although labeling of lysine side chains is possible, we do not expect much given the low labeling stoichiometry of ~1:1 used for our experiments. We updated the Methods section under MST experiments (line 689) with this information.

Reviewer #3 (Recommendations For The Authors):

By measuring the binding affinity of site A using the D70A mutant that retains site C at pH 5.6 is should be possible to verify if the affinity reported in Table 2 is affected by the quaternary structure of the system. The 40-fold difference in affinity between site A and site C at pH 5.6 should be sufficiently large to permit a meaningful measurement.

To address this suggestion, we have included additional data in Table 2 from the D70A/D287A mutant. Based on the cryo-EM structure of D287A, we expect that site C is still intact, which is why it was omitted from the original manuscript. However, the affinities measured at pH 6 and 7 are very consistent with those from the triple mutant (D70A/D287A/H263A), supporting the idea that complete abolishment of site C does not affect measurement of affinity at sites A or B. This additional data is presented in the section on "Zn2+ binding affinity" on line 304. We also note that the SEC profiles in the absence of Fab are consistent with formation of the native homodimer for all the mutants, as described in our response to reviewer 1 and now shown in Suppl. Fig. 6.

More details should be provided on the force field used for zinc(II) ions in MD simulations. Currently, there is only a reference to another article, where this info is in the caption of a supplementary figure.

We added a summary of our previous work to develop a non-bonded dummy model for Zn(II) on line 727 in the Methods section entitled "Overview of the MD simulations. However, we would like to point out that all details on the parameter development and the parameters themselves are stated in the Methods section “Classical force field model for Zn(II) ions” in our previous paper [Lopez-Redondo et al, J Gen Physiol 143 (2021)] and parameter files are available as package 2934 in the Ligandbook repository https://ligandbook.org/package/2934 .

We also realized that in the originally submitted version of this manuscript we reported “empty site B” simulations with an updated and experimental non-bonded Zn(II) dummy model that has close to experimental first-solvation shell water residence times but slightly worse solvation free energy. Although that does not really matter for these simulations because there was no Zn2+ ion in site B, we nevertheless performed a new set of 6 x 1 µs simulations with our published (J Gen Physiol 2021) Zn(II) model to make all simulations fully consistent with each other. The results remained qualitatively the same, with a lack of zinc ions in site B leading to increased flexibility in the TM2/3 loop and ultimately destabilization of the TMD-CTD interaction.

Author Response

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

We sincerely appreciate the opportunity to revise the manuscript and the reviewers' critical comments and valuable suggestions. After carefully revising the manuscript, we strongly believe that the reviewers' comments are invaluable and will significantly enhance the quality of the manuscript and contribute to our future research. Following the reviewers' comments, we conducted a comprehensive and meticulous review, addressing each point individually and making extensive modifications and corrections. The responses to each question are provided in a point-by-point manner as follows:

Reviewer 1:

This study delves into the impact of imidacloprid, an insecticide documented for its toxicity towards honeybees, on the development of bee larvae. The investigation involved exposing bee larvae to various concentrations of imidacloprid, and observing the resultant effects.

The findings of this study revealed that imidacloprid exerted a dose-dependent delay in the development of bee larvae, marked by reductions in body mass, width, and an overall decline in the growth index. Moreover, at elevated concentrations, imidacloprid was observed to impair neural transmission, induce oxidative stress, inflict damage to the gut, and inhibit hormones and genes essential for development. The larvae were found to engage antioxidant defense systems and deploy detoxification mechanisms to mitigate these effects.

However, the manuscript could be significantly enhanced through several improvements. Firstly, the structure of the manuscript warrants refinement to foster coherence and clarity. Additionally, there is a need for careful reevaluation of the concentrations of imidacloprid employed in the study, to ensure their relevance and applicability. In terms of references, greater attention to accuracy in citation is imperative.

Furthermore, while the authors have provided an overview of the general effects of imidacloprid on both vertebrates and invertebrates, the inclusion of a more exhaustive literature review with a specific focus on honey bees and other insects would bolster the context and significance of this research. This would be particularly beneficial in the introduction section, which should be subjected to a major revision.

In summary, this study offers preliminary evidence of the detrimental effects of imidacloprid on the development of bee larvae by interfering with molting and metabolism. This research holds potential as a valuable resource for assessing the risks posed by pesticides to juvenile stages of various animal species.

On behalf of all the authors, I express our most sincere gratitude for your critical comments and suggestions. Following your suggestions, we have thoroughly reviewed and revised the entire manuscript, including the issues of imidacloprid concentration and citation accuracy you raised. More importantly, we have significantly revised the structure and content of the introductory section of the manuscript to include many more detailed reviews of critical literature, with particular attention to the overview of relevant research on honey bees, Drosophila, and other insects, to promote coherence and clarity of the introduction and to enhance the context and importance of this research. We hope that these changes meet with your approval. Overall, your valuable comments have greatly improved the quality of the manuscript and will facilitate our future research.

Q1: Line 48, "Adults exposed to high doses of imidacloprid experience", please provide a more precise value for the high doses.

Thank you very much for your comments. Following your suggestion, we have provided precise values for high doses of imidacloprid for adult exposure based on the study by Dr. Wu et al. 2001.

Q2: Line 82, There are several larvae effect reports using next generation sequencing approach. The authors should include those related references in this section.

Thank you for your comments. We have included relevant references in our revised manuscript.

Q3: Line 394, for the concentration design, the maximum concentration of imidacloprid used in this study is 377 ppb, which is from the imidacloprid residue level in beeswax. Bees don't consume beeswax, and the reference is wrong.

Thank you for raising this critical issue. As you point out, bees do not eat beeswax, but it is important to stress that this may well mean that the bee larvae themselves are exposed to higher doses. Therefore, in this study, we ultimately designed for the worst-case scenario of 377 ppb of imidacloprid residues in beeswax. We would like your agreement on this point. In addition, we have corrected the citation errors in the references here and included them in the revised manuscript.

Reviewer 2:

This study provides evidence on the ability of sublethal imidacloprid doses to affect growth and development of honeybee larva. While checking the effect of doses that do not impact survival or food intake, the authors found changes in the expression of genes related to energy metabolism, antioxidant response, and P450 metabolism. The authors also identified cell death in the alimentary canal, and disturbances in levels of ROS markers, molting hormones, weight and growth ratio. The study strengths come from applying these different approaches to investigate the impacts of imidacloprid exposure. The study weaknesses are not providing an in-depth investigation of the mechanisms behind the impacts observed and not bringing the results in light of the current literature. For instance, the authors' hypothesis is based on two main points, the generation of ROS that leads to gut cell death and energy dysfunction, and the increased P450 expression. They propose this increases P450 expression which in turn increases energy consumption and could contribute to developmental retardation. There is however no investigation on the mechanisms of ROS generation (it could be through mitochondrial damage, Nox/ Duox activity, NOS activity, P450s activity, etc). A link between higher P450 expression and increased energy consumption leading to energy deprivation is also missing. It would also be important for the authors to provide a more complete literature review as previous works have investigated imidacloprid sublethal dose impacts in larval stages for bees and other insect models.

I greatly appreciate your insightful comments and valuable suggestions on behalf of all the authors. Thank you for identifying the limitations of this study and providing valuable comments and suggestions. These comments and suggestions have significantly improved the quality of the paper and will facilitate our future research. Following your comments, we have revised and corrected the manuscript point by point. We hope that these corrections meet with your approval.

Q1: Abstract: It would be important to rephrase the abstract to make it clear when authors are talking about gene expression results or functional assays.

Thank you for your comment. Following your suggestion, we have revised the abstract to make it clearer, especially the description of the gene expression results. Please see lines 15-34 in our revised manuscript.

“Abstract Imidacloprid is a global health threat that severely poisons the economically and ecologically important honeybee pollinator, Apis mellifera. However, its effects on developing bee larvae remain largely unexplored. Our pilot study showed that imidacloprid causes developmental delay in bee larvae, but the underlying toxicological mechanisms remain incompletely understood. In this study, we exposed bee larvae to imidacloprid at environmentally relevant concentrations of 0.7, 1.2, 3.1, and 377 ppb. There was a marked dose-dependent delay in larval development, characterized by reductions in body mass, width, and growth index. However, imidacloprid did not affect larval survival and food consumption. The primary toxicological effects induced by elevated concentrations of imidacloprid (377 ppb) included inhibition of neural transmission gene expression, induction of oxidative stress, gut structural damage, and apoptosis, inhibition of developmental regulatory hormones and genes, suppression of gene expression levels involved in proteolysis, amino acid transport, protein synthesis, carbohydrate catabolism, oxidative phosphorylation, and glycolysis energy production. In addition, we found that the larvae may use antioxidant defenses and P450 detoxification mechanisms to mitigate the effects of imidacloprid. Ultimately, this study provides the first evidence that environmentally exposed imidacloprid can affect the growth and development of bee larvae by disrupting molting regulation and limiting the metabolism and utilization of dietary nutrients and energy. These findings have broader implications for studies assessing pesticide hazards in other juvenile animals”

Q2: Line 55-58: rephrase the sentences to make it clear that imidacloprid was not created in 1925, but only in the 90's.

Thank you for pointing out this error. We have corrected the citation. Please see the line 58 in our revised version.

Q3: Line 88: typo: " remain to be systematically investigated"

Thank you for pointing out this error. We have rewritten the sentence. Please see lines 121-122 in our revised manuscript.

Q4: Introduction is lacking important citations, a few of the important ones are: Farooqui 2013 (doi: 10.1016/j.neuint.2012.09.020.) - hypothesis linking neonic exposure, nAChRs receptors, and ROS in honeybees; Ihara et al 2020 (https://doi.org/10.1073/pnas.2003667117) - the targets of imidacloprid in honeybees; Martelli et al 2020 (https://doi.org/10.1073/pnas.2011828117) - mechanistic investigation of imidacloprid sublethal damage in Drosophila; Whitehorn et al 2018 (doi: 10.7717/peerj.4772) - investigation of imidacloprid sublethal dose impact on growth and development of butterflies; Chen et al 2021 (doi: 10.3390/ijms222111835) - sublethal effects of imidacloprid exposure on gene expression in honeybees at different life stages. It is important that the authors perform a more complete literature search to compare their work to previous ones, drawing conclusions and highlighting their novelties.

We greatly appreciate your insightful comments and valuable suggestions. Following your suggestions, we have made significant revisions to the structure and content of the Introduction section. We have incorporated the critical literature you provided and other relevant literature reviews, with a particular emphasis on studies of bees, fruit flies, and other insects. These revisions aim to improve the coherence, clarity, background, and significance of the Introduction. We hope that these modifications meet with your approval. Please see the red text in the Introduction section in our revised version.

Q5: Line 104: Explanation on the doses used should be included here, not later in the methods. Also, important to highlight that whereas the doses tested were found in bee products, they likely mean that the bees themselves were being exposed to even higher doses.

Thank you for your comment. Following your suggestions, we have moved the explanation of the imidacloprid doses used in this study to the Results section, as you mentioned. Please see lines 138-142 in our revised manuscript.

Q6: Line 112: It is important to identify the neuronal targets of imidacloprid in honeybees. Many are known. Some of the nAChRs targets were not investigated in this study (such as subunit alpha8 and beta1). Plus, is alpha2 an imidacloprid target? How does the expression of other nAChRs subunits compares? Importantly, these genes are expressed mostly in the nervous system, so a more correct approach would be a tissue specific analysis. The lack of tissue specific analysis is a consistent flaw throughout the methodological design.

Thank you very much for your important comment. Bees have more than ten nAChR subunit members. Imidacloprid inhibits acetylcholinesterase activity by competitively binding to acetylcholinesterase receptors. As you noted, this study did not investigate the expression of all nAChR subunits, including the alpha8 and beta1 subunits, in different tissues, which is a shortcoming of our study. We have always failed to make a technological breakthrough and cannot dissect to obtain important tissues from developing larvae alone. We have therefore had to abandon this design and use the whole larva as a sample for measurement. We are aware that this is a shortcoming of this research. In the future, we will make a breakthrough in technology and conduct a comparative analysis of all nAChR subunit genes in different organizations and developmental stages to obtain more comprehensive and accurate data. Thank you again for raising this important issue and for your valuable suggestions.

Q7 ~ Q9: Line 125: P450s expression may have opposite behavior when exposed to insecticides depending on tissue (such as brain and fat body). When checking whole larva gene expression, the tissue specific profiles become diluted and thus less reliable (for reference, check: https://doi.org/10.1073/pnas.2011828117); Line 131: Again, for the analysis of oxidative stress it would be important to investigate a tissue specific expression pattern and measurement of ROS markers. Investigating different time points during the exposure also adds to the mechanistic understanding. Do all tissues respond in the same way? In which tissue does an increase in ROS generation start? How? Does it spread to other tissues? By which mechanisms is it generated; Results in general: Tissue specific analyses and more time points can provide a better understanding of how sublethal imidacloprid doses impact growth and survival. Thinking about the doses of choice in light of what bees might be exposed is also important. The mechanistic understanding is missing in the paper, and without it the study does not add much in comparison to previous ones.

Thank you very much for your valuable comments. As you pointed out, the intensity of P450 detoxification and oxidative stress varies considerably between tissues. When checking whole larva gene expression, the tissue-specific profiles become diluted, which is detrimental to elucidating mechanisms. In this study, we encountered technical barriers in obtaining independent samples of specific tissues for anatomical sampling. As a result, we had to forego analysis of some specific tissues, including the tissue-differentiated analyses of P450 gene expression patterns and ROS markers that you mentioned. We only examined larval overall detoxification and antioxidant responses to imidacloprid toxicity. While we do not believe that data from specific tissues are fully representative of the complex overall picture of larvae, there is no doubt that the decision to study larvae as a whole does not contribute to our complete understanding of the mechanisms by which imidacloprid causes larval developmental retardation and larval responses to imidacloprid toxicity. In addition, the fact that this study only analyzed one-time points during imidacloprid exposure and did not design and comparatively analyze different time points limits our complete understanding of the above mechanisms. In summary, as you have pointed out, tissue-specific analyses and more time points could better understand how sublethal doses of imidacloprid affect growth and survival. In future studies, we will overcome the technical challenges and refer to your suggestions for further systematic and in-depth mechanistic studies specifically targeting imidacloprid toxicity in different tissues at different exposure times and incorporate your suggestions, such as whether the response is consistent across all tissues, the origin of the increase in ROS production, how it increases, whether it spreads to other tissues, and the underlying mechanisms into the next experimental design. Again, Thank you for your constructive and valuable comments, which have provided valuable insight for our study on mechanisms. Undoubtedly, these comments will enhance the innovativeness of our study and greatly facilitate our future research.

Q10: Line 236: The conclusion that mitochondrial dysfunction is taking place is not well corroborated. Are there changes in mitochondrial aconitase activity to suggest the mitochondrial origin of ROS? How do mitochondria look like under electron microscopy? Evidence for mitochondrial damage from functional assays? Could the ATP reduced levels be caused by increased consumption by other systems, instead of reduced production? Without functional assays to demonstrate mitochondrial dysfunction the indirect measurements of gene expression at most suggest expression perturbations in mitochondria for the point in time when gene profiles were examined.

Thank you for the comments. Based on the data of the present study, i.e., suppression of mitochondrial oxidative phosphorylation (COX17, NDUFB7) and expression of genes of its alternative glycolytic pathways (Gapdh, Oscillin), as well as a decrease in the ATP content, suggests that imidacloprid exposure leads to impaired energy metabolism in larvae and not to mitochondrial dysfunction. We have corrected this uncritical language presentation error. Please see the lines 267 and 275 red text in our revised version. We hope that this correction will meet with your approval.

Q11: Though not the aim of the study, an important step forward would be to investigate whether these doses that do not impact survival but cause growth retardation could affect the many stereotypical behaviors displayed by the worker bees when they reach the adult life. Without this sort of analysis, it is difficult to stablish whether the doses tested will impact the colony health.

Thank you very much for your valuable suggestions, which give us broader ideas for our subsequent, more in-depth work on the mechanism of toxicity. Inspired by your suggestion, we plan to conduct further studies to investigate the effects of different levels of imidacloprid exposure on the developmental process of bee larvae and the underlying mechanism of toxicity. We will also investigate the intrinsic link between this juvenile toxicity and behavioral and physiological defects in adult individuals.

Q12: Line 376: the authors do not provide a link to their hypothesis that increased P450, and antioxidant response is reducing larvae nutrient supply.

Thank you for your comment. I apologize for not fully understanding your point. If you mean that the hypothesis proposed in this study that increased P450 and antioxidant responses reduce larval nutrient energy supply is not well-founded, we have already addressed this in the previous paragraph. See Figure 7 and lines 395-399 for more details in our revised manuscript.

Q13: Line 393: Were the colonies single-cohort? Were the frames from different hives mixed together to create the experimental groups? Or each experimental group comes from a different frame/colony? This information is important to establish how much genetic variation might exist between the different experimental groups.

Thank you for your comment. In this study, the selected colonies were healthy and not exposed to pathogens or pesticides. Two-day-old larvae from the same frames of the same hive were individually transferred to sterile 24-well cell culture plates. The plates contained a standard diet containing royal jelly, glucose, fructose, water, and yeast extract. We have included the above text in our revised manuscript. Please see the lines 430-432 red text in the revised manuscript.

Author Response

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

Please find enclosed our revised manuscript entitled “An unconventional gatekeeper mutation sensitizes inositol hexakisphosphate kinases to an allosteric inhibitor”. We would like to thank the editorial team and the reviewers for carefully reading the manuscript and for raising a number of valuable points. We have included additional data and discussion to address the questions raised. Please find the point-by-point responses below.

Reviewer #1:

1) While I understand that FMP-201300 is a tool (proof-of-concept) compound it would be useful to know if it has activity against IP6K1 (or IP6K2) in cells.

We were of course curious about this as well. Unfortunately, our attempts to generate cell lines in which IP6K1 or IP6K2 carry the gatekeeper mutation using CRISPR/Cas editing have not been successful so far. Nevertheless, to obtain information on the permeability and cellular activity of FMP-201300, we decided to treat wt cells, since the compound also inhibited IP6K1-wt and IP6K2wt at higher concentrations.

In a previous study, we could show that reduced intracellular 5PP-InsP5 levels lead to a decrease in rRNA synthesis (https://doi.org/10.1101/2022.11.11.516170). We now repeated this experiment with FMP-201300, along-side the known IP6K inhibitors TNP and SC-919, and could show that FMP-201300 it is able to reproduce this phenotype, strongly suggesting it is capable to diffuse through the cell membrane and act on IP6Ks. We have included this data as a new Figure (Figure S10) and in the discussion part of the manuscript.

2) Did the authors try docking studies to gain insight into the binding site of FMP-201300?

The reviewer raises an important point, and we indeed strongly considered docking studies during the progress of the project. However, given that the HDX-MS data show that the region around the αC-helix becomes much more flexible upon introducing the gatekeeper mutation, we were concerned that docking studies (which would be based on the static wt structure) may not accurately reflect the more dynamic state of the mutated IP6K.

Upon consulting with our colleagues with expertise in docking and molecular dynamics simulations, we believe that MD simulations would need to be performed to obtain a more realistic picture of this protein ligand interaction, which we would like to pursue in the future.

3) Regarding the SAR, it would be useful to know if both carboxylic acids are required for allosteric inhibition.

Given the available data, it appears very likely that both carboxylic acids are required for the inhibitor to unfold its potency. Compound A2, which only contained one carboxylate group, showed drastically reduced potency. We have altered the text in the main manuscript to get this point across more clearly.

4) It would be helpful if the authors presented a model for how they think the Leu210 to Valine mutation sensitizes IP6K1 to FMP-201300.

We agree that it is important to better visualize the structural factors that play a role in the sensitization towards the compound. We have generated a new Figure 5 (and the old Figure 5 is now Supplementary Figure 9), and added a section to demonstrate how we propose the mutation leads to the sensitization of IP6K1 to FMP-201300. For a better understanding, we have also included a depiction how the mutation already affects the apo structures. Furthermore, we have added some text in the HDX section, to better describe the proposed mechanism.

Minor:

1) Figure 4: The authors should use the same units in panels a and b.

Thank you for pointing this out, the figure was edited accordingly.

2) In the supplementary Excel file, it would be helpful to include a tab that contains a legend.

A contents page was added to help describe the layout of the supplementary Excel file.

Reviewer #2:

Overall, this is an excellent study of high quality. The identified FMP-201300 has the potential for further compound and probe development. My only minor comment is that the authors could spend more time discussing the proposed allosteric binding mode of FMP-201300 and provide more detailed figures to highlight the proposed interactions with the protein and the conformational changes that must ultimately take place to accommodate the allosteric modulator. I appreciate that the co-crystallization experiments did not yield bound inhibitor structures, but perhaps the authors could consider MD simulations to complete their study. However, that could be a story in itself and should not be a must for the publication of this great work.

We agree with the reviewer (and also reviewer 1) that it is important to better visualize the structural factors that play a role in the sensitization towards the compound. We have generated a new Figure 5 (and the old Figure 5 is now Supplementary Figure 9), and added a section to demonstrate how we propose the mutation leads to the sensitization of IP6K1 to FMP-201300. For a better understanding, we have also included a depiction how the mutation already affects the apo structures. Furthermore, we have added some text in the HDX section, to better describe the proposed mechanism. In brief, we propose that the mutation leads to increased flexibility of the region in the mutation, allowing accommodation of FMP-201300 and ATP. These same regions are also the regions that have large decreases in deuterium exchange upon addition of the inhibitor.

We also appreciate the comment about using computational methods, to predict the binding site (also a remark from reviewer 1). We strongly considered docking studies during the progress of the project. However, given that the HDX-MS data show that the region around the αC-helix becomes much more flexible upon introducing the gatekeeper mutation, we were concerned that docking studies (which would be based on the static wt structure) may not accurately reflect the more dynamic state of the mutated IP6K. As the reviewer points out, MD simulations would likely be needed to obtain a more realistic picture of this protein ligand interaction, which we would like to pursue in the future.

Author Response

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

Reviewer #1 (Public Review)

Overall, I quite enjoyed reading the manuscript and found it very well-structured and organized. I congratulate the authors for building this nice research. I do have a few major points to raise, but probably they would not affect the general message of the manuscript.

Thank you for taking the time to review our manuscript and the positive feedback. Following your suggestions, we have corrected some mistakes and added clarifications and a few of the suggested quality checks on the models. However, we decided not to run new analyses as: i) we believe there would be minor changes to the general message of the manuscript; and ii) while some suggested analyses are compelling, they are difficult to implement for different reasons or are outside the scope of the paper (clarified below).

I was confused about how IUCN data were used. The IUCN predictors are not mentioned in the model equations presented in the manuscript, but their effect size is reported in Figure 2.

Thank you for highlighting this issue. This was a typo: we forgot to mention the variable in both equations 1 and 2. Changed accordingly.

In the manuscript Methods, it is said that IUCN data was classified into 3 categories. I believe there was a mix of mechanisms in measuring it this way since at least two processes might be underlying IUCN data. First, one can inspect whether there is an effect on "scientific/societal interest" for assessed vs non-assessed species. This would not have any relationship with the assessed status itself. Assessed species are any with LC, NT, VU, EN, CR, EW, EX statuses, whereas non-assessed species might include DD and NE. Second, one may observe an effect of threat status itself, with threatened species being more researched than non-threatened species, this would only be possible for assessed species, although there are methods out there to impute missing statuses. By inspecting Figure 2, I got the feeling that only the second option was explored, but this would need to be confirmed.

We couldn’t test the effect of single categories (LC, NT, VU, EN, CR, EW, EX) because observations within factor levels were unbalanced. So, we re-grouped the different categories into three levels: “Threatened” (EX, EW, CR, EN and VU), “Non-Threatened” (NT and LC), and “Unknown” (DD and NE) and only tested this variable (your second option). Note that the effect size of the level Unknown is not shown in Figure 2 as this is the reference category. This is clarified in the caption of Figure 2.

In Figure 2, I was confused about the presence of three categories of domain. In the text, it states that four categories have been used. I believe these domains are non-mutually exclusive, that's why there is a fourth category. Would it not be better to assess the influence of domain through three dummy variables (terrestrial, marine, freshwater), where multiple presences (1's) would indicate the "multiple" category?

We opted for a categorical variable (rather than a dummy) to have the same number of variables in the two groups (‘species’ vs ‘culture’). This is needed for the variance partitioning analysis (VPA), because an unbalanced number of variables in one group of a VPA can artificially inflate R2 (see, e.g., this source: https://www.davidzeleny.net/anadat-r/doku.php/en:varpart). As for Figure 2, the level “Multiple”, being the reference category, is not shown. This is clarified in the caption: “Baseline levels for multilevel factor variables are: Domain [Multiple]”.

At present, I felt that the spatial components of your data were unexplored. Since you have centroids representing species distribution, it could be interesting to explore the presence of the species within protected areas or biodiversity hotspots. That might be something triggering at least scientific interest. Also, one can derive information about the major habitat of species occurrence (either using IUCN Major Habitat classification) or extracting overlap of species centroids with WWF biomes (e.g., simplified to just forested vs non-forested habitats; https://ecoregions.appspot.com/). Another point very common to research exploring biodiversity shortfalls is the proximity to research institutions (https://doi.org/10.1111/2041-210X.13152). And since societal interest is also being explored, what about the proximity to major cities (doi:10.1038/nature25181). Finally, other metrics derived from species centroids could inform "tropicality", if the species is tropical or not. Most often, the tropics species are neglected in comparison with those occurring in temperate regions.

We thank the reviewer for this suggestion, and we are aware that there are important spatial drivers of interest as highlighted in earlier research. Indeed, the spatial aspects of the data were somewhat underexplored as a deliberate choice because we hope to carry out additional work to explore these aspects in more detail. Nevertheless, we included the centroid of each species range as a broad proxy of its distribution, to help explore, for example, the role of species latitudinal distribution in driving interest metrics. We have also considered the suggestions provided as additional analyses, but we find these may be challenging to implement with the current data for a few reasons. First, each species centroid was calculated based on GBIF occurrences and therefore represents the midpoint of all locations, but not necessarily an area that is known to be occupied by the species. Using the centroid to assess whether a species is located in a given biome or within protected areas using this approach would therefore be potentially misleading (for example, for some terrestrial species it may fall in the sea, and vice versa). Also, for the same reasons, taking the centroid to estimate the species accessibility or proximity to research institutions may be misleading. We find that while important, these spatial aspects require a more nuanced approach to be explored in detail.

I was also thinking about the influence of time on the models. Species described long ago are often more known to people and scientists and had more "time" to be researched. Although metrics of societal interest were restricted to the last decade here, that does not necessarily mean that peoples' interest is not affected by their accumulated experiences. Similar reasoning applies to scientific interests, which have a lengthier time frame (~80 years). That said, the year of description or time since description could be added to capture some metric of time.

This is a good point, which we discussed prior to running the analysis. Indeed, there is evidence that such accumulated experiences can drive species interest as our own research has also previously highlighted (e.g. see Ladle et al. 2017 doi: 10.1002/pan3.10053). However, we felt that comparing the date of description as a proxy of accumulated human experiences with species was only fair within major biological groups and not between them. This is because taxonomic practices, definitions, and methods vary widely between biological groups. We therefore decided not to include time since description as a variable driving the measures of scientific and societal interest in this work. Nevertheless, we recognize the importance of the history of such experiences in driving human interest in species, and the consequences emerging from the loss of such links, and have thus included a brief discussion of this topic in the manuscript (see lines 177-182).

Model residuals could be checked for phylogenetic or spatial autocorrelation. I am aware there is no phylogenetic tree used, but the hierarchical taxonomy could be used (Phylum / Class / Order / Family / Genus) as a proxy for phylogenetic relationship.

We agree. Indeed, the hierarchical taxonomy was already included as a random factor (Phylum / Class / Order) in eq. 1. Note that we excluded Family and Genus from the random structure because in most Phyla a single genus and family has been sampled (as well as due to model convergence problems).

Concerning the spatial autocorrelation, one could check whether model residuals and their respective coordinate centroids of each species range. It is stated that GLMM has been used to avoid these non-independence issues, but it would be interesting to check whether residuals remained free of them.

Good suggestion, although the use of centroids may not be the most appropriate since it is only a rough approximation of each species distribution (see previous answer). Still, out of curiosity, we checked whether the random factor on biogeography was enough to capture residual spatial autocorrelation in the models. For this, we used the R package DHARMa, which performs a Moran's I test for distance-based autocorrelation. Given that some coordinates were duplicated, we grouped residuals by biogeographic regions (DHARMa requires all coordinates to be unique). Neither the Web of Science nor the Wikipedia models had spatial autocorrelation in the residuals:

Web of Science model: observed = –0.20482, expected = –0.14286, sd = 0.10682, p-value = 0.561

Wikipedia model: observed = –0.180820, expected = –0.142857, sd = 0.055513, p-value = 0.4941

A last point, it would be interesting to provide some sort of inset plots, such as barplots or donut plots (within the current plots), showing the proportion of species with respect to major clades and biogeographical regions.

This is a good suggestion, but we couldn’t find a good way to show this as an inset. We added a barchart showing the number of species in each Phyla/Division in the supplementary materials (Figures S2C). As for the proportion of species in each region, we thought it would be redundant with Figure S1 (summarizing spatial information in sampled species).

Reviewer #2 (Public Review):

Using standard and widely used tools, the authors revealed the factors (cultural, phenotypic, phylogenetic, etc.) shaping societal and scientific interest in natural species around the globe. The strength of this manuscript (and the authors') lies in its command of the available literature, database and variable management and analysis, and its solid discussion. The authors thus achieved a manuscript that was pleasant to read.

Thank you for taking the time to review our manuscript and the positive feedback.

While I agree that doing a global study requires losing details of local patterns, maybe this is exactly the biggest shortcoming of the manuscript, oblivious to how different cultures (compare USA to PNG, for example) are reflected in these global patterns.

Related to this previous point, my only other comment is about using English as a reference of societal interest (i.e., the presence of a common name in English). While English may be widespread in Academia, it is still not that common in other societal circles, especially those not using Wikipedia for lack of internet access.

We acknowledge the limitation of this choice, as well as our limited capacity to represent specific cultural contexts with our approach. Our decision to consider only the existence of English common names as a variable was partly driven by practical reasons, and partly by the very factors the reviewer highlights. Indeed, many cultures, communities and social circles do not use English frequently and also do not use the internet frequently. One consequence of this is also that the information compiled for species in other languages is more restricted than that available in English, including the existence of vernacular names. In languages other than English, it may even be the case that several common language names exist in reference to the same species, and this number may be an even better reflection of their cultural importance, but sadly this information is not comprehensively indexed across languages and biological groups which prevented us from considering it. On the other hand, most species have been attributed English common names as part of legislative, scientific and other societal processes, and it is therefore likely that if they are important in any specific cultural setting, they will probably also have a vernacular English language name. Ultimately, while we recognize the potential limitations of this decision, we felt that considering English common names was the simplest and less biassed approach to represent the degree with which a species is individually recognized nowadays. We now better expose the reasons for the decision to consider only English common names, and the limitations associated with it in the manuscript (lines 178-193).

Author Response

eLife assessment

This study reports the fundamental discovery of a novel structure in the developing gut that acts as a midline barrier between left and right asymmetries. The evidence supporting the dynamics, composition, and function of this novel basement membrane in the chick is in parts solid and in others convincing, but the investigation of its origin and impact on asymmetric organogenesis is not yet conclusive. This careful work is of broad relevance to anyone interested in patterning mechanisms, the importance of the extracellular matrix, and laterality disorders.

We extend our sincere gratitude to the editors at eLife for their meticulous evaluation of our manuscript, as well as the valuable insights shared in this Public Review. We also wish to convey our appreciation to the reviewers for their thought-provoking suggestions, which we are enthusiastic about integrating into our revised work. In this provisional response, our primary focus is to address the two main concerns raised: the necessity for functional data to elucidate the importance of the barrier, and the imperative to resolve uncertainties regarding its origin. We are dedicated to addressing these important points, and believe they will greatly enhance the quality and significance of our manuscript.

Joint Public Review:

When the left-right asymmetry of an animal body is established, a barrier that prevents the mixing of signals or cells across the midline is essential. Such a midline barrier preventing the spreading of asymmetric Nodal signaling during early left-right patterning has been identified. However, midline barriers during later asymmetric organogenesis have remained largely unknown, except in the brain. In this study, the authors discovered an unexpected structure in the midline of the developing midgut in the chick. Using immunofluorescence, they convincingly show the chemical composition of this midline structure as a double basement membrane and its transient existence during the left-right patterning of the dorsal mesentery, which authors showed previously to be essential for forming the gut loop and guiding local vasculogenesis. Labelling experiments suggest a physical barrier function, to cell mixing and signal diffusion in the dorsal mesentery. Cell labelling and graft experiments rule out a cellular composition of the midline from dorsal mesenchyme or endoderm origin and rule out an inducing role by the notochord. Based on laminin expression pattern and Ntn4 resistance, the authors propose a model, whereby the midline basement membrane is progressively deposited by the descending endoderm.

Laterality defects encompass severe malformations of visceral organs, with a heterogenous spectrum that remains poorly understood, by a lack of knowledge of the different players of left-right asymmetry. This fundamental work significantly advances our understanding of left-right asymmetric organogenesis, by identifying an organ-specific and stage-specific midline barrier. The complexities of basement membrane assembly, maintenance, and function are of importance in several other contexts, as for example in the kidney and brain. Thus, this original work is of broad interest.

Overall, reviewers refer to a strong and elegant paper discovering a novel midline structure, combining classic but challenging techniques, to show the dynamics, chemical, and physical properties of the midline. However, reviewers also indicate that further work will be necessary to conclude on the origin and impact of the midline for asymmetric organogenesis. Three issues have been raised to strengthen the claims:

1) The function of the midline as a physical barrier requires clarification. Dextran injection here seems to label cells and not the extracellular space. By counting the proportion of dextran-labeled cells rather than dextran intensity itself, the authors do not measure diffusion per se, but rather cell mixing.

We agree that an additional means of showing the barrier function is important. We are currently addressing this using a fluorescently tagged derivative of the drug AMD3100 that we recently synthesized, per Poty et al. 2015. We previously showed that AMD3100 perturbs left sided CXCR4-dependent vasculogenesis when introduced on the left side of the dorsal mesentery (DM), but not when introduced on the right (Mahadevan et al. 2014). These data suggest that a midline barrier prevents diffusion of AMD3100 across the DM. We are currently characterizing the extracellular diffusion of this fluorescent derivative through the DM to complement our previous dextran data.

Additionally, we should emphasize that the dextran-injected embryos shown in Fig. 6 D-F were isolated two hours post-injection, a timeframe insufficient for cell migration to occur across the DM (Mahadevan et al., 2014). We also collected additional post-midline stage embryos ten minutes after dextran injections - too short a timeframe for significant cellular migration (Mahadevan et al., 2014). Importantly, the fluorescent signal in those embryos was comparable to that observed in the embryos in Fig. 6. Thus, we believe the movement of fluorescent signal across the DM when the barrier starts to fragment (HH20-HH23) is unlikely to represent cell migration. More than a decade of DNA electroporation experiments of the left vs. right DM by our laboratory and others have never indicated substantial cell migration across the midline (Davis et al., 2008; Kurpios et al., 2008; Welsh et al., 2013; Mahadevan et al., 2014; Arraf et al. 2016; Sivakumar et al., 2018; Arraf et al. 2020; and Sanketi et al., 2022). This is also shown in our current GFP/RFP double electroporation data in Fig. 2 G-H, and DiI/DiO labeling data in Fig. 2 E-G. Collectively, our experiments suggest that the dextran signal we observed at HH20 and HH23 is likely not driven by cell mixing.

2) The descending endoderm zippering model for the formation of the midline lacks direct evidence. The claim of an endoderm origin is based on laminin expression, but the laminin observed in the midline with an antibody may not necessarily correspond to the same subtype assessed by in situ hybridization.

We have attempted to address this important issue by introducing several tagged laminin constructs, LAMB1-GFP, LAMB1-His, and LAMC1-His, to the endoderm via DNA electroporation to try to label the source of the basement membrane. However, despite endogenous laminin production and export within the endoderm, there appeared to be no export of any of the tagged proteins to the endodermal basement membrane. This experiment was further complicated by the necessarily large size of these constructs at 10-11kb due to the size of laminin subunit genes, resulting in low electroporation efficiency. Although we have not yet determined an alternative way to directly test the endodermal origin hypothesis, we are committed to exploring specific methods to help us test this in future experiments.

The midline may be Ntn4 resistant until it is injected in the relevant source cells.

Ntn4 has been shown to disrupt both nascently assembling and preformed mature basement membranes (Reuten et al., 2016). As such, we feel that this particular membrane’s resistance to degradation is likely not predicated by its stage of assembly.

Alternative origins could be considered, from the bilateral dorsal aortae or the paraxial mesoderm, which would explain the double layer as a meeting point of two lateral tissues.

We agree that alternate origins of the midline basement membrane cannot be ruled out from our existing data. We have indeed considered the bilateral dorsal aortae and the paraxial mesoderm as possibilities. However, at the earliest stages of midline basement membrane emergence, the dorsal aortae are already significantly distant from the nascent basement membrane, as are the somites, which have not yet undergone epithelial-to-mesenchymal transition. Fig. S2 G provides an example of a very early midline basement membrane without dorsal aortae or somite contact. Because this particular image is from a section that is fairly posterior in the HH12-13 embryo, it is thus less developed in pseudo-time and gives a window on midline formation in even earlier stage embryos. This is in contrast to the spatially close relationship of the midline basement membrane with the notochord and endoderm. In the context of potential dorsal aortae contributions, it is worth noting that the basement membrane of vascular endothelial cells has a distinct composition from a non-vascular basement membrane. For example, vascular endothelial cells produce only alpha 4 and alpha 5 laminin subunits but contain no alpha 1 subunit in any known species (reviewed in DiRusso et al., 2017). Thus, endothelial cell-derived basement membranes would not contain the alpha 1 laminin subunit that we used in our studies as a robust marker of the midline basement membrane. Note in Fig. 3 E-H and J-J’’’ the absence of dorsal aortae labeling using our laminin alpha 1 antibody. The dorsal aortae are also richer in fibronectin, as seen in Fig. S2, while the midline ECM exhibits far less fibronectin staining. While it may be possible that the converging aortae compress the midline ECM into a more compact structure, we feel direct contribution of basement membrane components is unlikely.

3) The title implies a role of the midline in left-right asymmetric gut development. However, the importance of the midline is currently inferred from previously published data and stage correlations and will require more direct evidence.

We agree that we have not fully and directly demonstrated the extent of the role of the midline in enabling the asymmetry of DM compartments during gut development. We propose the following revised title: “An atypical basement membrane forms a midline barrier during left-right asymmetric gut development”. It is important to note that we have made diligent efforts to investigate the functionality of the midline basement membrane through various methods in which we are highly experienced. However, while targeting either the left or right side of the DM is relatively straightforward, accessing the midline presents substantial challenges. We attempted physical perturbation using in vivo laser ablation, but we observed no significant effect or stable disruption of the midline. Additionally, our attempts at ablation using diphtheria toxin proved to be too harsh on the endoderm, preventing reliable and consistent data interpretation. We have tried electroporating MMP9 and MMP2 into the DM, but these did not produce any appreciable effect on the midline. We are also concerned that directly injecting MMPs or other enzymes may lead to injection-related tissue damage to the embryo that may be difficult to separate from direct MMP digestion of the matrix. However, we firmly believe that our inference regarding the involvement of the midline ECM in the asymmetry of DM compartments is robust, based on the functionally distinct yet closely positioned cell populations of the DM, and the timing of the midline in relation to the establishment of these asymmetric compartments. Notably, recent research conducted in our laboratory has highlighted the vital necessity of maintaining the separation of diffusible signaling molecules, such as Bmp4, from these neighboring cell populations, which would otherwise be in direct contact if not for the presence of the midline basement membrane (Sanketi et al., 2022). We will continue developing specific methods to perturb the midline in preparation of a revised manuscript.

Author Response

The following is the authors’ response to the previous reviews

We thank the Reviewers and Editors for the evaluation of our revised manuscript.

We especially value the careful assessment of Reviewer 1; at the same time, we clearly disagree with the reviewer’s statement that the revised manuscript “is essentially unchanged”. As appreciated by the other Reviewers, we performed a key experiment (in our opinion the only conclusive experiment) to further solidify that FK506-treatment kills parasites in a FK506-independent manner. Of note, however, Reviewer 1 made us aware of an error in the legend of Figure 4F, which likely contributed to the confusion regarding the antiplasmodial effect of FK506: Unfortunately, we missed updating this legend to appropriately imbed the new experiment. We therefore incorrectly stated that parasites were exposed to FK506 for 48 hours after FK506 treatment at 4-10 hpi and 36-42 hpi in G1. In contrast to the experiments described in the initial submission, parasite survival was not measured 48 h later, but in G2 ring stage parasites, i.e. at a time point during which parasitemia is not affected by the knockout of PfFKBP35. We have now corrected this. As pointed out correctly by Reviewer 1, it would otherwise not be possible to disentangle the effects of the gene knockout and the drug. The setup we now present in Figure 4F, however, is clearly able to do so.

We apologize for the inaccuracy and hope this resolves the ambiguities regarding the FKBP35-independent antimalarial effect of FK506. In line with the comments of Reviewers 2 and 3, we believe that our findings on FK506 activity are of particular importance for the malaria research community. We therefore hope that the final eLife assessment will reflect this.

Author Response

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

On behalf of my co-authors, we thank you very much for giving us the opportunity to revise our manuscript entitled “A positive feedback loop between ZEB2 and ACSL4 regulates lipid metabolism to promote breast cancer metastasis” (manuscript number: eLife-RP-RA-2023-87510).

We would like to convey our appreciation to you and the expert reviewers for your valuable time and effort in reviewing and improving our work. We are grateful for the constructive comments raised by the six expert reviewers. We have studied the reviewer’s comments carefully and have accordingly conducted additional experiments as recommended. We have made the following revisions point by point. We found that our work was substantially strengthened by addressing these points.

Reviewer #1 (Public Review):

In this study, Jiamin Lin et al. investigated the potential positive feedback loop between ZEB2 and ACSL4, which regulates lipid metabolism and breast cancer metastasis. They reported a correlation between high expression of ZEB2 and ACSL4 and poor survival of breast cancer patients, and showed that depletion of ZEB2 or ACSL4 significantly reduced lipid droplets abundance and cell migration in vitro. The authors also claimed that ZEB2 activated ACSL4 expression by directly binding to its promoter, while ACSL4 in turn stabilized ZEB2 by blocking its ubiquitination. While the topic is interesting, there are several major concerns with the study and its conclusions are not convincing.

1) Figure 1A, the clinical relevance or biological significance of drug-resistant luminal breast cancer cell lines with metastatic cancer is questionable. Additionally, the RNA-seq analysis lacked multiple test correction for differential gene expression analysis, and no fold-change cut-off was used, leading to incorrect thresholds and wrongly identified significant signals.

We appreciate the reviewer’s valuable questions to improve our manuscript. We identified many EMT related transcription factors such as ZEB2, SNAIL, TWIST, etc. was up-regulated in drug-resistant cells, so we hypothesized that drug-resistant cells may undergone EMT and acquire metastatic capability. The drug-resistant cells used in this study had already been proved and examined in the previous studies of our research team as follows:

(1) Zheng FM, Long ZJ, Hou ZJ et al., A novel small molecule aurora kinase inhibitor attenuates breast tumor-initiating cells and overcomes drug resistance. Mol Cancer Ther. 2014 Aug;13(8):1991-2003.

(2) Yang N, Wang C, Wang Z, et al., FOXM1 recruits nuclear Aurora kinase A to participate in a positive feedback loop essential for the self-renewal of breast cancer stem cells. Oncogene. 2017 Jun 15;36(24):3428-3440.

For the second question, we used the fold-change cut-off in RNA-seq analysis and the fold change was over 1.5-fold and the adjust P value is less than 0.05. To make it more clearly, we have reset the cut off with a |log2FC|2 and p<0.05 and generated the volcano Plot using R4.3.0 software for differentially expressed genes as follows in Author response image 1. The results showed 3217 and 3035 up-regulated genes in TAXOL-resistant and EPI-resistant cells respectively, along with 2427 (TAXOL) and 2901 (EPI) down-regulated genes. Both ACSL4 and ZEB2 were up-regulated in two cell lines. We have put the figure in the new supplementary Fig S2.

Author response image 1.

2) Figure 1D-E, the clinical associations between ACSL4 and ZEB2 overexpression and poor patient survival are not justified. The authors used an old web tool, the Kaplan-Meier plotter database, based on microarray data, to perform the analysis. The reviewer repeated the analysis and found that multiple microarray probes for ZEB2 were available, leading to opposite results when different probes were selected. The reviewer also repeated the analysis using more reliable TCGA RNA-seq data and found no correlation between ASCL4 or ZEB2 expression and post-progression survival.

We appreciate the reviewer’s thoughtful questions. The Kaplan-Meier plotter database (http://kmplot.com/analysis/) we used is handled by a PostgreSQL server, which integrates gene expression and clinical data simultaneously including GEO, EGA and TCGA data. We used auto-select best cutoff for the the Kaplan-Meier analysis. Due to the web tool is old, we repeated the Kaplan-Meier survival analysis using R4.3.0 software and split the patients in TCGA database according to the third quartile expression (new Fig. 1D-F). The results also show that patients with high expression of ACSL4 and/or ZEB2 have relatively worse prognosis as follows in Author response image 2 (p<0.01):

Author response image 2.

3) Figure 1I relied on IHC to support the negative correlation between ACSL4 and Erα expression, but the small sample size limits the power to establish the relationship and the results are not definitive without further replication or biological investigation. The authors should provide more detailed and comprehensive analysis, including appropriate statistical tests, to ensure the findings are robust and reliable.

We appreciate the reviewer’s suggestion. To better understand the positive correlation between ACSL4 and ZEB2 expression, we add up to 45 breast cancer cases for IHC analysis and the correlation is shown as follows in Author response image 3 (new Fig. 1 H):

Author response image 3.

4) Figure 3B-C lacks justification of the differences by showing only one field without any internal control for exposure. The reviewer suggests to show additional fields where cells with both efficiently and inefficiently knocked-down are present, to justify the robustness of the results. This can also be achieved by mixing control and knockdown cells.

We totally understand the reviewer's concern. Thank you for pointing out this problem. The lower magnification field of view is shown as follows and it includes both efficiently and inefficiently knocked-down cells. We have changed the Fig. 3B and C as follows in Author response image 4:

Author response image 4.

5) Figure 4A-D, oleate-induced cell migration is a well-documented feature across different cancer types. To make it more relevant to the current study, the authors should examine multiple cell lines with high and low ZEB2/ACSL4 expression to determine the underlying relevance.

We appreciate the reviewer’s comments and performed the suggested experiments. To better determine the role of oleic acid and ACSL4 on cell migration, we use MCF-7 cell line, which has low ZEB2/ACSL4 expression, to test the influence of oleate on the cell migration. Transwell and Wound healing assays revealed that oleic acid treated MCF-7 cells also exhibited enhanced invasive and metastatic capacities compared with control cells. This results indicates that oleate induces cell migration in MCF-7 cells may via mechanisms other than ACSL4. We have added the results to the new Supplementary Fig. 8 as follows in Author response image 5.

Author response image 5.

6) Figure 4E, it is difficulty to conclude that cancer cells utilize stored lipids during migration to fuel metastasis based on current data. Do you see any evidence of lipid signal decreasing in the leading edge of the scratch wound-healing migration assay? The authors should also compare signals between unmigrated and migrated cells in the transwell assay.

We appreciate the reviewer’s constructive suggestion. We performed the wound-healing migration assay and observed that the lipid signal was obviously decreased in the leading edge of the scratch, as shown in the Author response image 6 (New Fig. 4E). In the transwell experiment, the cells which migrated to the lower side of the chamber after 24 hours showed decreased lipid signals (Fig. 4F). All these results indicates that lipid is utilized during migration.

Author response image 6.

7) Figure 6 warrants a genome-wide ChIP-seq to justify direct regulation of ASCL4 promoter by ZEB2. The reviewer’s analysis of publicly available ZEB2 ChIP-seq in multiple cell types detected no ZEB2 binding signaling within {plus minus} 5 kb of ASCL4 promoter.

We thank the reviewer for the concern. We found that the breast cancer cells are not included in some data base, such as Cistrome Data Browser, which is a resource of human and mouse cis-regulatory information derived from ChIP-seq, DNase-seq and ATAC-seq chromatin profiling assays. Due to that different cell type may have totally different mechanisms, that’s why the ZEB2 binding signaling cannot be found within ASCL4 promoter in some cells.

We searched JASPAR data base (https://jaspar.genereg.net/), which is an open-access database of non-redundant transcription factor (TF) binding profiles, and found the consensus binding sequences (CACCT) of ZEB (zinc finger E-box binding homeobox) transcription family were within the 2kb of ASCL4 promoter as follows in Author response image 7.

Author response image 7.

8) Figure 7 presents a series of self-contradictory results. Figure 7C, why no significant change in ZEB2-MYC expression was observed in the presence of ACSL4 and/or HA-Ubi? In Figure 7 E&G, why robust ACSL4 expression is present in the control group in E but not in (G)? Additionally, why there is no degradation in ZEB2 baseline level over time in the shACSL4 group in E? These raise severe concerns about the data quality.

We appreciate the reviewer to point out these problems.

Response to question 1: In fig. 7C, we used 293T cell for the ubiquitin assay and it is not a breast cancer cells. The efficiency of over-expression is different between ZEB2 and ACSL4 in 293T cell lines.

Response to question 2: Because the expression of ACSL4 is low in MCF-7 and is high in MDA-MB-231 cells. In Figure 7E (New Fig. 7G), we used MDA-MB-231 cells for the control and ACSL4 knockdown cells. In Figure 7G (New Fig. 7I), we used MCF-7 cells for the control and ACSL4 over-expressed cells. We have also revised the figure legend of Fig.7 as follows:

I, The stability of ZEB2 protein was detected by CHX treatment assay in control or ACSL4 over-expressed MCF-7 cells. GAPDH was used as the internal loading control.

Response to question 3: Because knockdown of ACSL4 also significantly decreased the mRNA level of ZEB2 (New Fig. 7A), so the baseline levels of ZEB2 in the shACSL4 group (New Fig. 7G) were very low and degradation is not obvious.

9) Figure 7D, the IP result of ACSL4 is not justified as there is no enrichment of ACSL4 in the IP compared to input. With the current data, it is hard to justify that there is any direct interaction. Moreover, based on IF data in Figure 3B-C, ACSL4 is exclusively localized in the cytoplasm, while ZEB2 is exclusively localized in the nucleus. It is hard to believe there is any direct interaction and mutual regulation.

We appreciate the reviewer’s thoughtful questions. We have repeated the IP assay and found that the enrichment of ACSL4 was observed in the IP process and added to new Fig. 7E as follows in Author response image 8. We also repeated the immunofluorescence assay in the MDA-MB-231 cells. We observed that ZEB2 can also be found in the cytoplasm and co-localized with ACSL in some certain regions of the cytoplasm as follows in Author response image 9 (Supplementary Fig. S11):

Author response image 8.

Author response image 9.

Reviewer #2 (Public Review):

In this study, the authors validated a positive feedback loop between ZEB2 and ACSL4 in breast cancer, which regulates lipid metabolism to promote metastasis.

Overall, the study is original, well structured, and easy to read. Despite the reliability of the data discussed in this article, there are still some deficiencies that need to be addressed through further explanation.

Major issues:

1) The authors demonstrated that ACSL4 regulates ZEB2 not only via a post-transcriptional mechanism but also via a transcriptional mechanism. The authors have not provided a comprehensive explanation of the specific mechanism in this paper. Therefore, it is recommended that the author delve into the potential mechanisms in the discussion section. For example, related mechanisms affecting ZEB2 ubiquitination degradation, as well as factors affecting ZEB2 upstream transcriptional regulation, etc.

We appreciate the positive comments and constructive suggestion from the reviewer. We have added the following paragraph in the second paragraph of the discussion section :

Interestingly, our RNA-seq data revealed that some ubiquitin E3 ligases, such as FBXO4, UBE3C, NEDD4, RBX1 etc. were significantly reduced in ACSL4 knockdown cells (Fig. S12). This result indicated that ACSL4 may reduce the ubiquitin of ZEB2 via down-regulating ubiquitin E3 ligase. Additionally, we found that ACSL4 promoted ZEB transcription as the mRNA level of ZEB2 was significantly reduced after ACSL4 knockdown. A recent study reported that LD-derived lipolysis provide acetyl-CoA for the epigenetic regulation of gene transcription. We observed that ACSL4 can also promote FAO, which generates acetyl-CoA for the epigenetic regulation. It is likely that ACSL4 regulates the ZEB2 mRNA level via lipid-epigenetic reprogramming mechanism, which is worth studying in the future.

2) To further clarify the interaction of ZEB2 and ACSL4, it is best to perform in vitro glutathione-S-transferase (GST) pulldown assay and immunofluorescence assay.

We appreciate the reviewer’s suggestion. We performed GST pull-down assay to examine whether ZEB2 and ACSL4 form a complex. GST pull-down assay confirmed the interaction of ZEB2 and ACSL4 as follows in Author response image 10 (Supplementary Fig. S10). We also performed immunofluorescence assay and found that ZEB2 was co-localized with ACSL in some certain regions of the cytoplasm as follows in Author response image 11. (Supplementary Fig. S11):

Author response image 10.

Author response image 11.

3) In Figure 7B, the protein level of ZEB2 seems not to be altered in BT549 BCSC cell line after the depletion of ACSL4.

We appreciate the reviewer to point out this problem. The protein level of ZEB2 in BT549 BCSC cell is not abundant as MDA-MB-231. We repeated the experiment and found that ZEB2 was reduced after the depletion of ACSL4 in BT549. We have replaced the Fig.7B as follows in Author response image 12:

Author response image 12.

4) EMT is characterized by changes in cell morphology, so the staining of cytoskeletons with Phalloidin is needed.

We appreciate the reviewer’s suggestion and performed the staining. The results show that the ACSL4 knockdown cells had a significantly smaller length to width ratio, which indicates the reversion of EMT process, than those of the control group (p<0.05). We have put the results in Supplementary Fig. S4 as follows in Author response image 13:

Author response image 13.

5) Additional breast cancer cases or cohorts (such as TMA) should be used to validate the positive correlation between ACSL4 and ZEB2 expression through IHC analysis.

We thank the reviewer for the suggestion. To better understand the positive correlation between ACSL4 and ZEB2 expression, we added more breast cancer cases up to 45 for IHC analysis and validated the positive correlation between ACSL4 and ZEB2. We have put the results into Fig 1 H and I as follows in Author response image 14:

Author response image 14.

Reviewer #3 (Public Review):

The manuscript by Lin et al. reveals a novel positive regulatory loop between ZEB2 and ACSL4, which promotes lipid droplets storage to meet the energy needs of breast cancer metastasis. It is of interest, however, some concerns should be addressed to strengthen the finding.

Major concerns:

1) The effect of ZEB2 overexpression is not fully demonstrated in the whole study. This point should be addressed.

We appreciate the positive comments and constructive suggestion from the reviewer. We have performed ZEB2 over-expressed MCF7 cell line. Over-expression of ZEB2 significantly enhanced the metastatic and invasive capacities of MCF7 cells. (Supplementary Fig. S5A and 5B).

Author response image 15.

1. Does the addition of oleate restore the ability of migration or invasion in ACSL4 knockdown cells?

We thank the reviewer for the question. To address this point, the oleate was added in the culture medium of ACSL4 knockdown cells. As expected, the addition of oleate obviously restores the invasive and metastatic capacities of ACSL4 knockdown cells by 33.12% and 18.61% respectively. We have added the results in the new Fig. 4D as follows in Author response image 16:

Author response image 16.

3) Which cellular compartment does ACSL4 localize in and interact with ZEB2 to stabilize ZEB2?

We thank the reviewer for the question. We have repeated the immunofluorescence assay in the MDA-MB-231 cells. We observed that ZEB2 can also be found in the cytoplasm and co-localized with ACSL in some certain regions of the cytoplasm (Supplementary Fig. S11):

4) The ubiquitination assay and Co-IP assay are just performed in HEK293T cells. This result should be confirmed in MDA-MB-231 cells or Taxol-resistant MCF-7 cells.

We appreciate the reviewer’s suggestion. We performed the ubiquitination assay and IP assay in MDA-MB-231 cells as follows. The results confirm that knockdown of ACSL4 obviously enhanced the ubiqutination of ZEB2. We have put the results into Fig. 7D and 7F as follows in Author response image 17:

Author response image 17.

5) How does ACSL4 regulate ZEB2 at the mRNA level？Please verify.

We thank the reviewer for the thoughtful question. A recent study reported that LD-derived lipolysis provide acetyl-CoA for the epigenetic regulation of gene transcription. We observed that ACSL4 can promote FAO, which generates acetyl-CoA for the epigenetic regulation. It is likely that ACSL4 regulates the ZEB2 mRNA level via lipid-epigenetic reprogramming mechanism, which is worth studying in the future and we had added the following sentences into the second paragraph in the discussion section :

Additionally, we found that ACSL4 promoted ZEB2 transcription as the mRNA level of ZEB2 was significantly reduced after ACSL4 knockdown. A recent study reported that LD-derived lipolysis provide acetyl-CoA for the epigenetic regulation of gene transcription. We observed that ACSL4 can also promote FAO, which can generate acetyl-CoA for the epigenetic regulation. It is likely that ACSL4 regulates the ZEB2 mRNA level via lipid-epigenetic reprogramming mechanism, which is worth studying in the future.

6) In Fig. 2F, the silencing efficiency for ACSL4 and ZEB2 should be shown. In addition, the protein level of ZEB2 or ACSL4 in shZEB2 and shZEB2+ACSL4 groups should also be addressed.

We appreciate the reviewer's suggestions. We have added the protein levels in Fig 2F and 2H as follows in Author response image 18:

Author response image 18.

7) What is the survival status of patients with both high expression of ACSL4 and ZEB2 in TCGA. In addition, more survival data from databases especially patients with both high expression of ACSL4 and ZEB2 are needed to analyze to support the finding.

We thank the reviewer for the constructive suggestion. We repeated the Kaplan-Meier survival analysis of TCGA RNA-seq data by using R4.3.0 software. The survival data show that the patients with both high expression of ACSL4 and ZEB2 have the worst prognosis in the four groups (P<0.05) ( New Fig. 1D-F).

Reviewer #1 (Recommendations For The Authors):

10) Only one siRNA/shRNA was used for knockdown in one cell line. Different siRNAs/shRNAs and multiple cell lines should be used to rule out off-target effects.

We appreciate the reviewer’s suggestion. We have test three siRNA and shRNA for the knockdown efficiency (negative control siRNA or ACSL4 and ZEB2 siRNA were from the company of GenePharma), we chose one sequence with the best knock-down effect.

Author response image 19.

11) Western blot data are required to justify the overexpression or knockdown efficiency of ACSL4 in cells in Figure 2 A-C.

We thank the reviewer for the suggestion. we have added the following western blot data in Figure 2:

Author response image 20.

12) In Figure 1G, there is a huge variation of the protein input, which makes the results not justified. The authors should repeat the experiments to ensure consistency and reproducibility of the results.

We appreciate the reviewer to point out this problem. Because this is the tissue samples of breast cancer patients. The results are affected by the tumor tissue composition between different patient sample, and it is difficult to obtain fresh tissues. In our paper, paraffin specimens have been used for IHC staining, and the results confirmed that ACSL4 and ZEB2 are positively correlated. We have put the results in the supplementary data.

Reviewer #2 (Recommendations For The Authors):

1) Data from Figure 1A showed the EMT transcription factor SNAIL was also among the top upregulated genes. Please explain why the association between ACSL4 and ZEB2 was studied instead of ACSL4 and SNAIL.

We appreciate the reviewer’s question. We had calculated the correlation between the ACSL4 and SNAIL by Pearson’s correlation test. The correlation of ACSL4 and SNAIL is 0.33, less than that of ZEB2. Bedsides, the binding motif analysis reveals that the consensus sequence of ZEB transcription family is within the ACSL4 promoter. Thus, we investigated the relationship between ACSL4 and ZEB2 in breast cancer cells.

Author response image 21

2) What is the limitation of your study? Please add some relevant description in the part of discussion.

We appreciate the reviewer’s suggestion. We have added the description of limitation of our study in the last paragraph of discussion section as follows:

The limitation of this study is the clinical samples is only 45. The future study should expand the clinical samples and cases to provide more clinical evidence for the crucial role of ACSL4 in breast cancer metastasis.

3). In Figure 3 Figure Legends part, the authors used the word "knockout", which is a description error.

We appreciate the reviewer’s advice. We have corrected "knockout" into "knockdown".

Reviewer #3 (Recommendations For The Authors):

Minor concerns:

1) In line 352-353, the statement about whether the high or low expression of ACSL4 and ZEB2 or the advanced breast cancer affects prognosis is inaccurate.

We appreciate the reviewer to point out this problem. We have corrected the statement into “We found that patients with higher ACSL4 or ZEB2 expression, especially those with simultaneous high expression had worse prognosis than those with lower expression ”.

2) The title of the seventh part of your results contains a logical error that is opposite to the experimental conclusion.

We truly appreciate the reviewer to point out this problem. We have changed the title of the seventh part of results to “ACSL4 regulates ZEB2 mRNA expression and protein stabilization”.

Author Response

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

Reviewer #1

1) Overall, this is a useful tool, the data is well-presented, and the paper is well-written. However, the predictions are only compared with two existing reconstruction tools though more have been recently published

The aim of this work was to facilitate high-throughput generation of strain-specific metabolic models e.g. at the scale of 100s -1000s as indicated throughput the introduction (see lines 74-82, 91-94), and therefore we only compared tools which were capable of high-throughput analysis via command line and excluded others (e.g. merlin). We have now tested this against the other recent command line tool, gapseq which had escaped our gaze. Thank you for bringing this to our attention. Additionally, we have included KBase (ModelSEED, a web-based app that does not support high-throughput analysis) to allow for readers to interpret the results in the context of community standard approaches, since KBase is a popular tool.

We have added an explicit statement about the choice of approaches, now at lines 194-199 as follows:

“We compared the output and performance of Bactabolize to the two previously published tools that can support high-throughput analyses i.e. CarveMe (30) and gapseq (31). To aid interpretation in the context of community standard approaches, we also include a comparison to the popular web-based reconstruction tool, KBase (ModelSEED), and a manually curated metabolic reconstruction of K. pneumoniae strain KPPR1 (also known as VK055 and ATCC 43816, metabolic model named iKp1289) (15).”

The methods section was updated accordingly (now lines 552-558):

“A draft model was generated using gapseq version 1.2 with the ‘doall’ command using the unannotated genome (as gapseq does not take annotated input files). Gap-filling was subsequently performed using the ‘fill’ command and a custom M9 media file to match the nutrient list found in Bactabolize (https://github.com/kelwyres/Bactabolize/blob/main/data/media_definitions/m9 _media.json).

Finally, a draft model was constructed using the annotated genbank K. pneumoniae KPPR1 file and the KBase narrative (15) (https://narrative.kbase.us/narrative/ws.14145.obj.1).”

The results section (now lines 193-308) and Figure 2 have also been updated / restructured to reflect the new analyses, and include a comparison of the relative compute times for the construction of models (lines 281-291) as follows:

“While model features and accuracy are essential metrics for comparison, computation time is also a key consideration for high-throughput analyses. We recorded the time required for each tool to build draft models for 10 of the completed KpSC genomes used in the quality control framework (see below) on a high-performance computing cluster (Intel Xeon Gold 6150 CPU @ 2.70GHz and 155 GB of requested memory on a CentOS Linux release 7.9.2009 environment. CarveMe KpSC pan was the fastest with a mean of 20.04 (range 19.90 - 20.18) seconds, followed by CarveMe universal at 30.28 (range 29.20 - 31.80) seconds, then Bactabolize KpSC pan at 98.05 (range 92.19 - 100.4) seconds. KBase took 183.50 (range 120.00 - 338.00) seconds per genome via batch analysis, including genome upload time and queuing. gapseq took 5.46 (range 4.55 - 6.28) hours to produce draft models (not including the required gap-filling), consistent with previous reports (37).”

Finally, the whole discussion has been updated and substantially restructured (lines 472-474, 475-493, 494-512). Specific mentions to the new analyses are at lines:

472-474: “Consistent with this assertion, our draft KPPR1 model constructed with KBase (without manual curation) was an outlier in terms of the very low number of genes, reactions and metabolites that were included.”

475-493: “CarveMe with universal model (30) and gapseq (31) are the current gold standard automated approaches for model reconstruction, and we show that a draft KpSC model generated by Bactabolize with the KpSC pan v1 reference resulted in similar or better accuracy for phenotype prediction (Figure 2). Both the CarveMe universal and gapseq models resulted in high numbers of true-positive and true-negative growth predictions. However, these were also accompanied by comparatively higher numbers of false-positive predictions that resulted in a lower overall accuracy for substrate usage analysis compared to Bactabolize with the KpSC-pan v1 reference (Figure 2), and comparatively lower precision and specificity for the gene essentiality analysis. False-positive predictions may indicate that the relevant metabolic machinery are present in the cell but were not active during the growth experiments (e.g. due to lack of gene expression). In this regard, false-positives are not always a sign of model inaccuracy. However, false-positive predictions can also occur from incorrect gene annotations e.g. due to reduced specificity of ortholog assignment resulting from the use of the universal model without manual curation. Given a key objective here is to facilitate high-throughput analysis for large numbers of genomes, it is not feasible to expect that all models will be manually curated, and therefore we believe that identifying fewer genes with lower overall error rates provides greater confidence in the resulting draft models. We also note that the BiGG universal reference model which CarveMe leverages is no longer being actively maintained. In contrast, user defined reference models can be iteratively curated and updated to incorporate new knowledge and data as they become available.”

510-512: “However, gapseq’s long compute time makes it inappropriate for application to datasets comprising 100s-1000s of genomes (such as have become increasingly common in the bacterial population biology literature).”

2) My understanding is that the tool requires a set of reference reconstructions for other strains of the target species. If no reference reconstruction is available for another strain of the target species, can this species not be reconstructed?

Any input reference can be used to generate models however, single strain models matching the target species, or ideally a species-specific panreference, are recommended for best results. We have added a discussion on these points at lines 128-133:

“For optimum results we suggest using a pan-model that captures as much diversity as possible for the target species or group of interest, because Bactabolize’s reconstruction method is reductive i.e. each output strainspecific model will include only genes, reactions and metabolites that are present in the reference or a subset thereof (although novel genes, reactions and metabolites can be added via manual curation).”

We expand on these points further in the discussion:

494-512: “Bactabolize’s reference-based reconstruction approach is reductive, meaning the resultant draft models will comprise only the genes, reactions and metabolites present in the reference, or a subset thereof, and will not include novel reactions unless they are manually identified and curated by the user. This is an important caveat that should be considered carefully for application of Bactabolize to large genome data sets, particularly for genetically diverse organisms such as those in the KpSC. For optimum results we suggest using a curated pan-model that captures as much diversity as possible for the target species or group of interest. While we acknowledge that a reasonable resource investment is required to generate a high-quality reference, we have shown that a pan-model derived from just 37 representative strains can be sufficient to support the generation of highlyaccurate draft models (Figure 2 and 5). Additionally, we note that it is possible to use a single strain reference model, which should ideally represent the same or closely related species to that of the input genome assemblies, in order to facilitate accurate identification of gene orthologs. It is technically possible to use an unrelated reference model, but this is expected to result in inaccurate and/or incomplete outputs and has not been tested in this study. In circumstances were no high quality closely-related reference model is available, we recommend alternative reconstruction approaches that leverage universal databases e.g. CarveMe (30) or gapseq (31). However, gapseq’s long compute time makes it inappropriate for application to datasets comprising 100s-1000s of genomes (such as have become increasingly common in the bacterial population biology literature).”

3) How do the reconstructions generated by Bactabolize compare to those generated by other reconstruction tools besides CarveMe and ModelSEED, e.g., gapseq (Zimmermann et al, Genome Biology 2021. 22:81) or merlin (Capela et al, Nucleic Acids Res 2022, 50(11):6052-6066?

See response to rev 1 point 1.

4) How are the accuracy, specificity, and sensitivity of the pan-models calculated? Is the compared experimental data on the species level?

We used the pan-model as a reference from which we generated a strain-specific model for K. pneumoniae KPPR1 (using Bactabolize and CarveMe). This strain-specific metabolic model was then used to simulate growth phenotypes and compared to published experimental data for KPPR1. This was described in the methods section, including the calculations for the metrics (lines 589-593); however, we have also expanded the description within the results section to clarify the approach (lines 201-209):

“De novo draft models for strain KPPR1 were built using; i) Bactabolize with the KpSC pan v1 reference; ii) CarveMe, with its universal reference model (CarveMe universal); iii) CarveMe, with KpSC-pan v1 reference (CarveMe KpSC pan); iv) gapseq; and v) KBase (ModelSEED). ….. Subsequently, each model was used to predict growth phenotypes; i) in M9 minimal media with different sole sources of carbon, nitrogen, phosphorus and sulfur; and ii) for all possible single gene knockouts in LB under aerobic conditions. The predicted phenotypes were compared directly to the published phenotype data.” [Note the published data are cited in the previous manuscript sentence, not shown here].

5) The link https://github.com/rrwick/GFA-dead-end-counter, in line 286 does not work.

Link regenerated – now at line 451-452 and 604

Reviewer #2

1) KpSC pan-metabolic reference model is provided. Are they required as input for Bactabolize? Are the gene, metabolite information open accessible by users? o See response to reviewer 1 point 2 above and;

All data for the KpSC pan-model described in this work are accessible in the model files and amino acid + nucleotide files + data table at https://github.com/kelwyres/KpSC-pan-metabolic-model. This is also linked in the manuscript at line 631 and in the Data availability statement at line 661.

2) In the results section "description of Bactabolize", the authors present technical details on how to generate a metabolic model. For the input and output, please provide concrete examples to show the functionality of Bactabolize.

Detailed instructions, example code and example input/output files are available via the Bactabolize GitHub repository: https://github.com/kelwyres/Bactabolize.<br /> Instructions and example code can be found on the wiki: https://github.com/kelwyres/Bactabolize/wiki Test data and example files are at: https://github.com/kelwyres/Bactabolize/tree/main/data/test_data

The Github repository is linked in the manuscript at lines 95, 124, 552, and 667, and we have added a further reference at line 124, which mentions the example code/data: “Full documentation, including example code and test data are available at the Bactabolize code repository (https://github.com/kelwyres/Bactabolize).”

3) To generate metabolic models, the authors present comparison results with other methods. However, the authors only present the numbers in genes, metabolites and substrates. Since the interactions between gene, metabolite, and substrate are also critical, if possible, please provide the coverage details about these interactions. Venn diagram is recommended to compare these coverage differences.

Two additional supplementary figures have been generated (Figures S5 and 6) showing Venn diagrams of metabolites and reactions for the highthroughput analysis approaches that are most relevant to this work (see also response to rev 1, point 1). These are discussed at lines 224-237:

“Figures S5 and S6 show the overlaps of metabolites and reactions between the high-throughput reconstruction methods after processing with MetaNetX (59) to standardise the reaction and metabolite nomenclatures (excluding CarveMe pan for simplicity and given the likely problems of reaction oversubscription). The majority of the reactions included in the Bactabolize model were conserved in either the CarveMe universal model (n = 1225, 53.2%), gapseq model (n = 54, 2.3%) or both (n = 665, 28.9%). The reaction overlap was skewed to the CarveMe universal model which shared 1225 reactions that were conserved in the Bactabolize model but absent from the gapseq model. Notably, the gapseq model contained a large number (2200) of unique reactions (70.4% of those in the model). Similarly, the vast majority of metabolites in the Bactabolize model were conserved in one or both of the other models (n = 917, 85.6%). However, it is likely that true overlaps between methods are underrepresented due to the different reaction identifiers and chemical synonyms used within the BiGG (Bactabolize, CarveMe) vs ModelSEED nomenclatures (gapseq), which are difficult to harmonise in an automated manner even after the application of MetaNetX.”

Figure 2 shows not only the model numbers but also includes benchmarking to real phenotypic data in 2DEFG as the key mode of comparison between models. This encompasses meaningful interactions between gene, metabolic and substrate. The results are discussed at length in text at lines 253-271:

“We assessed the performance of each model for in silico prediction of growth phenotypes compared to the previously published experimental data (15). Accuracy, sensitivity, specificity, precision and F1 scores were calculated (60). Note that the specific set of growth substrates and gene knockouts that can be simulated is determined by the sets of genes and metabolites captured by each model and is therefore model-dependent (Data S1 and S2). Among those with matched experimental phenotype data, the Bactabolize and CarveMe universal models were able to predict growth for a greater number of carbon, nitrogen, phosphorous and sulfur substrates than gapseq, CarveMe KpSC pan, KBase and iKp1289 models (Figure 2C, Data S1). While the CarveMe universal model had the highest number of truepositive growth predictions overall (n = 132 of 617 total predictions), it also had a comparably high number of false-positive predictions (n = 39 of 617 total predictions, Figure 2D). Similarly, the gapseq and iKp1289 models resulted in 31 (262 total predictions) and 50 (513 total predictions) falsepositive predictions, respectively. In contrast, the Bactabolize model had fewer false-positive predictions (n = 21 of 505 total predictions) alongside a high number of true-positive predictions (n = 117 of 505 total predictions), resulting in the highest overall accuracy metrics (Figure 2E, Data S1). The KBase model was a notable outlier, associated with a high number of falsenegative predictions (n = 31 of 103 total predictions) and low false-positive predictions (n = 3 of 103 total predictions), presumably resulting from the very low number of genes and reactions included in the model, driving low sensitivity and accuracy.”

Lines 272-280:

“The gene essentiality results showed that gapseq produced the highest absolute number of true-positive gene essentiality predictions (n = 79 of), followed by Bactabolize KpSC pan (n = 44 of 1220 total predictions), then CarveMe universal (n = 39 of 1951 total predictions). CarveMe universal had the largest number of true-negatives by a wide margin (n = 1599 of 1951 total predictions), followed by gapseq (n = 1085 of 1403 total predictions), then Bactabolize KpSC pan (n = 939 of 1220 total predictions), driving their high accuracies (83.96%, 82.96% and 80.57%, respectively). The Bactabolize model was associated with the greatest overall precision and specificity (Figures 2F & 2G) while the gapseq model resulted in the highest F1-score and sensitivity.”

4) Are quality control and gap-filling needed to be processed when constructing a new metabolic model?

Our goal here was to implement an approach to support high-throughput analyses (see response to rev 1 point 1), including leveraging draft genome assemblies as the bases for the construction of strain-specific metabolic models. As part of this work, we have described a robust quality control (QC) framework for screening draft K. pneumoniae genomes i.e. to identify genome assemblies that should not be used. We developed this framework by comparison to models generated for matched completed genomes. Our analyses demonstrate the importance of applying QC to the input draft genome assemblies. When appropriate QC is applied to the input genomes, the resultant draft models show a high degree of completeness compared to the matched models derived from complete genomes. The draft models can also be used to simulate growth phenotypes with high accuracy as compared to those simulated for the matched complete genome models.

No specific QC was applied to the draft models themselves, other than confirmation of positive growth prediction in m9 minimal media plus glucose (which is expected to support growth of all K. pneumoniae). In cases where the input assembly passed our QC criteria but the resultant model was unable to simulate growth in m9 minimal media plus glucose, gap-filling may be optionally applied. Again, by comparison to the simulated phenotypes from matched complete genome models, we show that these gap-filled draft models can produce accurate phenotype predictions. See lines 396-404:

“Of the 901 draft genome assemblies which passed our QC criteria (≤200 assembly graph dead ends), 23 of the resulting draft models failed to simulate growth in M9 minimal media with glucose (despite capturing ≥99% of the genes and reactions in the corresponding complete models). It is expected that all KpSC models should be able to simulate growth on M9 media with glucose as a sole carbon source, as this central metabolism is universal amongst KpSC. To replace missing, critical reactions required for growth on M9 with glucose, we investigated model gap-filling using the patch_model command of Bactabolize. We then assessed the accuracy of the gap-filled models for prediction of growth on the full range of substrates, as compared to the predictions from the corresponding complete models.” Lines 409-413: “Substrate usage predictions from the 21 successfully gap-filled models were highly accurate, with 18/21 having a prediction concordance of ≥99% across all 846 growth conditions (12/21 had 100% concordance) (Figure S9). We therefore conclude that models generated for genome assemblies passing our QC criteria, which have been gap-filled to successfully simulate growth on minimal media plus glucose, are suitable for the prediction of growth across a range of substrates.”

5) Are there any visualization results to check the status of the generated draft model?

No. This is a tool for large-scale and rapid production of metabolic models, and phenotype prediction and we have not included visualisation tools. Third party tools are available e.g. https://fluxer.umbc.edu/. We do provide optional generation of MEMOTE reports at lines 136-138:

“Draft genome-scale metabolic models are output in both SMBL v3.1 (41) and JSON formats (one pair of files for each independent strain-specific model), along with an optional MEMOTE quality report (42)”.

Reviewer #3

1) The justification and evaluation of the generated models are inadequate and onedimensional. The authors only focus on statistics such as the number of reactions and genes in the models, which does not accurately depict the completeness of the model.

The reviewer has misunderstood how we have used ‘completeness’ in this manuscript. In the section describing our novel QC framework, we use this term to refer to the relative completeness of draft models generated from draft genome assemblies as compared to curated models generated from complete genome assemblies for the same strains. The latter were considered as the ‘complete’ models for this purpose. We are not referring to any measure of network or metabolic pathway completeness. We specifically refer to gene and reaction capture compared to the ‘complete’ models because these features directly reflect the problem we are trying to address i.e. that draft genome assemblies may not contain the complete set of genes that are truly present in the underlying genome. We have updated the manuscript text to further clarify the problem we aim to address in this section and justify the use of gene and reaction capture metrics:

Lines 310-319: “There are now thousands of bacterial genomes available in public databases, the majority of which are in draft form, comprising 10s to 1000s of assembly contigs. This fragmentation of the genome is caused by repetitive sequences that cannot be resolved by the assembly algorithm and/or sequence drop-out. The latter can result in the loss of genetic information such that some portion of genes present in the underlying genome are lost from the genome assembly (either completely or partially). This in turn, poses a limitation for the reconstruction of metabolic models using these assemblies, since most published approaches use sequence searches to predict the presence/absence of genes and their associated enzymatic reactions. Therefore, if we are to use public genome data for high-throughput metabolic modelling studies, it is essential to evaluate the expected model accuracies and understand the minimum input genome quality requirements.”

The biological accuracy of the curated ‘complete’ models has been described previously, and this is now noted in the text at lines 320-324:

“Here we performed a systematic analysis leveraging our published curated KpSC models (n=37, (14)), which were generated using completed genome sequences and were therefore considered to represent ‘complete’ models for which the underlying genome sequence contains all genes that are truly present in the genome (note the biological accuracy of these models was reported previously (14) and is not the subject of the current study).”

Throughput the manuscript we not only compare models in terms of the numbers of genes and reactions, but through comparison of binary growth predictions. Specifically, in the Performance Comparison section (Bactabolize vs other approaches) we use comparison of predicted to experimental phenotypes for strain KPPR1 (see response to rev 1 point 4 for details). In the QC Framework section we compare the predictions derived from draft models generated from draft genome assemblies to those derived from the matched ‘complete’ models, and report the concordance as a measure of impact of input assembly quality (lines 309-394). In the final results section (Predictive accuracy of draft models), we generate 10 additional models and compare the growth predictions to matched experimental data (lines 414-433). We view these phenotype prediction comparisons as the ultimate measure of ‘completeness’ with which to assess our models, because these data have direct biological meaning.

2) The authors have not provided evidence or discussion on the accuracy of any metabolic fluxes, which are considered to be crucial for reconstructing metabolic models. Additionally, the authors have not mentioned the importance of non-growth associated maintenance and the criticality of biomass composition analysis, both of which significantly determine the fluxes in the system.

We acknowledge the importance of flux calculations and accurate biomass compositions when using genome-scale models to quantitatively predict growth rates. However, at this stage, the reconstructions developed using Bactabolize are intended for binary predictions and comparisons of growth capabilities on various substrates. The accuracies we report are based on measures of network completion (presence/absence of relevant reactions leading to growth or no-growth phenotypes) rather than specific growth rates. Thus, the models generated by Bactabolize can be used to explore diversity at the strain level in terms of growth capabilities and can serve as a scaffold for building detailed (customized biomass), strain-specific models. Measuring biomass composition and metabolic flux analysis require significant experimental comparisons that are outside the scope of the current study but could be performed for target strains based on reconstructions developed using Bactabolize.

3) It would be interesting to compare the accuracy of the models generated using Bactabolize with those manually curated.

We did exactly this. We compared the manually curated model iKp1289 as part of our benchmarking. Lines 194 – 199:

“We compared the output and performance of Bactabolize to the two previously published tools that can support high-throughput analyses i.e. CarveMe (30) and gapseq (31). To aid interpretation in the context of community standard approaches, we also include a comparison to the popular web-based reconstruction tool, KBase (ModelSEED), and a manually curated metabolic reconstruction of K. pneumoniae strain KPPR1 (also known as VK055 and ATCC 43816, metabolic model named iKp1289) (15).”

Unfortunately, as far as we aware there are currently no other published manually curated models for strains with matched phenotype data that are also not included as part of our pan-reference model (the latter is a key point to ensure a fair comparison of models generated using our pan-reference vs those generated with a universal reference).

4) The authors have not provided evidence or discussion on the accuracy of any metabolic fluxes, which are considered to be crucial for reconstructing metabolic models.

See response to rev 3, point 2.

5) The justification regarding the completeness of the models requires further discussion.

See response to rev 3, point 1.

6) A detailed discussion on the importance of manually curated models would significantly enhance the quality of the manuscript.

This has been added at lines 458-474:

“Traditionally, genome-scale metabolic reconstruction approaches have relied upon significant manual curation efforts. While there will always remain a need for high quality curated models, such resource intensive approaches preclude their application at scale, and have therefore limited analyses to small numbers of individual strains (15, 16). However, automated reconstruction approaches can support the generation and comparison of multiple strain-specific draft models from which meaningful biological insights can be derived (61). Additionally, the quality of curated models is likely to vary depending on their age, level and type of curation, as well as the approach used for preliminary drafting. Indeed it is possible for automated approaches to outperform manually curated models; a draft model for K. pneumoniae KPPR1 generated using Bactabolize with the KpSC pan-v1 reference model outperformed the manually curated iKp1289 model representing the same strain (15). iKp1289 was published in 2017 (6 years prior to this study) and was initially drafted via the KBase pipeline (33), which uses RAST to annotate the sequences with Enzyme Commission numbers. It has been demonstrated several times that the Enzyme Commission scheme has systematic errors (62, 63), leading to a loss in accuracy when compared to the ortholog identification methods used by automated approaches. Consistent with this assertion, our draft KPPR1 model constructed with KBase (without manual curation) was an outlier in terms of the very low number of genes, reactions and metabolites that were included.”

Author Response

The following is the authors’ response to the previous reviews

Reviewer #2 (Recommendations For The Authors):

1) Overall, the novel phylogenetic analyses presented are satisfactory. With this new piece of information in hand, I would suggest using maximum-likelihood analyses as the major evidence supporting ortholog annotations. In fact, it would be best advised to add the bootstrap support analyses (perhaps over new trees) to the phylogenies presented in the supplement.

Thank you for suggestion. Although it would make sense to present phylogenetic trees constructed by maximum-likelihood analyses, we decided to keep the original trees (for CDCA7 and HELLS) in supplemental figures for an aesthetic reason. For example, for CDCA7/zf-4CXXC_R tree made by maximum likelihood method *Hif2_data2_zf4CXXC_R1_iqtree.txt), it would have been easier to visualize if the plant CDCA7 clade was positioned at the bottom, not the top, of the tree, as the topology was identical in both cases. Unfortunately, as the calculated result randomly put plant CDCA7 clade at the top, plant CDCA7 clade appears to be separated from the clades representing the rest of CDCA7 homologs. While we could manually adjust this in the final drawing, we wanted to avoid that.

2) There are still a few places in the main text where RBH - and is associated E-value - is used as evidence of orthology. As mentioned in my original review, this is evidence for homology, not orthology. Please make sure to amend the final text (for example in the first paragraph of the result section).

We concurred and amended the manuscript following this recommendation.

3) We agree with reviewer 1 that part of the functional considerations outside of the human and frog example should be softened, or clearly labelled as an hypothesis - which is now supported by this interesting study

I assume that this is related to Introduction of CDCA7. As this study defined CDCA7 homologs in result section We believe that this point has been addressed in our last revision.

4) In addition, make sure to indicate in the main text state the point about DNMT3 nomenclature (w.r.t. DRM).

In page 10, we added a sentence below to clarify this point.

“In this report, we call a protein DNMT3 if it clusters into the clade including metazoan DNMT3, plant DNMT3, and DRM.”

Author Response

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

eLife assessment

This important manuscript reveals signatures of co-evolution of two nucleosome remodeling factors, Lsh/HELLS and CDCA7, which are involved in the regulation of eukaryotic DNA methylation. The results suggest that the roles for the two factors in DNA methylation maintenance pathways can be traced back to the last eukaryotic common ancestor and that the CDC7A-HELLS-DNMT axis shaped the evolutionary retention of DNA methylation in eukaryotes. The evolutionary analyses are solid, although more refined phylogenetic approaches could have strengthened some of the claims. Overall, this study should be useful for researchers studying DNA methylation pathways in different organisms, and it should be of general interest to colleagues in the fields of evolutionary biology, chromatin biology and genome biology.

We sincerely appreciate constructive comments and suggestions by the reviewers and a fair and accurate summary by the monitoring editor. Below we made point-by-point responses to reviewers’ comments.

Reviewer #1 (Public Review):

Overall, I find the work performed by the authors very interesting. However, the authors have not always included literature that seems relevant to their study. For instance, I do not understand why two papers Dunican et al 2013 and Dunican et al 2015, which provide important insight into Lsh/HELLS function in mouse, frog and fish were not cited. It is also important that the authors are specific about what is known and in particular about what is not known about CDCA7 function in DNA methylation regulation. Unless I am mistaken, there is currently only one study (Velasco et al 2018) investigating the effect of CDCA7 disruption on DNA methylation levels (in ICF3 patient lymphoblastoid cell lines) on a genome-wide scale (Illumina 450K arrays). Unoki et al 2019 report that CDCA7 and HELLS gene knockout in human HEK293T cells moderately and extremely reduces DNA methylation levels at pericentromeric satellite-2 and centromeric alpha-satellite repeats, respectively. No other loci were investigated, and it is therefore not known whether a CDCA7-associated maintenance methylation phenotype extends beyond (peri)centromeric satellites. Thijssen et al performed siRNA- mediated knockdown experiments in mouse embryonic fibroblasts (differentiated cells) and showed that lower levels of Zbtb24, Cdca7 and Hells protein correlate with reduced minor satellite repeat methylation, thereby implicating these factors in mouse minor satellite repeat DNA methylation maintenance. Furthermore, studies that demonstrate a HELLS-CDCA7 interaction are currently limited to Xenopus egg extract (Jenness et al 2018) and the human HEK293 cell line (Unoki et al 2019). Whether such an interaction exists in any other organism and is of relevance to DNA methylation mechanisms remains to be determined. Therefore, in my opinion, the conclusion that "Our co- evolution analysis suggests that DNA methylation-related functionalities of CDCA7 and HELLS are inherited from LECA" should be softened, as the evidence for this scenario is not very compelling and seems premature in the absence of molecular data from more species.

We appreciate this reviewer’s thorough reading of our manuscript.

Regarding the citation issues, we will cite Dunican 2013 and Dunican 2015. In addition, we went through the manuscript to update the citations.

As pointed out by the reviewer, the role of CDCA7 in genome DNA methylation was extensively studied in Velasco et al 2018. The result, together with Thijssen et al (2015), and Unoki et al. (2018), supports the idea that ZBTB24, CDCA7 and HELLS act within the same pathway to promote DNA methylation, the pattern of which is overlapping but distinct from DNMT3B-mediated methylation. This observation suggests that a ZBTB24- CDCA7-HELLS mechanism for DNA methylation may involve an alternative DNMT. Interestingly, our analysis of the gene presence-absence pattern revealed that the presence of CDCA7 coincides with DNMT1 more than DNMT3 genes. Indeed, while CDCA7 is lost from diverse branches of eukaryote species, genomes encoding CDCA7 always encode HELLS, and almost always encode DNMT1. Based on this observation, we speculate the role of CDCA7 is tightly linked to HELLS and DNA methylation throughout evolution.

As pointed out by Reviewer 1, the link between CDCA7, HELLS and DNA methylation has not been determined experimentally across these species. However, based on our previously published and unpublished data, we are confident about the functional interaction between CDCA7 and HELLS in Xenopus laevis and Homo sapiens.

Furthermore, the importance of HELLS homologs in DNA methylation has been extensively studied in human, mice and plants. We hope our current study will motivate the field to experimentally test the evolutionary conservation of HELLS-CDCA7 interaction, as well as their importance in DNA methylation, in other species.

The authors used BLAST searches to characterize the evolutionary conservation of CDCA7 family proteins in vertebrates. From Figure 2A, it seems that they identify a LEDGF binding motif in CDCA7/JPO1. Is this correct and if yes, could you please elaborate and show this result? This is interesting and important to clarify because previous literature (Tesina et al 2015) reports a LEDGF binding motif only in CDCA7L/JPO2.

We searched for a LEDGF binding motif ({E/D}-X-E-X-F-X-G-F, also known as IBM described in Tesina et al 2015) in vertebrate CDCA7 proteins, and reported their positions in Figure 2A. Examples of identified LEDGF-binding motifs are now presented in Fig. 2C.

To provide evidence for a potential evolutionary co-selection of CDCA7, HELLS and the DNA methyltransferases (DNMTs) the authors performed CoPAP analysis. Throughout the manuscript, it is unclear to me what the authors mean when referring to "DNMT3". In the Material and Methods section, the authors mention that human DNMT3A was used in BLAST searches to identify proteins with DNA methyltransferase domains. Does this mean that "DNMT3" should be DNMT3A? And if yes, should "DNMT3" be corrected to "DNMT3A"? Is there a reason that "DNMT3A" was chosen for the BLAST searches?

As described in the Methods section, both Human DNMT1 and DNMT3A were used to initially identify any proteins containing a domain homologous to the DNA methyltransferase catalytic domain. Within Metazoa, if their orthologs exist, the top hit from BLAST search using human DNMT1 and DNMT3A show E-value 0.0, and thus their orthology is robust. This is even true for DNMT1 and DNMT3 homologs in the sponge Amphimedon queenslandica, which is one of the earliest-branching metazoan species. For other DNMTs, such as DNMT2, DNMT4, DNMT5, DNMT6, we conducted separate BLAST searches using those proteins as baits as described in Methods. The methyltransferase domain was then isolated using the NCBI conserved domains search. The selected DNMT domain sequences were aligned with CLUSTALW to generate a phylogenetic tree to further classify DNMTs. In response to reviewer #2’s comments, we also generated another multi-sequence alignment of DNMTs using MUSCLE v5 and conducted maximum-likelihood-based phylogenetic tree assembly using IQ-TREE (new Fig. S6). The overall topology of these trees is consistent except for orphan DNMTs. It has been suggested that vertebrate DNMT3A and DNMT3B are derived from duplication of a DNMT3 gene of chordates ancestor (e.g., Liu et al 2020, PMID 31969623). As such many invertebrates encode only one DNMT3. As previously shown (Yaari et al., 2019, PMID 30962443), plants have two distinct DNMT3-like protein family, the ‘true DNMT3’ and DRM, the plant specific de novo DNMT that is often considered to be a DNMT3 homolog (see Reviewer 2’s comment). Our phylogenetic analysis successfully deviated the clade of DNMT3 and DRM from the rest of DNMTs (Figure S6). Yaari et al noted that PpDNMT3a and PpDNMT3b, the two DNMT3 orthologs encoded by the basal plant Physcomitrella patens, are not orthologs of mammalian DNMT3A and DNMT3B, respectively. Therefore, to minimize such nomenclature confusions, any DNMTs that belong to either the DNMT3 or DRM clades indicated in Figure S6 are collectively referred to as ‘DNMT3’ throughout the paper (see Figure S2 for overview).

CoPAP analysis revealed that CDCA7 and HELLS are dynamically lost in the Hymenoptera clade and either co-occurs with DNMT3 or DNMT1/UHRF1 loss, which seems important. Unfortunately, the authors do not provide sufficient information in their figures or supplementary data about what is already known regarding DNA methylation levels in the different Hymenoptera species to further consider a potential impact of this observation. What is "the DNA methylation status" of all these organisms? This information cannot be easily retrieved from Table S2. A clearer presentation of what is actually known already would improve this paragraph.

As the DNA methylation status of the species in the Hymenoptera clade has not been comprehensively tested, we initially did not include this information to Figure 7. However, during the course of the revision, we realized that Bewick et al.2017 (PMID 28025279) reported that DNA methylation is absent from the braconid wasp Aphidius ervi. We originally conducted synteny analysis on Aphidius gifuensis, which has a chromosome-level genome assembly with annotated proteins available in NCBI, whereas annotated proteins for Aphidius ervi protein are not available in NCBI. By conducting tBLASTn search against the Aphidius ervi genome, we now found that the presence/absence pattern of CDCA7, HELLS, DNMT1, DNMT3 and UHRF1 in Aphidius ervi is identical to that of Aphidius gifuensis, with a caveat that genome assembly of Aphidius ervi is at scaffold-level. In other words, DNA methylation, DNMT1 and CDCA7 are absent in Aphidius ervi, where 5mC is undetectable. Additionally, we also realized that the DNA methylation status reported for some species in Bewick et al. 2017 was inferred from the CpG frequency instead of the direct experimental detection of methylated cytosines. Therefore, we have amended Table S3 to indicate the presence of 5mC only for those species where this was experimentally tested. As such, we now consider the DNA methylation status of Fopius arisanus, which lacks DNMT1 and CDCA7, to be unknown.

Altogether, among the 17 Hymenoptera species that we analyzed (listed in the amended Table S3), the 8 species that have detectable DNA methylation all encode CDCA7, whereas the 2 species that do not have detectable DNA methylation lack CDCA7. We will note this finding in the revised text, and include the known 5mC status in the new Figure 7.

Furthermore, A. thaliana DDM1, and mouse and human Lsh/Hells are known to preferably promote DNA methylation at satellite repeats, transposable elements and repetitive regions of the genome. On the other hand, DNA methylation in insects and other invertebrates occurs in genic rather than intergenic regions and transposable elements (e.g. Bewick et al 2017; Werren JH PlosGenetics 2013). It would be helpful to elaborate on these differences.

We were aware of this interesting point, which was discussed in the third paragraph of the Discussion. To better illustrate this point, we now expanded the Discussion (page 14) to speculate about the role of DNA methylation in insects, where emerging evidence indicates the importance of DNMT1 in meiosis. It should be noted that, in the Arabidopsis ddm1 mutant, reduction of CG methylation of gene bodies is common (50% of all methylated euchromatic genes) (Zemach et al, 2013). In addition, hypomethylation is not limited to satellite repeats and transposable elements in ICF patients defective in HELLS or CDCA7 (Velasco et al., 2018).

Reviewer #2 (Public Review):

In this manuscript, Funabiki and colleagues investigated the co-evolution of DNA methylation and nucleosome remolding in eukaryotes. This study is motivated by several observations: (1) despite being ancestrally derived, many eukaryotes lost DNA methylation and/or DNA methyltransferases; (2) over many genomic loci, the establishment and maintenance of DNA methylation relies on a conserved nucleosome remodeling complex composed of CDCA7 and HELLS; (3) it remains unknown if/how this functional link influenced the evolution of DNA methylation. The authors hypothesize that if CDCA7-HELLS function was required for DNA methylation in the last eukaryote common ancestor, this should be accompanied by signatures of co-evolution during eukaryote radiation.

To test this hypothesis, they first set out to investigate the presence/absence of putative functional orthologs of CDCA7, HELLS and DNMTs across major eukaryotic clades. They succeed in identifying homologs of these genes in all clades spanning 180 species. To annotate putative functional orthologs, they use similarity over key functional domains and residues such as ICF related mutations for CDCA7 and SNF2 domains for HELLS. Using established eukaryote phylogenies, the authors conclude that the CDCA7-HELLS-DNMT axis arose in the last common ancestor to all eukaryotes. Importantly, they found recurrent loss events of CDCA7-HELLS-DNMT in at least 40 eukaryotic species, most of them lacking DNA methylation.

Having identified these factors, they successfully identify signatures of co-evolution between DNMTs, CDCA7 and HELLS using CoPAP analysis - a probabilistic model inferring the likelihood of interactions between genes given a set of presence/absence patterns. As a control, such interactions are not detected with other remodelers or chromatin modifying pathways also found across eukaryotes. Expanding on this analysis, the authors found that CDCA7 was more likely to be lost in species without DNA methylation.

In conclusion, the authors suggest that the CDCA7-HELLS-DNMT axis is ancestral in eukaryotes and raise the hypothesis that CDCA7 becomes quickly dispensable upon the loss of DNA methylation and/or that CDCA7 might be the first step toward the switch from DNA methylation-based genome regulation to other modes.

The data and analyses reported are significant and solid. However, using more refined phylogenetic approaches could have strengthened the orthologous relationships presented. Overall, this work is a conceptual advance in our understanding of the evolutionary coupling between nucleosome remolding and DNA methylation. It also provides a useful resource to study the early origins of DNA methylation related molecular process. Finally, it brings forward the interesting hypothesis that since eukaryotes are faced with the challenge of performing DNA methylation in the context of nucleosome packed DNA, loosing factors such as CDCA7-HELLS likely led to recurrent innovations in chromatin-based genome regulation.

Strengths:

• The hypothesis linking nucleosome remodeling and the evolution of DNA methylation.

• Deep mapping of DNA methylation related process in eukaryotes.

• Identification and evolutionary trajectories of novel homologs/orthologs of CDCA7.

• Identification of CDCA7-HELLS-DNMT co-evolution across eukaryotes.

Weaknesses:

• Orthology assignment based on protein similarity.

• No statistical support for the topologies of gene/proteins trees (figure S1, S3, S4, S6) which could have strengthened the hypothesis of shared ancestry.

We appreciate the reviewers’ accurate summary, nicely emphasizing the importance of the our study. We agree that better phylogenetic analysis for orthology assignment will strengthen our conclusion. Having anticipated this weakness, however, we specifically conducted a CoPAP analysis exclusively for Ecdysozoa specieswhich supported our major conclusion, as orthology assignment is straightforward in these species. For example, if we conduct BLAST search against the clonal raider ant Oocerea biroi protein dataset using human HELLS as a query, top 1 hit is a protein sequence annotated as one of three isoforms of ‘lymphoid-specific helicase” (i.e., HELLS), with E value 0.0. Similarly, the top BLAST hit from the Oocerea biroi dataset using human DNMT1 as a query also returns with isoforms of DNMT1 with E value 0.0. As such, there are little disputes in orthology assignment in Ecdysozoa. Outside of Chordata, classification of DNMTs, particularly in Excavata and SAR, require more extensive identification in these supergroups. Our current orthology assignment for the major targets in this study (HELLS, DNMT1, DNMT3, DNMT5) is largely consistent with published results (Ponger et al., 2005 PMID 15689527; Huff et al, 2014 PMID 24630728; Yaari et al., 2019 PMID 30962443; Bewick et al., 2019 PMID 30778188). However, while we are preparing this response and re-crosschecking our assignments with these references, we realized that we had erroneously missed DNMT5 orthologs in Leucosporidium creatinivorum, Postia placenta, Armillaria gallica and Saitoella complicata, and a DNMT6 ortholog in Fragilariopsis cylindrus. We also recognized that DNMT4 orthologs were identified in Fragilariopsis cylindrus and Thalassiosira pseudonana in Huff et al 2014 (PMID 24630728), but in our phylogenetic analysis, these proteins form a distinct clade between DNMT1/Dim-2 and DNMT4 (original Figure S6), although the confidence level of this classification by Huff et al was not strong. To resolve this potential confusion in DNMT annotations, we generated new multiple sequence alignments with MUSCLE v5 and IQ-TREE 2 (maximum likelihood-based method, coupled with selection of optimal substitution model and bootstrapping). The tree topology was not significantly altered between the two methods, except for the unambiguous location of orphan DNMTs and DNMT4-related proteins. To avoid unnecessary confusion in the DNMT annotations, we decided to present MUSCLE-IQ- TREE for the DNMT phylogenetic tree and classification (new Fig. S6). The raw results of IQ-TREE analysis for CDCA7/zf-4CXXC_R1, HELLS SNF2 domain, and DNMTs are included as Dataset S1-S3. We then conducted CoPAP analysis using the corrected classification. As it is not clear a priori if fungal specific CDCA7-like proteins (now referred to as CDCA7F with class II zf-4CXXC_R1) should be considered CDCA7 orthologs, we conducted CoPAP against two lists; the first list includes CDCA7F in the CDCA7 group, whereas the second list includes a separate category of class II zn-4CXXC_R1, which includes CDCA7F. Both results show slightly different topology in the coevolutionary linkages but support our major conclusion that CDCA7 coevolved with DNMT1-UHRF1 and HELLS. These new CoPAP results are shown in Fig. S7.

Reviewer #1 (Recommendations For The Authors):

Summary

Last sentence: "...a unique specialized role of CDCA7 in HELLS-dependent DNA methylation maintenance...". What do the authors mean?

Our analysis strongly indicates that CDCA7 is dispensable in systems lacking HELLS and DNMT (particularly DNMT1). In other words, species preserve CDCA7 only if it has both HELLS and DNMT1 (or in some cases DNMT5). The importance of HELLS homologs in DNA methylation has been extensively studied in human, mouse and plants. However, in these studies, substantial DNA methylation remains despite the defective HELLS/DDM1 (especially in euchromatic regions). Additionally, there are species (e.g., Bombyx mori) that have DNMT1 and detectable DNA methylation but lacks HELLS and CDCA7. These observations suggest that the role of CDCA7 must be unique and specialized in a way that it is strongly coupled to HELLS-dependent DNA methylation (but not HELLS-independent DNA methylation), and that this function of CDCA7 seems to be inherited from the last eukaryotic common ancestor.

Introduction

• page 3: "DNMTs are largely subdivided into maintenance and de novo DNMTs" - Which species are the authors referring to?

As described in the cited reference (Lyko 2018), maintenance DNA methylation and de novo DNA methylation are well accepted functional classification of DNA methylation. It is also currently accepted that distinct DNMTs execute maintenance DNA methylation or de novo DNA methylation, although crosstalk between these processes has been reported. Therefore, we stated, “DNMTs are largely subdivided into maintenance DNMTs and de novo DNMTs”, and this subdivision is species independent.

• page 3" "Maintenance DNMTs recognize hemimethylated CpGs. " - Can the authors please define the species and/or literature they are referring to? This seems important to clarify. For instance, mammalian DNMT1 requires a co-factor, UHRF1, which recognizes hemimethylated DNA and H3K9me3 (Bostick et al 2007).

We meant to describe, “Maintenance DNMTs directly or indirectly recognize hemimethylated CpGs…”. The specific requirement of UHRF1 for DNMT1-mediated maintenance DNA methylation is explained in the subsequent sentence “In animals…”. In the case of Cryptococcus neoformans, DNMT5 recognizes hemimethylated DNA independently of UHRF1 in vitro to execute maintenance methylation.

• page 3: The authors may want to mention that A. thaliana also has a de novo DNA methyltransferase, DRM2, a homolog of the mammalian DNMT3 methyltransferases. This seems important, since they show in Figure 1 that a de novo methyltransferase is found in A. thaliana. Also, later in their manuscript they mention plant de novo DNA methylation.

Thanks for pointing this out. As shown in Figure 5, we classified plant DRMs as DNMT3-like proteins, but we now note this in the Introduction.

• page 3: Sentence starting "In about 50% of ICF patients,..." - Why is DNMT3B referred to as "de novo", is it not a de novo DNA methyltransferase?

You are correct. Quotation marks are now removed to avoid unnecessary confusion.

• page 4: Sentence starting "Indeed, the importance of HELLS/CDCA7 in DNA methylation maintenance...", - Which references (Han et al., 2020; Ming et al., 2021; Unoki, 2021; Unoki et al., 2020) provide experimental evidence for a role of CDCA7 in DNA methylation maintenance by DNMT1?

Thanks for pointing out the typo. “/CDCA7” is now removed.

• page 5: Sentence starting "Indeed, it has been shown that DNMT3A..." - Should DNMTB be DNMT3B?

Yes. This is now corrected.

Results

• Page 5: Sentence starting "However, we identified a protein..." - No A. thaliana reference?

We added Zemach et al 2010, and Chan et al 2005.

• Figure 2B: "ICF4 mutations" should this be "ICF3 mutations"?

• Figure 3: "ICF4 mutations" should this be "ICF3 mutations"?

• Figure 4: "ICF4 mutations" should this be "ICF3 mutations"?

• Figure S1: Orange colored "CDC7L (fish), CDC7e, CDC7, CDC7L" is there an "A" missing?

• Figure S5: "ICF4 mutations" should this be "ICF3 mutations"?

These typos are now corrected. Thank you.

• Figure S7: What is "CDCA7(II)" referring to, "zf-4CXXC_R1 class II (plants)"?

The original CDCA7 (II) included proteins with class II zf-4CXXC_R1, which are found in plants, fungi, Acanthamoeba castellanii and Amphimedon. Among those species, the prototypical CDCA7 orthologs are absent only in fungi. It has been a priori unclear if fungal proteins with class II zf-4CXXC_R1 (now we term CDCA7F) should be included in CDCA7 for CoPAP analysis. Although we originally included CDCA7F in CDCA7, we now show the results of two analyses. In the first one (Fig. S7A) CDCA7F was included in CDCA7, whereas in in the second one (Fig. S7B) CDCA7F was included in the separate category of class II zf-4CXXC_R1. Topologies of two results are slightly different, but they both show coevolutionary linkage between the CDCA7 and DNMT1- UHRF1 cluster.

• Figure 4 and 5: In the case of preliminary genome assemblies what is the difference between empty squares with dotted lines and filled squares without dotted lines?

As it is difficult to be certain of a gene’s absence (did the species lose the gene or is it simply not annotated due to incomplete genome coverage?), we illustrated the absence of a gene in preliminary genome assemblies with an empty square with dotted outline. Since the presence of a gene is evident regardless of the level of genome assembly, the presence of a gene is represented with filled squares with solid lines, even for preliminary genome assemblies.

• Figure 1: Why was Mus musculus - one of the main model organisms used for many DNA methylation studies not included? Also what are empty and filled squares?

Filled and empty squares indicate the presence and absence of the indicated genes, respectively. Clarifying statement is now added in the figure legends. Mus musculus is now included in the figure.

• Figure S2: Adding the existence of DNA methylation and DNMT3 in the bottom right part of the figure (overall no of species) would make this panel more informative

We included this overview to summarize the co-retention of CDCA7, HELLS and maintenance DNMTs across the analyzed species. We decided not to include DNA methylation, since DNA methylation status is known for only a fraction of the listed species. Inclusion of DNMT3 will introduce too many possible gene presence-absence combinations to convey a clear message. However, we now mention in the revised text (page 11, second paragraph) that unlike the prevalent co-retention of DNMT1 in species with CDCA7, we identified several species that possess CDCA7, HELLS and DNMT1 but lack DNMT3. These examples include insects such as the bed bug Cimex lectularius and the red paper wasp Polistes canadensis.

• Page 6: Sentence starting "This leucine zipper sequence is highly conserved..." - Figure/Reference missing?

The sequence alignment of the leucine zipper is now shown in Fig. 2C.

• page 6: Sentence starting "In contrast to zf-4CXXC_R1 motif-containing proteins..." - The authors may want to mention the role of the CXXC zf domain in KDM2A/B, DNMT1, MLL1/2 and TET1/3 and what the CDCA7 CXXC zf domain is/could be required for.

The notion that zf-CXXC binds to nonmethylated CpG is now included. Due to the substantial difference between zf-CXXC and zf-4CXXC_R1, we hesitated to relate the function of zf-4CXXC_R1 with zf-CXXC, but we now discuss a potential role of zf- 4CXXC_R1 in sensing DNA methylation status in Discussion (Page 13).

• page 7: Sentence starting "Second, the fifth cysteine is replaced..."- Zoopagomycota" - Figure 4A does not have this labeling, one has to deduce this from Figure 4B.

We fixed this by including the list of Zoopagomycota species in the main text.

• page 7: Sentence containing "Neurospora crassa DMM-1 does not directly regulate DNA methylation or demethylation but rather..." - How does the information about DMM- 1 relate to what is shown in Figure 4B, to CDCA7, HELLS and DNMTs? Please clarify.

Both Neurospora DMM-1 and Arabidopsis IBM1 contain the JmjC domain and are implicated in an indirect control mechanism of DNA methylation. Since it has never been pointed out that they have a divergent zf-4CXXC_R1 domain, which clearly shares the origin with CDCA7 proteins, we thought that this is important to note. We realized that we did not clearly mark Neurospora XP-956257 as DMM-1 in Fig. 4B. This is now fixed.

• Heading "Systematic identification of CDCA7, HELLS and DNMT homologs in eukaryotes". When mentioning CDCA7 the authors may want to decide on the use of one consistent definition of "prototypical (Class I) CDCA7-like proteins (i.e. CDCA7 orthologs)" "Class I CDCA7 proteins". Constantly changing the way how they refer to these proteins is very confusing.

We now make it clear that we call proteins with class I zf-CXXC_R1 motif CDCA7 orthologs. We also define class II zf-4CXXC_R1 (as those with a substitution at ICF- associated glycine residue). Since no clear CDCA7 orthologs can be found in fungi, we now call fungi proteins with class II zf-4CXXC_R1 “CDCA7F”, implying its ambiguous orthology assignment.

Under this heading there is also no mention of DNMTs. Instead, the authors introduce DNMTs under the heading "Classification of DNMTs in eukaryotes" - Please clarify.

This is now corrected.

• page 9: Sentence containing "... presence of DNMT1, UHRF1 and CDCA7 outside of Viridiplantae and Opisthokonta is rare". What does "rare" mean? How is UHRF1 relevant here?

Among the 32 species outside of Viridiplantae and Opisthokonta, only the Acanthamoeba castellanii genome encodes clear orthologs of DNMT1, UHRF1 and CDCA7. Although it is often difficult to deduce if the selected panel of species is a reasonable representation, we think that it is not unreasonable to state that Acanthamoeba is a rare case to encode this set of proteins outside of Viridiplantae and Opisthokonta. We include UHRF1 since it is a well-established activator of DNMT1, and indeed our CoPAP analysis showed a tight coevolution of UHRF1 with DNMT1. Outside of Viridiplantae and Opisthokonta, only Acanthamoeba castellanii and Naegleria gruberi encode UHRF1. Interestingly, these two species also encode CDCA7 and HELLS.

Having said that, we rephrased this sentence, which reads; “Species that encode a set of DNMT1, UHRF1, CDCA7 and HELLS are particularly enriched in Viridiplantae and Metazoa.”

• page 11: Sentence containing "..., that the function of CDCA7-like proteins is strongly linked to HELLS and DNMT1,..." What do the authors mean with "the function of CDCA7-like proteins"? And what happened to DNMT3?

Our observation that almost all species that contain CDCA7 (including fungal CDCA7F) also have DNMT1 and HELLS, despite the frequent loss of these genes in species that do not contain CDCA7, indicates “that the function of CDCA7-like proteins is strongly linked to HELLS and DNMT1”. We found only 2 species that possesses CDCA7 (class I or class II) but not DNMT1 among the panel of 180 species. These 2 exceptional species, Naegleria gruberi and Taphrina deformans, do encode UHRF1-like proteins and a DNMT (an orphan DNMT in N. gruberi and DNMT4 in T. deformans). In contrast, we found 26 species that possess CDCA7 (or CDCA7F) but not DNMT3 (Table S1), so the linkage between CDCA7 and DNMT3 is weaker.

• page 11: Sentence containing "..., CDCA7 is lost from this gene cluster in parasitoid wasps, including Ichneumonoidea wasps and chalcid wasps". This sentence is confusing because already in an earlier paragraph the authors say that "Microplitis demolitor lost CDCA7" and in the following sentence they say "...among Ichneumonoidea wasps, CDCA7 appears to be lost in the Braconidae clade, ...". It would greatly help this reader if the authors could streamline these sentences and also decide on whether CDCA7 is lost in M. demolitor or CDCA7 appears to be lost in M.demolitor.

The confusion was in part due to the difficulty in differentiating between the true loss of a gene versus its apparent absence in a species due to an incomplete genome assembly, including for of M. demolitor. To verify that the loss of CDCA7 was not due to gaps in the genome assembly, we executed the synteny analysis. However, we edited this section to improve the readability (Page 12-13).

What could be the role for HELLS/CDCA7 in insect DNA methylation? In several cases, the authors analyses reveal co-evolutionary links between DNMT3 (DNMT3A?) and CDCA7/HELLS. I do not understand why this finding is not really discussed by the authors. Instead there is a strong focus on replication-uncoupled DNA methylation maintenance. Could the authors elaborate why?

The role of DNA methylation in insects is largely unclear, so discussion must be highly speculative. A recent finding in the clonal raider ant, showing that DNMT1 is not essential for development but is critical for oogenesis, pointed toward a possible more universal role of DNA methylation in meiosis. Stimulated from a finding in Neurospora, where DNA methylation is required for homolog pairing during meiosis, we discuss a speculative model that DNA methylation status acts as a hallmark to distinguish between healthy/young DNA and old/mutated (or competitive/pathogenic) DNA at homolog pairing during meiosis (page 14).

Regarding the cases where CDCA7 and DNMT3 are co-lost, we had discussed about this phenomenon at the last section of Result, stating, “This co-loss of CDCA7 and DNA methylation (together with either DNMT1-UHRF1or DNMT3) in braconid wasps suggests that evolutionary preservation of CDCA7 is more sensitive to DNA methylation status per se than to the presence or absence of a particular DNMT subtype.” Please note that we found several lineages that lacks CDCA7 but has DNMT1 (and DNMT3), whereas almost all species that has CDCA7 also has DNMT1 (but not necessarily DNMT3). Supported with our CoPAP analyses, our results indicate the tight functional link between CDCA7 and DNMT1, but it does not necessarily mean that CDCA7 does not play any role related to DNMT3 or de novo methylation. Clarification of this point and our speculation of how CDCA7 loss is linked to reduced requirement of DNA methylation are discussed in page 13 and 14 with additional texts.

Discussion

• page 12: Where is the data supporting. "... the red flour beetle Tribolium castaneum possesses DNMT1 and HELLS, but lost DNMT3 and CDCA7"?

Figure 5, Figure S2 and Table S1. This is now noted in the text.

• page 14: Based on which parts of their analyses or evidence from the literature can the authors speculate that "...the evolutionary arrival of HELLS-CDCA7 in eukaryotes might have been required to transmit the original immunity-related role of DNA methylation from prokaryotes to nucleosome-containing (eukaryotic) genomes"? Please clarify.

This is inferred from the well-known role of DNA methylation in bacteria for defending against phage viruses. However, it was not correct to state that such a function was inherited from prokaryotes. It should be stated that it was inherited from the last universal common ancestor (LUCA). We also admit that it is not clear if such an immunity-related role was inherited from LUCA, or if it emerged through convergent evolution. Therefore, we amended this description to emphasize our hypothesis that the advent of CDCA7 was “a key step to transmit the DNA methylation system from the LUCA to the eukaryotic ancestor with nucleosome-containing genomes”.

Supplementary Figures/Tables

• page 26: Table S2 and Table S3, it seems that these tables show data that supports what is shown in Figure 7 and not Figure 5.

You are correct. Thank you for pointing out the typos.

Has the methylation status been assessed in C. glomerata, C. typhae, Chelonus insularis, Diachasma alloeum or Aphidius gifuensis? Please clarify in Table S2.

Not to our knowledge. However, as we realized that absence of DNA methylation in Aphidius ervi was previously reported (Bewick et al 2017), we now included this data together with presence/absence analysis of DNMT1, UHRF1, DNMT3, CDCA7 and HELLS. Known presence/absence of DNA methylation is now shown in Fig.7.

Reviewer #2 (Recommendations For The Authors):

Recommendation to strengthen the paper:

1) Phylogenetics:

• Test and report the appropriateness of the substitution model used in protein alignments/trees.

• Use Maximum likelihood methods and/or MCM Bayesian inference to build and report trees with well supported topologies. This is required to properly assign orthology (shared ancestry). This will avoid false interpretation due to technical limitation of similarity-based phylogenies (without statistical support). Figure S1, S3, S4 and S6.

To address these points, we made new multisequence alignments using MUSCLE v6 and generated phylogenetic trees using the maximum likelihood-based IQ-TREE 2, where multiple models were screened. A consensus tree was generated after 1000 bootstrap replicates from the best alignment and model. The topology and assignment of these new trees were largely consistent with the original trees, except for some corrections in DNMT assignment as discussed below.

1. We realized that we erroneously missed DNMT5 orthologs of Leucosporidium creatinivorum, Postia placenta, Armillaria gallica and Saitoella complicata., and DNMT6 orthologs from Fragilariopsis cylindrus reported in Huff et al 2014 (PMID 24630728). They are now included in the new list and CoPAP analysis.

2. DNMT4 orthologs were identified in Fragilariopsis cylindrus and Thalassiosira pseudonana by Huff et al 2014 (PMID 24630728), but in our original phylogenetic analysis, these proteins form a distinct clade between DNMT1/Dim-2 and DNMT4. The new tree and classification are more consistent with Huff et al, so we present the new tree in Fig. S6 and conducted the classification based on this tree.

Beside Fig. S6, we decided to maintain original Fig. S1, S3 and S4 (with a few adjustments) for better visibility, but we included the results of IQ-TREE analysis as Dataset S1-S3.

The CoPAP analysis based on the revised assignment slightly changed the topology of coevolutionary linkages. In addition, we obtained a slightly different result depending on whether fungal specific CDCA7 with class II zn-4CXXC_R1 (now referred to as CDCA7F) is included as a CDCA7 ortholog or not. Despite this difference, we reproducibly observed the coevolutionary linkage between CDCA7 and DNMT1- UHRF1.

• Be more careful with wording: RBH is not sufficient to call gene/proteins orthologs (e.g. Page 8). The above mentioned method will help you support this claim (+ synteny when you can).

We were aware of this issue. This is why we conducted phylogenetic tree building based on sequence alignment of full-length HELLS (Fig. S3) and SNF2 domain only (Fig. S4), as explained in the text. We found that the RBH criterion is robust in Metazoa; orthologs are easily recognizable with very low E-value (0.0) and extensive homology over the full length of the protein, while synteny is not practical to employ in the diverse set of species.

• Also, use "co-retention" or "co-evolution" but not "co-selection" when describing CoPAP results - as CoPAP does not test for signature of natural selection.

This is a good point and is now corrected.

• The statistics (p-val...) underlying the CoPAP analyses should be explained.

The explanation is now added in Methods section.

“A method to calculate p-value for CoPAP was described previously (Cohen et al., 2012, PMID 22962457). Briefly, for each pair of tested genes, Pearson's correlation coefficient was computed. Parametric bootstrapping was used to compute a p-value by comparing it with a simulated correlation coefficient calculated based on a null distribution of independently evolving pairs with a comparable exchangeability (a value reporting the likelihood of gene gain and loss events across the tree).”

2) Figure S2 and S3 could be improved for readability

After consideration of this criticism, we decided to keep their original formats for following reasons.

Figure S2. The purpose of this list is to better visualize the comprehensive list shown in Table S2. A consolidated list is already shown in Figure 5. An alternative choice is to make a diagram where individual species names are unreadable. This kind of presentation is seen in many published papers, but we found that they are not helpful to check the details. As this is a supplementary figure, we prefer to show the detailed data that can be visible without a specialized software.

Figure S3. This figure is included to show which SNF2 family proteins are more likely to be misassigned as HELLS/DDM1 orthologs. We believe that the figure serves this purpose.

3) What is the meaning of the coloring patterns of ICF residues in znf?

ICF residues are highlighted as light blue in the schematics to indicate its conservation. In the alignment, the coloring reflects the level of conservation within the shown set of proteins, and the choice of coloring was set by Jalview.

4) To improve clarity: the introduction could be more focused on evolutionary considerations and functional link between CDCA7-HELLS and DNMTs.

We revised the first paragraph of the introduction to illustrate this point.

5) Could indicate the CDC7A loss / DNA methylation hypothesis in the abstract.

We now included this hypothesis in the Abstract.

Author Response

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

Reviewer #1 (Public Review):

This study provides insights into the early detection of malignancies with noninvasive methods. The study contained a large sample size with external validation cohort, which raises the credibility and universality of this model. The new model achieved high levels of AUC in discriminating malignancies from healthy controls, as well as the ability to distinguish tumor of origin. Based on these findings, prospective studies are needed to further confirm its predictive capacity.

However, there are several concerns about the manuscript, which needs to be clarified or modified.

1) The use of "multimodal model" will definitely increase workload of the testing. From the results of this manuscript, the integration of multimodal data did not significantly outperform the EM-based model. Is this kind of integration necessary? Is that tool really cost-effective? The authors did not convince me of its necessity, advantages, and clinical application.

To provide further evidence supporting the advantages of using multimodal model (stack model) over EM-based model, we performed the DeLong test and provided data in Table S7 and Figure S6. Our data show that the stack model outperformed the EM-based model, with significantly higher AUC (AUC difference = 0.0286, p<0.0001). Moreover, the stack model exhibited significantly higher sensitivity for detecting cancer patients of five cancer types in both discovery (73.8% versus 59.5%, p<0.0001, Figure S6A) and validation cohort (72.4% versus 61.5%, p=0.0002, Figure S6B) at comparable specificity of > 95%. The number of misclassified cases were lower when using stack model as compared to the EM-based model (Figure S6C and S6D). Strikingly, we observed that the stack model significantly improved the sensitivity for detecting lung cancer patients compared to the EM based model in both discovery (78.5% versus 44.1%, Figure S6A) and validation cohort ( 83.7% versus 55.8%, Figure S6B), indicating that other ctDNA signatures are also the important biomarkers for detecting lung cancer. Therefore, we conclude that the combination of multiple signatures of ctDNA, ie. the multimodel approach, could improve the sensitivity of multi-cancer detection.

Given the same wet lab protocol, the difference in computational time between a single EM-based model and the stack model is about 10-11 minutes per sample, but the real difference in analysis time can be reduced to ~1 min/sample by parallelization. With regards to the wet lab protocol, an important novelty of SPOT-MAS technology is its all-in-one approach that enables simultaneous analysis of different ctDNA signatures using a single blood draw and a single library reaction, greatly reducing the experimental cost. Thus, we strongly argue that our approach improves the detection sensitivity by increasing the breadth of ctDNA analysis while achieving cost effectiveness for sample preparation and sequencing with negligible trade-off of analysis time .

We have also added the following sentences in the discussion to clarify this point. (Line 618-625)

“Moreover, this study showed that the feature of EM achieved the highest performance among the five examined ctDNA signatures in discriminating cancer from healthy controls (Figure S6). Importantly, we found that combining EM with other ctDNA signatures in a stack model could further improve the sensitivity for detecting cancer samples, with significant improvement for lung cancer patients (Figure S6A and S6B). These findings highlighted that the multimodal analysis of multiple ctDNA signatures by SPOT-MAS could increase the breadth of ctDNA feature analysis, thus enhancing the detection sensitivity while maintaining the low cost of sample preparation and sequencing.”

2) The baseline characteristics of part of the enrolled patients are not clear. It seems that some of the cancer patients were diagnosed only by imaging examinations. The manuscript described "staging information was not available for 25.7% of cancer patients, who were confirmed by specialized clinicians to have non-metastatic tumors". I have no idea how did this confirmation make? According to clinicians' experience only?

Our study only recruited cancer patients with non-systemic-metastatic stages (Stage I-IIIA) in which cancer is localized to the primary sites and has not spread to other organs. We excluded patients who were diagnosed with metastatic stage IIIB and IV cancer. All healthy subjects were confirmed to have no history of cancer at the time of enrollment. They were followed up at six months and one year after enrollment. The majority of cancer patients (74.3%) were confirmed to have cancer by abnormal imaging examination and subsequent tissue biopsy confirmation of tumor staging and metastasis status. For patients with unavailable staging information (25.7%), they initially went to the study hospitals for imaging examination. Upon receiving positive imaging results (MRI scan or CT scan), they moved to another hospital for surgery, leading to missing tumor staging information at the original study hospitals. The metastasis status of these patients were later obtained via communications between the clinicians at the study hospitals and the clinicians at the surgery hospitals, subject to existing data sharing agreement between the two hospitals. For those with metastatic cancer or unclear metastatic status, they were excluded from our study.

We have added the following sentences in the method (Line 127-135) and discussion section (Line 679-688).

“Cancer patients were confirmed to have cancer by abnormal imaging examination and subsequent tissue biopsy confirmation of malignancy. Cancer stages were determined by the TNM (Tumor, Node, Metastasis) system classification according to the American Joint Committee on Cancer and the International Union for Cancer Control. Our study only recruited cancer patients with non-systemic-metastatic stages (Stage I-IIIA) in which cancer is localized to the primary sites and has not spread to other organs. We excluded patients who were diagnosed with metastatic stage IIIB and IV cancer. All healthy subjects were confirmed to have no history of cancer at the time of enrollment. They were followed up at six months and one year after enrollment to ensure that they did not develop cancer.”

“For patients with unavailable staging information, their initial imaging examinations were conducted at the study hospitals. However, subsequent tests and surgical procedures were performed at a different hospital, as per the patients' preferences. Consequently, the original study hospitals lacked access to comprehensive tumor staging data. To address this limitation, the metastasis status of these patients was obtained via communication channels between the clinicians at the study hospitals and those at the surgery hospitals. This enabled the retrieval of limited information, adhering to an established data-sharing agreement between the two institutions. To maintain the robustness of our analysis, patients diagnosed with metastatic cancer or those with indeterminate metastatic status were subsequently excluded from the study.”

3) It seems that one of the important advantages of this new model is the low depth coverage in comparing to previous screening models for cancer. The authors should discuss more on the reason why the new model could achieve comparable predictive accuracy with an obviously lower sequencing depth.

We thanked the reviewer for the suggestion. We have added the following sentences in the discussion to explain why our assay could achieve good performance at low depth sequencing. (Line 571-584)

“However, the low amount of ctDNA fragments in plasma samples of patients with early-stage cancer as well as the molecular heterogeneity of different cancer types are known as the major challenges for liquid biopsy based multi-cancer detection assays. Thus, sequencing at high depth coverages is required to capture enough informative cancer DNA fragments in the finite plasma sample to achieve early cancer detection. In support to this notion, many groups (1-4) have developed assays that exploited high depth coverage of sequencing to detect ctDNA fragments in plasma of early stage cancer patients. However, this strategy might not be cost effective and feasible for population wide screening in developing countries. Alternatively, we argued that increasing breadth of ctDNA analysis could maximize the ability to detect ctDNA fragments with heterogeneous genetic and epigenetic changes at shallow sequencing depth, thus improving the sensitivity for multicancer detection. To demonstrate the feasibility of this approach, we built a stacking ensemble model to combine nine different ctDNA signatures and demonstrated its superior performance on cancer detection in comparison to single-feature models (Figure 7B and 7C).”

4) The readability of this manuscript needs to be improved. The focus of the background section is not clear, with too much detail of other studies and few purposeful summaries. You need to explain the goals and clinical significance of your study. In addition, the results section is too long, and needs to be shortened and simplified. Move some of the inessential results and sentences to supplementary materials or methods.

We thank the reviewer for these constructive suggestions. Accrodingly, we have reduced the details of other studies (Line 85-91) as follows:

“In recent years, there has been considerable interest in exploring the potential of ctDNA alterations for early detection of cancer (5, 6). One such approach is the PanSeer test, which uses 477 differentially methylated regions (DMRs) in ctDNA to detect five different types of cancer up to four years prior to conventional diagnosis (7). The DELFI assay employs a genome-wide analysis of ctDNA fragment profiles to increase sensitivity in early detection (1). Recently, the Galleri test has emerged as a multi-cancer detection assay that analyses more than 100,000 methylation regions in the genome to detect over 50 cancer types and localize the tumor site (8).”

We have modified the text in the introduction to explain the goals and clinical significance of our study (Line 111-123)

“In this study, we aimed to expand our multimodal approach, SPOT-MAS, to comprehensively analyze methylomics, fragmentomics, DNA copy number and end motifs of cfDNA and evaluate its utility to simultaneously detecting and locating cancer from a single screening test.” “Our findings demonstrate that the multimodal approach of SPOT-MAS enables profiling of multiple ctDNA signatures across the entire genome at low sequencing depth to detect five different cancer types in their early stages. Beyond detecting the presence of cancer signals, our assay was able to predict the tumor location, which is important for clinicians to fast-track the follow-up diagnostic and guide necessary treatment. Thus, SPOT-MAS has the potential to become a universal, simple, and cost-effective approach for early multi-cancer detection in a large population.”

Reviewer #2 (Public Review):

The authors tried to diagnose cancers and pinpoint tissues of origin using cfDNA. To achieve the goal, they developed a framework to assess methylation, CNA, and other genomic features. They established discovery and validation cohorts for systematic assessment and successfully achieved robust prediction power.

1) Still, there are places for improvement. The diagnostic effect can be maximized if their framework works well in early-stage cancer patients. According to Table 1, about 10% of the participants are stage I. Do these cancers also perform well as compared to late stage cancers?

We have performed the comparison of SPOT-MAS performance on different stages and provided the data in Supplementary table S8 and Supplementary Figure S4J and S4L. Our data showed that SPOT-MAS achieved lower sensitivity for detecting stage I and II cancers as compared to stage IIIA cancers in both discovery (61.54% and 69.82% for stage I and II respectively versus 78.67% for stage IIIA, Supplementary table 8) and validation cohort (73.91% and 62.32% for stage I and II, respectively versus 88.31% for stage IIIA, Supplementary table 8). This suggested that cancer stages can influence the performance of our models.

2) Can authors show a systematic comparison of their method to other previous methods to summarize what their algorithm can achieve compared to others.

We have conducted a systematic comparison of our method with others in the Supplementary Table S11.

Reviewer #1 (Recommendations For The Authors):

There are still points for the authors to clarify and consider for incorporation into revision.

• Please first clarify the issues mentioned in "public review". Several complements are needed.

We have addressed all of the reviewer’s comments in “public review”.

1) Line 72-73: Different approaches of early cancer screening assays have different features, application scenarios, and of course, limitations. It's too vague to describe in this way. More importantly, diagnosis of malignancies relies on pathological diagnosis, I don't think the results of unsuccessful screening would be overdiagnosis and overtreatment. That's overstatements.

We have rewritten the statement as follows (Line 72-75)

“Although currently guided screening tests have each been shown to provide better treatment outcomes and reduce cancer mortality, some of them are invasive, thus having low accessibility. Importantly, most of them are single cancer screening tests, which may result in high false positive rates when used sequentially.”

2) Line 115-130: The findings in this study shouldn't be introduced here.

We have removed this section.

3) Line 496-498: It surprised me that the model performed even better in independent validation cohort, which is quite different from the usual situations. Please explain it.

We agree with the reviewer that model performance in independent validation cohort is often lower than in discovery cohort. In our case, we have carefully confirmed our data by utilizing cross-validation (CV). Cross-validation is a widely used process in which the data being used for training the model is separated into folds or partitions and the model is trained and validated for each fold; the performance estimates are then calculated to obtain mean and confidence interval (GraphPad Prism, Wilson/Brown method). To further confirm our findings, we have increased the cross-validation fold into 50, and consistently detected no significant difference in the performance between Discovery and Validation cohorts (p=0.1277, DeLong’s test).

We have added the following sentence in the discussion to explain this (Line 633-635)

“Despite a slightly higher AUC value in the validation cohort compared to the discovery cohort, no significant differences in AUC values were observed between the two cohorts at CV of 10 or 50 (p=0.1277, DeLong’s test).”

4) Line 499-501: For the cut-off value selection, the authors thought that for cancer screening, specificity is more important than sensitivity? It's controversial. The sensitivity is only approximately 70%, I think that a missed diagnosis is even worse.

We agree with the reviewer that both specificity and sensitivity are important metrics of a cancer detection test. However, there is a trade-off between sensitivity and specificity and the preference for either one of them remains a controversial topic. For a screening test, the preference should be determined by considering the prevalence of the disease, in this case - cancer. The low prevalence of cancers indicates that even a small percentage of false-positive test results due to low specificity of the assay, spread across a national population, would hugely increase the demand for confirmatory imaging as well as biopsy sampling of imaging-detected benign abnormalities (9). Thus, false positives have obvious implications for health-care resources as well as patient well-being. Conversely, higher sensitivities will make sure that more cancer cases are detected and avoid delays in diagnosis. To mitigate the impact of insufficient sensitivity of a cancer screening test, it is important to consult the test-takers that current liquid biopsy tests should only be used as a complementary approach to the available diagnosis tests to increase rates of cancer detection. To be used as a stand-alone test, further work is required to improve its performance, with more focus on increasing sensitivity while maintaining high specificity.

We have added the following sentences in the discussion to explain why we set a high threshold of specificity (Line 660-671)

“For an effective screening test, careful consideration of disease prevalence, cancer in this context, is imperative. Given the low prevalence of cancers, even a small proportion of false-positive test results arising from reduced assay specificity, if extrapolated to a national population, could significantly escalate the need for confirmatory imaging and biopsy procedures for benign abnormalities detected during screening. Thus, false-positives can have substantial implications for both healthcare resources and patient well-being. Conversely, a screening test with high sensitivity ensures that most cancer cases are detected and minimizes delays in diagnosis. To address potential limitations posed by low sensitivity in cancer screening tests, we suggest that current liquid biopsy tests should be employed as a complementary approach to existing diagnostic methods to enhance cancer detection rates. To be used a stand-alone test, further work is required to improve its performance, with a particular emphasis on improving sensitivity while preserving high specificity.”

5) The methylation profiles have been used broadly in ctDNA, while your also integrated the fragmentomics, copy number aberration and end motif into the new model. In the discussion section, it would be better to further compare your new model with several previous models based on conventional ctDNA methylation markers (10, 11) for early detection of malignancies. What are the advantages of adding the other two types of data? Why the new model could achieve comparable predictive accuracy with an obviously lower sequencing depth?

We thank the reviewer for the suggestion. We have added the following sentences in the discussion to highlight the novelty of our multimodal approach. (Line 587-610)

“Previous studies have reported that methylation changes at target regions could be exploited for detecting ctDNA in plasma of patients with early-stage cancer (10, 11).”

“In addition to methylation alterations, recent studies have revealed that the DNA copy number, fragmentomics profile (1) and end motif profile (12) at genome wide scales have been shown as useful features for healthy-cancer classification. Therefore, we propose that the combination of these markers might provide added value to increase the performance of liquid biopsy assays. We demonstrated that the same bisulfite sequencing data could be used to identify somatic CNA (Figure 4), cancer-associated fragment length (Figure 5) and end motifs (Figure 6), highlighting the advantage of SPOT-MAS in capturing the broad landscape of ctDNA signatures without high cost deep sequencing. For cancer-associated fragment length, we pre-processed this data into five different feature tables to better reflect the information embedded within the data. Overall, we integrated multiple features of ctDNA including methylation, fragment length, end motif and copy number changes into a multi-cancer detection model and demonstrated that this approach could distinguish healthy individuals with patients from five popular cancer types. This strategy enables increased breadth of ctDNA analysis at shallow sequencing depth to overcome the limitation of low amount of ctDNA fragments in plasma samples as well as molecular heterogeneity of cancers.”

Moreover, we have conducted a systematic comparison of our method with others in the Supplementary Table 11.

6) Line 667-668: The wording should be modest. "Successfully detect and localize" is not appropriate.

We have rewritten the sentence. (Line 713-716)

“Our large-scale case-control study demonstrated that SPOT-MAS, with its unique combination of multimodal analysis of cfDNA signatures and innovative machine-learning algorithms, can detect and localize multiple types of cancer with high accuracy at a low-cost sequencing.”

Reviewer #2 (Recommendations For The Authors):

1) Are the patients and controls all from Vietnam? If I am not mistaken, it is hard to find demographic information for controls. Also it is not clear if samples from controls were processed simultaneously or at a same institution or using the same protocol etc.

We thank the reviewer for asking this question. All cancer patients and controls are from Vietnam, who were recruited from five hospitals including Medic Medical Center, University Medical Center Ho Chi Minh City, Thu Duc City Hospital, National Cancer Hospital and Hanoi Medical University. At each research sites, blood samples from both cancer patients and healthy subjects were collected in in Streck Cell-Free DNA BCT tubes and subsequently transported to a central laboratory located in Medical Genetics Institute for cfDNA isolation, library preparation and sequencing. In a recent publication (10), we have investigated the impact of logistic time and hemolysis rates of blood samples collected from different clinical sites on cfDNA concentration and sequencing quality. We did not observe any noticeable impact of such variations on cfDNA concentrations or sequencing library yields. However, future analytical validation studies are required to evaluate the impact of variation in sampling technique across different clinical sites on the robustness or accuracy of assay results.

We have added the following sentences in the discussion to highlight this important point (Line 696-704)

“At each research sites, blood samples from both cancer patients and healthy subjects were collected in in Streck Cell-Free DNA BCT tubes and subsequently transported to a central laboratory located in Medical Genetics Institute for cfDNA isolation, library preparation and sequencing. In a recent publication (10), we have investigated the impact of logistic time and hemolysis rates of blood samples collected from different clinical sites on cfDNA concentration and sequencing quality. We did not observe any noticeable impact of such variations on cfDNA concentrations or sequencing library yields. However, future analytical validation studies using a larger sample size are required to evaluate the impact of variation in sampling technique across different clinical sites on the robustness or accuracy of assay results.”

References

1. Cristiano S, Leal A, Phallen J, Fiksel J, Adleff V, Bruhm DC, et al. Genome-wide cell-free DNA fragmentation in patients with cancer. Nature. 2019;570(7761):385-9.

2. Cohen JD, Li L, Wang Y, Thoburn C, Afsari B, Danilova L, et al. Detection and localization of surgically resectable cancers with a multi-analyte blood test. Science. 2018;359(6378):926-30.

3. Liu MC, Oxnard GR, Klein EA, Swanton C, Seiden MV. Sensitive and specific multi-cancer detection and localization using methylation signatures in cell-free DNA. Ann Oncol. 2020;31(6):745-59.

4. Stackpole ML, Zeng W, Li S, Liu C-C, Zhou Y, He S, et al. Cost-effective methylome sequencing of cell-free DNA for accurately detecting and locating cancer. Nature Communications. 2022;13(1):5566.

5. Constantin N, Sina AA, Korbie D, Trau M. Opportunities for Early Cancer Detection: The Rise of ctDNA Methylation-Based Pan-Cancer Screening Technologies. Epigenomes. 2022;6(1).

6. Phan TH, Chi Nguyen VT, Thi Pham TT, Nguyen VC, Ho TD, Quynh Pham TM, et al. Circulating DNA methylation profile improves the accuracy of serum biomarkers for the detection of nonmetastatic hepatocellular carcinoma. Future Oncol. 2022;18(39):4399-413.

7. Chen X, Gole J, Gore A, He Q, Lu M, Min J, et al. Non-invasive early detection of cancer four years before conventional diagnosis using a blood test. Nature Communications. 2020;11(1):3475.

8. Jamshidi A, Liu MC, Klein EA, Venn O, Hubbell E, Beausang JF, et al. Evaluation of cell-free DNA approaches for multi-cancer early detection. Cancer Cell. 2022;40(12):1537-49.e12.

9. Ignatiadis M, Sledge GW, Jeffrey SS. Liquid biopsy enters the clinic - implementation issues and future challenges. Nat Rev Clin Oncol. 2021;18(5):297-312.

10. Xu RH, Wei W, Krawczyk M, Wang W, Luo H, Flagg K, et al. Circulating tumour DNA methylation markers for diagnosis and prognosis of hepatocellular carcinoma. Nat Mater. 2017;16(11):1155-61.

11. Luo H, Zhao Q, Wei W, Zheng L, Yi S, Li G, et al. Circulating tumor DNA methylation profiles enable early diagnosis, prognosis prediction, and screening for colorectal cancer. Sci Transl Med. 2020;12(524).

12. Jiang P, Sun K, Peng W, Cheng SH, Ni M, Yeung PC, et al. Plasma DNA End-Motif Profiling as a Fragmentomic Marker in Cancer, Pregnancy, and Transplantation. Cancer Discovery. 2020;10(5):664-73.

Author Response

Pancreatic phenotype reported by Wang et al., 2019 (PMID 30324491)

The reported human knockout of SLC39A5 (homozygous for R311* allele) suggests that SLC39A5 is dispensable for embryonic development with no adverse effect on postnatal pancreatic development or function (Saleheen D, 2017). Indicative of conserved expression and function, Slc39a5 is non-essential in mice, with homozygous or heterozygous deletion of Slc39a5 resulting in elevated serum zinc (Fig. 2) and no resulting impairment in pancreatic development or function (Fig. S3, S4E-F, S5E-F, S6E-F, S7E-F, S8A-H).

The observed antihyperglycemic effects in the Slc39a5 LOF animals were not driven by changes in insulin production and/or clearance (Fig. S3, S4E-F, S5E-F, S6E-F, S7E-F, S8A-H). Our observations related to pancreatic function (both exocrine and endocrine; Fig. 3 and Suppl. Table 3-5) in the Slc39a5 LOF mice are in agreement with reported metabolic phenotyping by the International Mouse Phenotyping Consortium (https://www.mousephenotype.org/data/genes/MGI:1919336). Intriguingly, Wang et al. reported impaired insulin secretion in mice with Ins2-cre mediated deletion of Slc39a5 in β-cell cells (Wang X, 2019). These findings are difficult to interpret in light of single cell RNA-seq analyses of mouse pancreas demonstrating absence of Slc39a5 expression in Ins2+ pancreatic β-cells (The Tabula Muris Consortium, 2018 and 2020). Consistently, SLC39A5 expression in human pancreas is largely restricted to pancreatic acinar and ductal cells (Baron M, 2016; Muraro MJ, 2016; Xin Y, 2016).

Taken together, these observations suggest that the protective metabolic changes are presumably extra-pancreatic in both mouse and human.

Sex Differences:

Slc39a5 LOF activates hepatic AMPK signaling in both sexes, hepatic AKT signaling is elevated in females, suggesting that the observed glucose lowering effects in the Slc39a5 LOF male mice is possibly driven by improvements in extra hepatic glucose metabolism in males or that the magnitude of zinc mediated protein phosphatase inhibition is insufficient to influence the hepatic PI3K/AKT signaling in males. Whether the promotion of hepatic AMPK and AKT signaling occurs solely as a result of zinc mediated inhibition of protein phosphatases or a result of concurrent convergent mechanisms potentially influenced by sex hormones remains to be resolved in future investigations.

Overall, integrated analyses of the metabolic phenotyping in our models (both diet-induced and congenital obesity) are consistent with the well documented sex-dependent susceptibility to obesity-related metabolic alterations such as insulin resistance, hepatic steatosis and dyslipidemia (Goodpaster BH, 2003; Priego T, 2008; Medrikova D, 2012; Bertolotti M, 2014; Frias JO 2001; Krotkiewski M, 1983; Lebeck J, 2016).

Author Response

Reviewer #1 (Public Review):

Medwig-Kinney et al perform the latest in a series of studies unraveling the genetic and physical mechanisms involved in the formation of C. elegans gonad. They have paid particular attention to how two different cell fates are specified, the ventral uterine (VU) or anchor cell (AC), and the behaviors of these two cell types. This cell fate choice is interesting because the anchor cell performs an invasive migration through a basement membrane. A process that is required for correct C. elegans gonad formation and that can act as a model for other invasive processes, such as malignant cancer progression. The authors have identified a range of genes that are involved in the AC/VC fate choice, and that imparts the AC cell with its ability to arrest the cell cycle and perform an invasive migration. Taking advantage of a range of genetic tools, the authors show that the transcription factor NHR-63 is strongly expressed in the AC cell. The authors also present evidence that NHR-63 is could function as a transcriptional repressor through interactions with a Groucho and also a TCF homolog, and they also suggest that these proteins are forming repressive condensates through phase separation.

The authors have produced an extensive dataset to support their two primary claims: that NHR-67 expression levels determine whether a cell is invasive or proliferative, and also that NHR-67 forms a repressive complex through interactions with other proteins. The authors should be commended for clearly and honestly conveying what is already known in this area of study with exhaustive references. But absent data unambiguously linking the formation and dissolution of NHR-67 condensates with the activation of downstream genes that NHR-67 is actively repressing, the novelty of these findings is limited.

Response 1.1: We thank the reviewer for recognizing the extensive dataset we provide in this manuscript in support of our claims that, (1) NHR-67 expression levels are important for distinguishing between AC and VU cell fates, and (2) NHR-67 interacts with transcriptional repressors in VU cells. We acknowledge that a complete mechanistic understanding of the functional significance of NHR-67 puncta is not possible without knowing direct targets of NHR-67 in the AC. Unfortunately, tools to identify transcriptional targets in individual cells or lineages in C. elegans do not exist, and generation of such tools would be beyond the scope of this work. This is evidenced by the fact that the first successful attempt to transcriptionally profile the AC was only posted as a preprint one month ago (Costa et al., doi: 10.1101/2022.12.28.522136). It is our hope that the findings we present here can be integrated with future AC- and VUspecific profiling efforts to provide a more complete picture of the functional significance of NHR-67 subnuclear organization.

Reviewer #2 (Public Review):

Medwig-Kinney et al. explore the role of the transcription factor NHR-67 in distinguishing between AC and VU cell identity in the C. elegans gonad. NHR-67 is expressed at high levels in AC cells where it induces G1 arrest, a requirement for the AC fate invasion program (Matus et al., 2015). NHR-67 is also present at low levels in the non-invasive VU cells and, in this new study, the authors suggest a role for this residual NHR-67 in maintaining VU cell fate. What this new role entails, however, is not clear. The model in Figure 7E shows NHR-67 switching from a transcriptional activator in ACs to a transcriptional repressor in VUs by virtue of recruiting translational repressors. In this model, NHR-67 actively suppresses AC differentiation in VU cells by binding to its normal targets and acting as a repressor rather than an activator. Elsewhere in the text, however, the authors suggest that NHR-67 is "post-translationally sequestered" (line 450) in nuclear condensates in VU cells. In that model, the low levels of NHR-67 in VU cells are not functional because inactivated by sequestration in condensates away from DNA. Neither model is fully supported by the data, which may explain why the authors seem to imply both possibilities. This uncertainty is confusing and prevents the paper from arriving at a compelling conclusion. What is the function, if any, of NHR-67 and so-called "repressive condensates" in VU cells?

Response 2.1: As the reviewer correctly notes, we present two possible models in this manuscript. The interaction between NHR-67 and the Groucho/TCF complex in the VU cells could (1) switch the role of NHR-67 from a transcriptional activator to a transcriptional repressor, or (2) sequester NHR-67 away from its transcriptional targets. Indeed, we cannot definitively exclude the possibility of either model. In our resubmission, we will attempt to make this more clear in the text and by presenting both possible models in the summary figure (Fig. 7E).

Below we list problems with data interpretation and key missing experiments:

1) The authors report that NHR-67 forms "repressive condensates" (aka. puncta) in the nuclei of VU cells and imply that these condensates prevent VU cells from becoming ACs. Fig. 3A, however, shows an example of an AC that also assemble NHR-67 puncta (these are less obvious simply due to the higher levels of NHR-67 in ACs). The presence of NHR-67 puncta in the AC seems to directly contradict the author's assumption that the puncta repress the AC fate program. Similarly, Figure 5-figure supplement 1A shows that UNC-37 and LSY-22 also form puncta in ACs. The authors need to analyze both AC and VU cells to demonstrate that NHR-67 puncta only form in VUs, as implied by their model.

Response 2.2: The puncta formed by NHR-67 in the AC are different in appearance than those observed in the VU cells and furthermore do not exhibit strong colocalization with that of UNC-37 or LSY-22. The Manders’ overlap coefficient between NHR-67 and UNC-37 is 0.181 in the AC, whereas it is 0.686 in the VU cells. Likewise, the Manders’ overlap coefficient between NHR-67 and LSY-22 is 0.189 in the AC compared to 0.741 in the VU cells. We speculate that the areas of NHR-67 subnuclear enrichment in the AC may represent concentration around transcriptional targets, but testing this would require knowledge of direct targets of NHR-67.

2) While a pool of NHR-67 localizes to "repressive condensates", it appears that a substantial portion of NHR-67 also exists diffusively in the nucleoplasm. This would appear to contradict a "sequestration model" since, for such a model to work, a majority of NHR-67 should be in puncta. What proportion of NHR-67 is in puncta? Is the concentration of NHR-67 in the nucleoplasm lower in VUs compared to ACs and does this depend on the puncta?

Response 2.3: The proportion of NHR-67 localizing to puncta versus the nucleoplasm is dynamic, as these puncta form and dissolve over the course of the cell cycle. However, we estimate that approximately 25-40% of NHR-67 protein resides in puncta based on segmentation and quantification of fluorescent intensity of sum Z-projections. We also measured NHR-67 concentration in the nucleoplasm of VU cells and found that it is only 28% of what is observed in ACs (n = 10). We disagree with the notion that the majority of NHR-67 protein should be located in puncta to support the sequestration model. As one example, previously published work examining phase separation of endogenous YAP shows that it is present in the nucleoplasm in addition to puncta (Cai et al., 2019, doi: 10.1038/s41556-019-0433-z). In our system, it is possible that the combination of transcriptional downregulation and partial sequestration away from DNA is sufficient to disrupt the normal activity of NHR-67.

3) The authors do not report whether NHR-67, UNC-37, LSY-22, or POP-1 localization to puncta is interdependent, as implied in the model shown in Fig. 7.

Response 2.4: It is difficult to test whether localization of these proteins to puncta is interdependent, as perturbation of UNC-37, LSY-22, and POP-1 result in ectopic ACs. Trying to determine if loss of puncta results in VU-to-AC transdifferentiation or vice versa becomes a chicken-egg argument. It is also possible that UNC-37 and LSY-22 are at least partially redundant in this context. We based our model, shown in Fig. 7E, on known or predicted protein-protein interactions, which we confirmed through yeast two-hybrid analyses (Fig. 7D; Fig. 7-figure supplement 1).

4) The evidence that the "repressor condensates" suppress AC fate in VUs is presented in Fig. 4D where the authors deplete the presumed repressor LSY-22. First, the authors do not examine whether NHR-67 forms puncta under these conditions. Second, the authors rely on a single marker (cdh-3p::mCherry::moeABD) to score AC fate: this marker shows weak expression in cells flanking one bright cell (presumably the AC) which the authors interpret as a VU AC transformation. The authors, however, do not identify the cells that express the marker by lineage analyses and dismiss the possibility that the marker-positive cells could arise from the division of an ACcommitted cell. Finally, the authors did not test whether marker expression was dependent on NHR-67, as predicted by the model shown in Fig. 7.

Response 2.5: For the auxin-inducible degron experiments, strains contained labeled AID-tagged proteins, a labeled TIR1 transgene, and a labeled AC marker. Thus, we were limited by the number of fluorescent channels we could covisualize and therefore could not also visualize NHR-67 (to assess for puncta formation) or another AC marker (such as LAG-2). We could have generated an AID-tagged LSY-22 strain without a fluorescent protein, but then we would not be able to quantify its depletion, which this reviewer points out is important to measure. We did visualize NHR-67::GFP expression following RNAi-induced knockdown of POP-1 and observed consistent loss of puncta in ectopic ACs. However, this again becomes a chicken-egg argument as far as whether cell fate change or loss of puncta causes the other.

5) Interaction between NHR-67 and UNC-37 is shown using Y2H, but not verified in vivo. Furthermore, the functional significance of the NHR-67/UNC-37 interaction is not tested.

Response 2.6: We attempted to remove the intrinsically disordered region found at the C-terminus of the endogenous nhr-67 locus, using CRISPR/Cas9, as this would both confirm the NHR-67/UNC-37 interaction in vivo and allow us to determine the functional significance of this interaction. However, we were unable to recover a viable line after several attempts, suggesting that this region of the protein is vital.

6) Throughout the manuscript, the authors do not use lineage analysis to confirm fate transformation as is the standard in the field.

Response 2.7: The timing between AC/VU cell fate specification and AC invasion (the point at which we look for differentiated ACs) is approximately 10-12 hours at 25 °C. With our imaging setup, we are limited to approximately 3-4 hours of live-cell imaging. Therefore, lineage tracing was not feasible for our experiments. Instead, we relied on visualization of established markers of AC and VU cell fate to determine how ectopic ACs arose. In Fig. 6B,C we show that the expression of two AC markers (cdh-3 and lag-2) turn on while a VU marker (lag-1) get downregulated within the same cell. In our opinion, live-imaging experiments that show in real time changes in cell fate via reporters was the most definitive way to observe the phenotype.

There are 4 multipotential gonadal cells with the potential to differentiate into VUs or ACs. Which ones contribute to the extra ACs in the different genetic backgrounds examined was not determined, which complicates interpretation. The authors should consider and test the following possibilities: disruption of NHR-67 regulation causes 1) extra pluripotent cells to directly become ACs early in development, 2) causes VU cells to gradually trans-fate to an AC-like fate after VU fate specification (as implied by the authors), or 3) causes an AC to undergo extra cell division(s)?? In Fig. 1F, 5 cells are designated as ACs, which is one more that the 4 precursors depicted in Fig. 1A, implying that some of the "ACs" were derived from progenitors that divided.

Response 2.8: When trying to determine the source of the ectopic ACs, we considered the three possibilities noted by the reviewer: (1) misspecification of AC/VU precursors, (2) VU-to-AC transdifferentiation, or (3) proliferation of the AC. We eliminated option 3 as a possibility, as the ectopic ACs we observed here were invasive and all of our previous work has shown that proliferating ACs cannot invade and that cell cycle exit is necessary for invasion (Matus et al., 2015; MedwigKinney & Smith et al., 2020; Smith et al., 2022). Specifically, NHR-67 is upstream of the cyclin dependent kinase CKI-1 and we found that induced expression of NHR-67 resulted in slow growth and developmental arrest, likely because of inducing cell cycle exit. For our experiment using hsp::NHR-67, we induced heat shock after AC/VU specification. For POP-1 perturbation, we explicitly acknowledged that misspecification of the AC/VU precursors could also contribute to ectopic ACs (Fig. 6A; lines 368-385). We could not achieve robust protein depletion through delayed RNAi treatment, so instead we utilized timelapse microscopy and quantification of AC and VU cell markers (Fig. 6B,C; see response 2.7 above).

In conclusion, while the authors report on interesting observations, in particular the co-localization of NHR-67 with UNC-37/Groucho and POP-1 in nuclear puncta, the functional significance of these observations remains unclear. The authors have not demonstrated that the "repressive condensates" are functional and play a role in the suppression of AC fate in VU cells as claimed. The colocalization data suggest that NHR-67 interacts with repressors, but additional experiments are needed to demonstrate that these interactions are specific to VUs, impact VU fate, and sequester NHR-67 from its targets or transform NHR-67 into a transcriptional repressor.

Response 2.9: We agree that, at this time, we cannot pinpoint the precise mechanism through which NHR-67 puncta function (i.e., by sequestering NHR-67 from DNA or switching the role of NHR-67 from activating to repressing). However, identification of NHR-67 puncta and their colocalization with UNC-37, LSY-22, and POP-1 in VU cells allowed us to discover an undescribed role for the Groucho/TCF complex in maintaining VU cell fate. This, combined with our evidence demonstrating that NHR-67 transcriptional regulation is important for distinguishing between AC and VU cell fate, are the main contributions of our study.

Reviewer #1 (Recommendations For The Authors):

I am not a C. elegans researcher and I find this paper fairly hard to follow. One major recommendation I would like to see is to improve the consistency of the labeling of the figures. There are many figures showing many things and I struggled to keep track of everything. For example, the thing that we are looking at in the microscope images (typically GFP tagged to a protein of interest) is sometimes labeled above the image, sometimes to the side, and sometimes within the panel. Experimental conditions are also formatted arbitrarily. As much as they can do so, could the authors try and make their labeling consistent? This would help me follow the data.

Response 1.2: We thank the reviewer for this suggestion and have reorganized the figures (namely Figure 3, Figure 4, Figure 4–figure supplement 1, Figure 5, and Figure 6) such that the tagged allele or marker is labeled at the top, and the time, stage, and/or perturbation is labeled on the side.

Is the yeast one-hybrid assay enough to confirm a direct interaction between HLH-2 and NHR-67? Obviously, it supports it, but since this is not a definitive test in C. elegans, I feel the description of this result should be modified to account for this.

Response 1.3: We agree that the yeast one-hybrid assay identifies sequences that are capable of being bound to a protein and does not prove that a DNA-protein interaction occurs in vivo. We have modified our language describing this result in our resubmission (lines 222-224).

NHR-67 and POP-1 eventually form two large spots. This observation supports the claims that these are condensates, but it is clearly different from the observations in Ciona where the condensates remain more or less stable until they quickly dissolve at the onset of mitosis. Do the authors have any idea why these condensates are behaving this way? Is it always two spots? This implies it is forming around some sort of diploid nuclear structure.

Response 1.4: Hes.a puncta observed in Ciona were indeed shown to be dynamic, as puncta were captured fusing together (see Figure 6B of Treen et al., 2021). However, these puncta did not appear to coalesce into two puncta specifically, as is consistently observed with NHR-67 in C. elegans. We agree with the reviewer in that this observation is very interesting and likely correlates to a diploid nuclear structure, however we have yet to identify this.

In Ciona, for the two examples of repressive condensates, it was shown that the removal of the C-terminal Groucho recruiting repressor domains of HesA end ERF disrupts condensate formation. Have the authors attempted a similar experiment for NHR-67 or Pop1?

Response 1.5: We agree that this would have been an ideal experiment to perform. We attempted to remove the intrinsically disordered region found at the C-terminus of NHR-67 with CRISPR, but were unable to generate a stable line, suggesting that this region may be critical for NHR-67 function in other developmental stages or tissues.

Other minor points:

Fig 4D - I found the labeling of this figure the most confusing.

Response 1.6: We thank the reviewer for bringing this to our attention. For this panel, in addition to the changes we made reference above (Response 1.2), we simplified the labeling of the TIR1 transgene and instead reference it in the figure legend for simplicity.

Line 354 - I think this is mislabeled. Is it supposed to be Figure 5H, not 5F, and 5B, not 5C?

Response 1.7: We thank the reviewer for spotting this error. This reference to Figure 5F has been updated and now correctly references Figure 5H (line 338).

Reviewer #2 (Recommendations For The Authors):

The authors use several methods to overexpress NHR-67 including 1) an NHR-67 transgene (Fig. 1), 2) overexpression of the transcriptional activator HLH-2 or 3) removal of a factor that normally degrades HLH-2 in VU cells (Fig. 2). In all cases, the rate of VU AC transformation is either very low (5%) or not reported but presumed to be zero, since other groups have done similar experiments and reported no such conversion (eg. Benavidez et al., 2022). What is the significance of this finding? Does this mean that high levels of NHR-67 are not sufficient to promote AC fate because NHR-67 is sequestered in puncta when expressed in VU cells? Fig. 2A suggests that NHR-67 is in puncta in all VUs where overexpressed. Would the inactivation of GROUCHO in that background result in extra ACs?

Response 2.10: Indeed, we would expect that overexpression of NHR-67 may not normally be sufficient to induce cell fate transformation if the Groucho/TCF complex is still functional. Unfortunately we were unable to achieve strong depletion of UNC-37 and LSY-22 through RNAi, and thus relied on the auxin-inducible protein degradation system. Since we are limited by the number of fluorescent channels we can co-visualize, it would not be feasible to combine a heat-shock inducible transgene, a TIR1 transgene, an AID-tagged protein, and multiple cell fate markers.

The data are often presented as numbers of animals with increased or decreased expression of a particular marker, but no quantification of expression is provided. For example, in Figure 1E, 32/35 animals are reported to exhibit ectopic expression of LIN-12 in the AC and reduced expression of LAG-2. What is the range of the increase/decrease in LIN-12/LAG-2 expression and how does this compare to natural variation in wild-type? The same concerns apply to Fig. 4D.

Response 2.11: For resubmission, we have quantified the data shown in Figure 1E and now report expression levels of LIN-12::mNeonGreen and LAG-2::P2A::H2B::mTurquoise2 in Figure 1–figure supplement 2. We have also quantified the data in Figure 4D and now report expression levels of cdh-3p::mCherry::moeABD in Figure 4E. Quantification methods have been added to the Materials and Methods section (lines 612-617).

The authors explain that it is difficult to study a repressive role for POP-1 as this protein functions in multiple developmental pathways and POP-1 depletion needs to be carefully timed for the data to be interpretable. The authors then go on to use RNAi to deplete POP-1 but do not describe in the methods how they achieve the needed precise temporal control.

Response 2.12: We did indeed describe methods for the GFP-targeting nanobody, which we expressed under a uterinespecific promoter expressed after AC/VU specification. However, since the penetrance of phenotypes associated with this perturbation was low, we utilized RNA interference. We separated the cell fate specification and cell fate maintenance phenotypes by visualizing AC markers (Fig. 6A), which we would expect to be expressed at equal levels if ACs adopted their fate at the same time (via misspecification). We also paired these with a marker for VU cell fate and co-visualized them over time (Fig. 6B,C).

The authors also do not report the efficiency of protein depletion by RNAi or Auxin treatment.

Response 2.13: Auxin-induced depletion of mNeonGreen::AID::LSY-22 resulted in more than 90% decrease in expression (n > 75 uterine cells). The AID-tagged allele for UNC-37 was labeled with BFP, which was barely detectable by our imaging system and photobleached very quickly, so we did not quantify its depletion. However, considering that UNC37 and LSY-22 are both expressed fairly uniform and ubiquitously, and that LSY-22 is expressed at higher levels than UNC-37 at the L3 stage according to WormBase (31.9 FPKM vs. 23.5 FPKM), we would predict that its auxin-induced depletion would be just as potent if not moreso.

Some of the work presented repeats previously published observations, and it is difficult at times to keep track of what is confirmatory and what is new. For example, this group already published on the enrichment of HLH-2 and NHR-67 in the AC, as well as the positive regulation of NHR-67 by HLH-2 (Medwig-Kinney et al 2020). Additionally, prior papers have already reported the interaction between HLH-2 and the nhr-67 locus.

Response 2.14: The work presented in this manuscript does not repeat any previously published experiments. When we introduced the endogenously tagged NHR-67 and HLH-2 strains in previous work (Medwig-Kinney & Smith et al., 2020), we quantified expression of these proteins in the AC over time but did not compare expression between the AC and VU cells. Additionally, we previously showed that HLH-2 positively regulates NHR-67 in the AC (Medwig-Kinney & Smith et al., 2020), but never showed this is the case in the VU cells. Considering that this regulatory interaction was not observed in the AC/VU cell precursors, we believe that determining whether these proteins interact in the context of the VU cells was a valid question to address.

Treen et al. 2021 are cited as prior evidence for the existence of "repressive condensates", however, that study does NOT experimentally demonstrate a function for these structures.

Response 2.15: By “repressive condensates” we are referring to condensation of proteins known to be transcriptional repressors. While we agree that we were not able to demonstrate transcriptional repression of specific loci, our data showing that perturbation of the Groucho repressors UNC-37 and LSY-22 results in ectopic ACs is consistent with the hypothesis that these proteins repress the default AC fate. We have modified our title and text to more clearly distinguish our interpretations versus speculations.

Author Response

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

Reviewer #1 (Public Review):

This manuscript by Leibinger et al describes their results from testing an interesting hypothesis that microtubule detyrosination inhibits axon regeneration and its inhibitor parthenolide could facilitate axon regeneration and perhaps functional recovery. Overall, the results from in vitro studies are largely well performed. However, the in vivo data are less convincing.

Interpretation of the findings in this study are limited by several gaps:

1) It is unclear whether microtubule detyrosination a primary effect of hIL-6 and PTEN deletion or secondary to the increased axon growth?

This point is based on a misunderstanding, as shown in Fig. 2 by Western blot, that detyrosination was increased after intravitreal injection of AAV2-hIL-6 into optic nerves. These optic nerves were uninjured! This indicates that the increased detyrosination is an effect of the treatment itself and does not occur due to axonal regeneration.

Why hIL-6 and PTEN nevertheless increase axonal regeneration is because the positive effect on other signaling pathways, such as JAK/STAT3 and mTOR, ultimately predominates. Consequently, we show, for both PTEN ko and hIL-6, that we can further enhance these positive effects by neutralizing the negative aspect of increased detyrosination using DMAPT.

2) Is there any direct evidence for Akt and/or JAK/Stat3 to promote microtubule detyrosination?

Regarding the AKT/GSK3 signaling pathway, it has been well described that GSK3 activity leads to phosphorylation of microtubule-associated protein 1B, which results in enhanced tubulin detyrosination (Lucas et al., 1998, Goold et al 1999, Owen and Gordon-Weeks 2003). As shown in our previous and cited work, hIL-6 promotes the activation of AKT, which in turn inhibits GSK3 (Leibinger et al. 2016). In Fig. 2, we have also shown that intravitreal hIL-6 treatment in the optic nerve leads to increased inhibitory phosphorylation of GSK3 at the target site of AKT, and that tubulin detyrosination is increased. The same was also shown for PTEN ko: In a previous publication, we showed that PTEN ko increases AKT activity, inhibiting GSK3 phosphorylation (Leibinger et al. 2019). In Fig. 3 of the actual study, we show that PTEN ko results in enhanced tubulin detyrosination. In conclusion, treatments activating the AKT/GSK3 signaling enhance tubulin detyrosination.

On the other hand, JAK/STAT3 has no direct effect on detyrosination. This was demonstrated in experiments using the CNTF application, which reportedly activates the JAK/STAT3 pathway without affecting AKT/GSK3 (Leibinger et al, 2009, 2016, 2017).

In cell culture, we have shown that activation of the JAK/STAT3 pathway by CNTF does not change tubulin detyrosination in neurites (Fig. 1 H, I, M; N). Moreover, DMAPT in RGC’s cell bodies does not affect the phosphorylation of STAT3 and S6, and thus has no measurable effect on JAK/STAT3 or the mTOR pathway.

3) What is the impact of parthenolide on cell soma of neurons and other cell types?

Parthenolide and DMAPT show a regenerative effect in the nanomolar range (cell culture) and a bell-shaped concentration-response curve. We show a close correlation between detyrosinated microtubules and regeneration (with and without hIL-6 or PTEN-KO), which is, in our opinion, convincing. Moreover, we would like to address a likely misunderstanding in this comment and provide further clarification. The detyrosination of alpha-tubulin occurs after its attachment to microtubules through the action of the tubulin carboxy peptidase vasohibin 1 and 2 (Vash 1, 2). Consequently, tubulin is already present in the detyrosinated form within existing microtubules, and the administration of DMAPT does not affect these pre-existing microtubules. However, DMAPT does play a crucial role in preventing the detyrosination of newly attached tubulin dimers in the growth cones of developing axons. This explains why we can detect detyrosinated tubulin specifically in those regions and why our immunohistochemical analyses in the cell culture experiments focused solely on axon tips.

It is important to note that when used at low concentrations, which promote axon growth, DMAPT does not measurably affect detyrosination in other neuronal compartments, such as the RGCs' somata. We might observe a decrease in detyrosination only at much higher concentrations. However, this outcome would be inconsequential to our findings.

Whether additional effects of DMAPT contribute to improved regeneration is not excluded, although unlikely. If so, their investigation would be beyond the scope of the current paper.

4) Direct evidence that parthenolide augments PTEN deletion in optic nerve or spinal cord is not provided.

Our research paper primarily investigates the combination of DMAPT with h-IL-6. We chose to combine DMAPT with hIL-6 because, unlike PTEN-KO, only hIL-6 has been demonstrated to facilitate functional recovery following a complete spinal cord crush injury (Leibinger et al., 2021). Therefore, it is unclear why conducting in vivo experiments with PTEN-KO would be necessary, which cannot be used therapeutically. Since we have shown the beneficial effects of DMAPT on hIL-6 in two different in vivo models (optic nerve and spinal cord) anatomically and functionally, we feel that the repetition of these experiments with PTEN ko, which has no therapeutic implication, would not justify the sacrifice of additional animals. This would contradict the principles of reduction, refinement, and replacement, aiming to minimize the use of animals in our research.

In contrast, the PTEN experiments primarily serve to support the underlying mechanism and demonstrate that DMAPT generally counteracts the negative effect on MT detyrosination, even in conjunction with other procedures that activate the PI3K/AKT pathway. These findings were mechanistically elucidated through cell culture experiments utilizing immunohistochemial analysis, which the editors highlighted as strengths of our paper.

5) Serotonergic neurotoxin DHT ablates both regenerating and non-regenerating serotonergic axons, which makes spinal cord findings it difficult to interpret.

The impact of unregenerated serotonergic axons on stereotypic hind leg movements, as assessed through BMS analysis, appears to be minimal, as demonstrated in our previous study (Leibinger et al., 2021). Specifically, our findings revealed that depleting serotonergic neurons using DHT did not significantly affect the BMS score in uninjured animals (Leibinger et al., 2021). Furthermore, even in the control group comprising animals with spinal cord lesions where anatomical regeneration of the RpST did not occur, the administration of DHT had no discernible effect (Fig. 7 K, L).

To address this concern, we included the following information in the revised manuscript: "It might be considered plausible that the depletion of non-regenerated serotonergic axons could have contributed to these results. However, we can largely dismiss this possibility, as DHT did not influence the non-regenerated vehicle control group. Additionally, in a previous publication, we have demonstrated that the general depletion of serotonergic neurons in uninjured animals also does not significantly impact open field locomotion, as measured by the BMS score and subscore (Leibinger et al., 2021)."

6) DMAPT was given by i.p. injection. What happens to microtubule detyrosination in other cells within and outside of CNS?

This question is the same as raised under point 3. -> response see 3.

Reviewer #2 (Public Review):

In the current study, Fischer and colleagues extensively examined the role of parthenolide in inhibiting microtubule detyrosination and making the mechanistic link for the compound to facilitate the role of IL6 and PTEN/KO in promoting neurite outgrowth and axon regeneration. The in vitro and mechanistic work laid the foundation for the authors to reach several key predictions that such detyrosination can be applied for in vivo applications. Thus the authors extended the work to optic nerve regeneration and spinal cord recovery. The in vivo compound that the authors utilized is DMAPT, which plays a synergistic role with existing pro-regeneration therapies, such as Il6 treatment.

The major strength of the work is the first half of the mechanistic inquiries, where the authors combined cell biology and biochemistry approaches to dissect the mechanistic link from parthenolide to microtube dynamics. The shortcoming is that the in vivo data is limited, and the effects might be considered mild, especially by benchmarking with other established and effective strategies.

The work is solid and prepares a basis for others to test the role of DMAPT in other settings, especially in the setting of other effective pro-regenerative approaches. With the goal of comprehensive and functional recovery in vivo, the impact of the work and the utilities of the methods remain to be tested broadly in other models in vivo.

Reviewer #3 (Public Review):

The primary goal of this paper is to examine microtubule detyrosination as a potential therapeutic target for axon regeneration. Using dimethylamino-parthenolide (DMAPT), this study extensively examines mechanistic links between microtubule detyrosination, interleukin-6 (IL-6), and PTEN in neurite outgrowth in retinal ganglion cells in vitro. These findings provide convincing evidence that parthenolide has a synergistic effect on IL-6- and PTEN-related mechanisms of neurite outgrowth in vitro. The potential efficacy of systemic DMAPT treatment to promote axon regeneration in mouse models of optic nerve crush and spinal cord injury was also examined.

Strengths

1) The examination of synergistic activities between parthenolide, hyperIL-6, and PTEN knockout is leveraged not only for potential therapeutic value, but also to validate and delineate mechanism of action.

2) The in vitro studies, including primary human retinal ganglion cells, utilize a multi-level approach to dissect the mechanistic link from parthenolide to microtubule dynamics.

3) The studies provide a basis for others to test the role of DMAPT in other settings, particularly in the context of other effective pro-regenerative approaches.

Weaknesses

1) In vivo studies are limited to select outcomes of recovery and do not validate or address mechanism of action in vivo.

Reviewer #1 (Recommendations For The Authors):

Overall, it doesn't seem like the authors bought into or addressed any issues raised during the previous review. In testing their central hypothesis, a critical experiment was to assess the outcome of PTEN knockout in combination with their novel treatment (parthenolide or DMAPT). Unfortunately, this and other issues have not been addressed in this revision.

PTEN is not part of our central hypothesis. Our research paper primarily investigates the combination of DMAPT with h-IL-6. We chose to combine DMAPT with hIL-6 because, unlike PTEN-KO, only hIL-6 has been demonstrated to facilitate functional recovery following a complete spinal cord crush injury (Leibinger et al., 2021). Therefore, it is unclear why conducting in vivo experiments with PTEN-KO would be necessary, which cannot be used therapeutically. Since we have shown the beneficial effects of DMAPT on hIL-6 in two different in vivo models (optic nerve and spinal cord) anatomically and functionally, we feel that the repetition of these experiments with PTEN ko, which has no therapeutic implication, would not justify the sacrifice of additional animals. This would contradict the principles of reduction, refinement, and replacement, aiming to minimize the use of animals in our research.

In contrast, the PTEN experiments primarily serve to support the underlying mechanism and demonstrate that DMAPT generally counteracts the negative effect on MT detyrosination, even in conjunction with other procedures that activate the PI3K/AKT pathway. These findings were mechanistically elucidated through cell culture experiments utilizing immunohistochemial analysis, which the editors highlighted as strengths of our paper.

Reviewer #2 (Recommendations For The Authors):

The response and revision provided here did not improve the manuscript - the authors chose to focus on re-organizing the methods but did not provide any new experimental data. Thus my recommendations remain the same as the previous round. In brief, the in vivo evidence was rather weak, especially if no further evidence was offered to respond to these points below.

To possibly improve the manuscript, the authors could consider enhancing the in vivo parts in the following manner;

1) possibly detyrosination staining in the optic nerve vertical section - it would be interesting to see how the detyrosination assays may work for regenerating conditions, or as an alternate, the authors may consider retina tissue biochemistry (with & without IL6, with & without DMAPT) repeating the biochemical assays as established Fig 2B –

The detyrosination of alpha-tubulin occurs after its attachment to microtubules through the action of the tubulin carboxy peptidase vasohibin 1 and 2 (Vash 1, 2). Consequently, tubulin is already present in the detyrosinated form within existing microtubules, and the administration of DMAPT does not affect these pre-existing microtubules. However, DMAPT does play a crucial role in preventing the detyrosination of newly attached tubulin dimers in the growth cones of developing axons. This explains why we can detect detyrosinated tubulin specifically in those regions and why our immunohistochemical analyses in the cell culture experiments focused solely on axon tips.

It is important to note that when used at low concentrations, which promote axon growth, DMAPT does not measurably affect detyrosination in other neuronal compartments, such as the RGCs' somata. We might observe a decrease in detyrosination only at much higher concentrations. Because of these reasons, we could not clearly identify and stain axon tips in 14 µm thick optic nerve sections.

2) How do the authors benchmark the DMAPT retreatment in the setting of PTEN (aav2-cre injection for cKO) and /or PTEN/SOCS3/CNTF dKO? Which are the best approaches to promote optic nerve regeneration? Would the authors expect DMAPT retreatment to be synergetic with PTENcKO?

Based on our previous findings, we anticipate that DMAPT would exhibit a synergistic effect when combined with PTEN ko, as demonstrated in our in vitro studies with cultured neurons. Additionally, synergistic effects between DMAPT and PTEN/SOCS3 dKO +CNTF are possible. While these hypotheses hold promise, our current paper primarily focuses on combining DMAPT with hIL-6, which has consistently shown remarkable efficacy as a standalone treatment in optic nerve regeneration.

3) Regarding the DMAPT treatment, one notable issue was that the RGC survival subject to ONC was very poor, which may limit the effects of DMAPT daily injection. The authors may consider further combining DMAPT with the DLK/LZK inhibitors to examine the synergistic effects.

As DMAPT itself is not neuroprotective and does not affect retinal ganglion cells' (RGCs) regenerative state by inducing the expression of regeneration-associated genes, a combination with a neuroprotective and regenerative treatment would show stronger effects. This is exactly what we found when combining DMAPT with neuroprotective hIL-6 (Leibinger et al. 2016) in the current paper.

Moreover, in the raphespinal tract, where respective neurons do not undergo apoptotic cell death after axotomy, the DMAPT effect on anatomic axon regeneration was stronger than in the optic nerve, even without combination with hIL-6, with some axons reaching distances of up to 7 mm distal to the lesion. So, DMAPT can induce long-distance regeneration in neuronal populations unaffected by cell death. Therefore, additional experiments with DLK/LZK inhibitors, as suggested by this reviewer, would not provide an additional benefit to our paper and would not justify the additional sacrifice of animal lives.

4) Overall, the phenotypes in Figs 5-8 were rather weak after DMAPT treatment, which are universal challenges to spinal cord regeneration. The authors may present this section of the data with further clarification on the selection standards in the methods, such as how the animals and treatment were selected and how a double-blinded experimental design may help further evaluate the effects of DMAPT treatment. I found little relevant information in the current manuscript.

In the anatomic and functional regeneration analysis presented in Fig. 5-8, we only included animals with a BMS score of 0 one day after the spinal cord crush, indicating a complete absence of hind leg movement. Furthermore, we employed immunohistochemical staining to ensure that no serotonergic axons were detected at 8-10 mm from the lesion site in any of the animals, thus confirming the thoroughness of the lesion (Supplementary Fig. 4). Both the evaluation of the BMS score and the assessment of anatomical regeneration was conducted in a double-blinded manner, ensuring unbiased and objective observations. To address this concern, we will add the following paragraph in the M&M part:

“Blinding procedure for in vivo experiments Before the start of the experiment, individual vials containing DMAPT or vehicle (DMSO) stock solution were prepared for each particular experimental animal. The vials were randomized by a person who was neither involved in the implementation nor in the evaluation of the experiments. These numbers were randomly distributed to mice of the same age and sex in different cages. This was carried out independently by another person who was neither involved in the data evaluation nor the randomization of the samples. This was followed by the execution of the experiments and the evaluation by scientists who were not involved in any of the randomization processes and did not know the identity of the injected samples. After completion of the data collection, values from mice with signs of spared axons were first removed from the data set for reasons of quality assurance. The criteria for this were a BMS-Sore of a maximum of 0-1 on the first day after the lesion and the absence of uninjured serotonergic axons in spinal cord cross-sections >8-10 mm distal to the lesion site. Finally, the data points were assigned to the respective experimental groups by the person who initially blinded the vials.”

Reviewer #3 (Recommendations For The Authors):

Addition of supporting data, revision of discussion, and inclusion of references for parthenolide activities improved the manuscript and adequately addressed concerns

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

We feel that the use of human RGCs should be considered a highlight and strength of our paper because, as far as we know, our study is the first to utilize human primary cultures of RGCs to confirm the effectiveness of drugs on human cells. Therefore, this might be of interest to colleagues in our field. Moreover, we have added additional data as suppl. Fig. proving that these cells are living RGCs so this concern has been addressed. In addition, we provide further explanations why other activities of DMAPT beyond microtubule detyrosination, such as oxidative stress and NFkB inhibition, are not considered in experimental examinations or in the interpretation of findings. Therefore, we strongly recommend that this point should not be considered a weakness.<br />

Strengths:

1) The examination of synergistic activities between parthenolide, hyper-IL-6, and PTEN knockout is leveraged not only for potential therapeutic value, but also to validate and delineate mechanism of action.

2) The in vitro studies utilize a multi-level approach that combines cell biology and biochemistry approaches to dissect the mechanistic link from parthenolide to microtubule dynamics.

3) The studies provide a basis for others to test the role of DMAPT in other settings, particularly in the context of other effective pro-regenerative approaches.

Weaknesses:

1) In vivo studies are limited to select outcomes of recovery and do not validate or address mechanism of action in vivo.

2) Known activities of DMAPT beyond microtubule detyrosination, such as oxidative stress, mitochondrial function and NFkB inhibition, are not considered in experimental examinations or in the interpretation of findings.

Our research indicates that parthenolide exhibits a regenerative effect within a nanomolar range and with a bell-shaped concentration-response curve in culture. Moreover, we demonstrate a close correlation between the inhibition of detyrosinated microtubules and regeneration and consider the effects of hIL-6 or PTEN-KO on detyrosination in mouse and human RGCs. Therefore, we offer a coherent and satisfactory mechanistic explanation for the effects of parthenolide. We, therefore, feel the request to experimentally explore additional, somewhat speculative possibilities is not reasonable or helpful, and this issue should not be considered as a weakness. Moreover, to the best of our knowledge, no evidence suggests profound antioxidative effects of DMAPT or parthenolide within these low-concentration ranges and that these would affect axon regeneration. Antioxidative effects may also not explain the observed bell-shaped curve. Furthermore, we have already considered the effect of NFkappaB in our previous work (Gobrecht et al., 2016) and shown that NFkappaB remains unaffected by low concentrations of parthenolide. Hence, conducting additional experiments addressing oxidative stress or other speculative causes will not strengthen our findings and do not justify the additional sacrifice of animal lives.

Nevertheless, we added the following sentence in our manuscript to address this issue: “Although we cannot exclude the possibility that other known activities of parthenolide/DMAPT, such as oxidative stress or NF-kB inhibition, could have contributed to the observed effects, this is rather unlikely because such effects have only been reported at much higher micromolar concentrations (Bork et al., 1997; Saadane et al., 2007; Carlisi et al., 2016; Gobrecht et al., 2016).”

Editorial Comments:

The reviewers' consensus is that this manuscript, although containing an impressive amount of data, lacks cohesion.

The mechanistic studies in vitro are of a distinctly different caliber than the in vivo studies. Additional data is needed to demonstrate that the mechanisms delineated in vitro are related to the outcomes in vivo. As is, this reads as a comprehensive in vitro study with premature in vivo data tacked on the end.

The manuscript should contain the necessary background and contextual information needed to fully understand the work. Clarity of rationale and context for experimental method/design (why one reagent or insult is selected over another), result interpretation (what does this data tell you and not tell you), and implications for results (what does this mean in the context of current knowledge) should be improved throughout.

Technical:

1) There is no validation of human RGC cultures. If this data is to remain in the manuscript, proper verification data should be provided to demonstrate that these are indeed RGCs and that they are viable.

The retinal ganglion cells (RGCs) were identified by applying the same criteria as murine and rat RGCs,encompassing morphological and immunohistochemical criteria. The staining of a piece of human retina (see Author response image 1) shows βIII-tubulin-positive cells in the ganglion cell layer and forming axonal bundles in the fiber layer. These are RGCs, and it is confirmed that the βIII-tubulin antibody stains human RGCs (Author response image 1A). In addition, the somata of these human RGCs in the retina have a similar diameter (somewhat larger than murine RGCs Author response image 1A, B) to the cultured βIII-tubulin-positive cells (RGCs) and a similar morphology. Finally, these regenerating neurons are GAP43-positive, a regeneration-associated protein shown in Author response image 1C. Thus, these data prove that the cultured cells were human RGCs. These data were included as a suppl. Fig. 1.

The viability of the neurons was confirmed, as evidenced by their ability to grow neurites - a clear indication of their vitality. We also verified the viability by calceinstaining.

As far as we know, our study is the first to utilize human primary cultures of RGCs to confirm the effectiveness of CNTF and parthenolide on human cells. Therefore, we would have expected this accomplishment to be emphasized as a strength of our paper.

Author response image 1.

A) Retinal flat mounts from human (left) and mouse (right) stained for βIII-tubulin. Scale bar: 50 μm. B) Human (left) and mouse (right) RGCs cultured for 4 days and stained for βIII-tubulin. Scale bar: 25 μm. C) Human βIIItubulin-positive RGCs with regenerating neurites are also GAP43-positive. Scale bar: 50 μm

2) For graphs depicting means and errors, it is advised that the authors evaluate their use of SEM. Standard deviation should be used when illustrating the distribution of measurements/individuals within a population. Standard error should be used for determining accuracy of the calculated mean, i.e. how close are individuals to the calculated mean? Since standard error is a measure of accuracy rather than distribution, it moves towards zero as the population size increases, regardless of the distribution. Thus, error bars intended to show the range of an effect (i.e. how much functional recovery with treatment?), should be depicted as standard deviation, which illustrates the actual range of data.

To provide best possible transparency we incorporated each individual data point within our graphs, thus offering a detailed depiction of the complete range of effects. We firmly believe that this approach provides enhanced clarity compared to a standard deviation and grants a more comprehensive understanding of the data. It is worth noting that also presenting the standard error adds supplementary information regarding the accuracy of the calculated mean.

Thus, we firmly stand by our chosen method of data presentation, as we believe it furnishes readers with more valuable insights. However, if there are additional compelling arguments to display the standard deviation instead of the standard error, we are more than willing to consider them.

3) One notable issue was that the RGC survival subject to ONC was very poor, which may limit the effects of DMAPT daily injection. The authors may consider further combining DMAPT with the DLK/LZK inhibitors to examine the synergistic effects.

As DMAPT itself is not neuroprotective and does not affect retinal ganglion cells' (RGCs) regenerative state by inducing the expression of regeneration-associated genes, a combination with a neuroprotective and regenerative treatment would show stronger effects. This is exactly what we found when combining DMAPT with neuroprotective hIL-6 (Leibinger et al. 2016) in the current paper.

Moreover, in the raphespinal tract, where respective neurons do not undergo apoptotic cell death after axotomy, the DMAPT effect on anatomic axon regeneration was stronger than in the optic nerve, even without combination with hIL-6, with some axons reaching distances of up to 7 mm distal to the lesion. So, DMAPT can induce long-distance regeneration in neuronal populations unaffected by cell death. Therefore, we feel that additional experiments with DLK/LZK inhibitors, as suggested by this reviewer, would not provide an additional benefit to our paper and not justify the additional sacrifice of animal lives.

To address this issue, we added the following paragraph: “Expectedly, DMAPT was not able to protect RGCs from axotomy-induced cell death (Fig. 4 F, G) since it does solely accelerate microtubule polymerization in axonal growth cones without affecting neuroprotective signaling pathways in the cell body (Fig. 1 F, G; supplementary Fig. 2). We then repeated these experiments in combination with intravitreally applied AAV2hIL-6 which reportedly has a significant neuroprotective effect (Leibinger et al., 2016) (Fig. 4 H).”

4) Serotonergic neurotoxin DHT, which in the spinal cord injury model ablates both regenerating and nonregenerating serotonergic axons, which makes interpretation of the results difficult. This should be addressed directly in interpretation and discussion.

The impact of unregenerated serotonergic axons on stereotypic hind leg movements, as assessed through BMS analysis, appears to be minimal, as demonstrated in our previous study (Leibinger et al., 2021). Specifically, our findings revealed that depleting serotonergic neurons using DHT did not significantly affect the BMS score in uninjured animals (Leibinger et al., 2021). Furthermore, even in the control group comprising animals with spinal cord lesions where anatomical regeneration of the RpST did not occur, the administration of DHT had no discernible effect (Fig. 7 K, L).

To address this concern, we propose including the following information in the revised manuscript: "It might appear conceivable that the depletion of non-regenerated serotonergic axons may have contributed to these results. However, we can rule this out since DHT did not influence the non-regenerated vehicle control group. Furthermore, we have shown in a previous publication that the general depletion of serotonergic neurons in uninjured animals also has no significant influence on openfield locomotion as measured in the BMS score and subscore (Leibinger et al., 2021). Furthermore, we have shown in a previous publication that the general depletion of serotonergic neurons in uninjured animals also has no significant influence on openfield locomotion as measured in the BMS score and subscore (Leibinger et al., 2021).”

5). Overall, the phenotypes in Figs 5-8 were rather weak after DMAPT treatment, which are universal challenges to spinal cord regeneration. The authors may present this section of the data with further clarification on the selection standards in the methods, such as how the animals and treatment were selected and how a double-blinded experimental design may help further evaluate the effects of DMAPT treatment. I found little relevant information in the current manuscript.

In the anatomic and functional regeneration analysis presented in Figures 5-8, we only included animals with a BMS score of 0 one day after the spinal cord crush, indicating a complete absence of hind leg movement. Furthermore, we employed immunohistochemical staining to ensure that no serotonergic axons were detected at 8-10 mm from the lesion site in any of the animals, thus confirming the thoroughness of the lesion (Supplementary Fig. 4). Both the evaluation of the BMS score and the assessment of anatomical regeneration was conducted in a doubleblinded manner, ensuring unbiased and objective observations. To address this concern, we will add the following paragraph in the M&M part:

“Blinding procedure for in vivo experiments Before the start of the experiment, individual vials containing DMAPT or vehicle (DMSO) stock solution were prepared for each experimental animal. The vials were randomized by a person who was neither involved in the implementation nor evaluated the experiments. These numbers were randomly distributed to mice of the same age and sex in different cages. This was carried out independently by another person who was neither involved in the data evaluation nor the randomization of the samples. This was followed by the execution of the experiments and the evaluation by scientists who were not involved in any randomization processes and did not know the identity of the injected samples. After completion of the data collection, values from mice with signs of spared axons were first removed from the data set for quality assurance. The criteria for this were a BMS Sore of a maximum of 0-1 on the first day after the lesion and the absence of uninjured serotonergic axons in spinal cord cross-sections >9-10 mm distal to the lesion site. Finally, the data points were assigned to the respective experimental groups by the person who initially blinded the vials.”

6) Several supplemental figures are discussed as critical elements of the studies performed. The authors are encouraged to include figures discussed as primary data as primary figures in the manuscript and provide the necessary information regarding experimental design and methods, including "n".

Thank you for the suggestion.

7) While the "n" is clear for some subsets of figures (as noted in the rebuttal), it is not clear for all outcomes/figure subsets. For example, it appears that some outcomes were performed in only a subset of the total experimental population and not in the context of statistically significant result. A good example of this is the figure for in vivo suboptimal dosing. The experimental design suggests n=7-10, but the group considered suboptimal due to statistical insignificance is listed as n=4. Is this an entirely separate cohort? If so, is n=4 sufficient and was it considered statistically in the context of the higher-powered cohorts? The lack of clarity regarding experimental design should be addressed.

To ensure transparency we have provided all n-numbers for each outcome and figure subset. Additionally, the precise n-numbers can be inferred by observing the number of individual points depicted in the graphs. All statistical data are appropriately indicated in the figure legends for reference.

The data presented in suppl. Fig. 3 represents a preliminary experiment to find effective doses of DMAPT in vivo. In this initial phase, we tested three different doses of DMAPT (0.2, 2, 20 µg/kg) in a reduced group size of only four animals per group. This reduction in animal numbers aligns with the principles to determine reduction, refinement, and replacement, aiming to minimize the use of animals in our research. Subsequently, the group demonstrating the most robust effect (2 µg/kg) was expanded by including additional animals to meet the a priori calculated sample size and validate the results. These additional animal data are presented in Figure 4 A-C. In the case of suppl. Fig. 3 A, B the statistical analysis indicated a significant effect in A using an n=4. As a result, there was no need to utilize additional animals for this particular experiment.

Gaps:

1) By in vitro studies, the authors showed that hIL-6 treatment or PTEN knockout elevated microtubule detyrosination. But when does this occur? In another words, is this a primary effect of these treatments or secondary to the increased axon growth? How does this fit with the observations that these interventions promote axon regeneration both in vitro and in vivo?

This point also seems to be based on a misunderstanding, as shown in Figure 2 by Western blot, that detyrosination was increased after intravitreal injection of AAV2-hIL-6 into optic nerves. These optic nerves were uninjured! This indicates that the increased detyrosination is an effect of the treatment itself and does not occur due to axonal regeneration.

Why hIL-6 and PTEN nevertheless increase axonal regeneration is because the positive effect on other signaling pathways, such as JAK/STAT3 and mTOR, ultimately predominates. Consequently, we show, for both PTEN ko and hIL-6, that we can further enhance these positive effects by neutralizing the negative aspect of increased detyrosination using DMAPT.

2) Is there any direct evidence for Akt and/or JAK/Stat3 to promote microtubule detyrosination?

As described in our previous and cited work, hIL-6, in contrast to CNTF, promotes the activation of AKT (Leibinger et al. 2016). In Fig. 2, we have also shown that intravitreal hIL-6 treatment in the optic nerve leads to increased phosphorylation of GSK3, a substrate of AKT, and that tubulin detyrosination is increased.

As far as we know, JAK/STAT3 has no direct effect on detyrosination.

In cell culture, we have shown that activation of the JAK/STAT3 pathway by CNTF application does not change tubulin detyrosination in neurites (Fig. 1 H, I, M; N).

DMAPT in RGC’s cell bodies does not affect the phosphorylation of STAT3 and S6, and thus has no measurable effect on JAK/STAT3 or the mTOR pathway. Moreover, tubulin detyrosination in neuronal cell bodies is not affected by DMAPT.

3) Empirical data linking in vivo regeneration with mechanisms delineated in in vitro studies is limited. The addition of such data (i.e. biochemical assays, relevant histology) would better enable interpretation of in vivo studies and improve cohesiveness of the work as a whole.

The mechanistic links between hIL-6 /PTEN-signaling and tubulin detyrosination and the abrogation of the adverse effects by DMAPT have been extensively addressed in vitro, which has been positively highlighted here in several places. Indeed, the in vivo data were intended to mainly confirm that the mechanisms elaborated in vitro are relevant to axonal regeneration and functional restoration in vivo. Most importantly our data demonstrate that systemic DMAPT application promotes axon regeneration in the CNS and improves functional recovery after a complete spinal cord injury. Form a clinical point of view this is important.

4) DMAPT activities are not limited to microtubule detyrosination. These alternate activities should be considered, particularly in in vivo studies. Empirical evidence of the potential impact for these mechanisms in the retina, optic nerve, and systemically is strongly encouraged. In vitro studies or studies of a specific neuronal population are insufficient to extrapolate activities in an intact system.

Parthenolide and DMAPT show a regenerative effect in the nanomolar range (cell culture) and a bell-shaped concentration-response curve. We show a close correlation between detyrosinated microtubules and regeneration (with and without hIL6 or PTEN-KO), which is, in our opinion, convincing. Whether additional effects of DMAPT contribute to improved regeneration is not excluded, although unlikely. If so, their investigation would be beyond the scope of the current paper.

5) How do the authors benchmark the DMAPT retreatment in the setting of PTEN (aav2-cre injection for cKO) and /or PTEN/SOCS3/CNTF dKO? Which are the best approaches to promote optic nerve regeneration? Would the authors expect DMAPT retreatment to be synergetic with PTENcKO?

Based on our previous findings, we anticipate that DMAPT would exhibit a synergistic effect when combined with PTEN ko, as demonstrated in our in vitro studies with cultured neurons. Additionally, synergistic effects between DMAPT and PTEN/SOCS3 dKO +CNTF are possible. While these hypotheses hold promise, our current paper primarily focuses on combining DMAPT with hIL-6, which has consistently shown remarkable efficacy as a standalone treatment in optic nerve regeneration.

Furthermore, our rationale for combining DMAPT with hIL-6 rather than PTEN-KO stems from the fact that, unlike PTEN-KO, hIL-6 has been proven to enable functional recovery following complete spinal cord crush injuries (Leibinger et al., 2021).

6) A cohesive discussion of findings would be beneficial. What can and cannot be elucidated from in vitro and in vivo studies? How does the in vivo effect compare to existing strategies? What are the limitations of the studies performed? Are there alternative explanations for the findings in vitro or in vivo?

We appreciate these suggestions.

Author Response

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

We would like to thank you for considering the above manuscript for publication in eLife and for sending it for review. We would like to thank the editors and reviewers for taking the time to read our manuscript and for their expert comments. These comments have been helpful and have improved our manuscript. We would like to address the following comments:

eLife assessment

This valuable study advances our knowledge of the effects of anxiety/depression treatment on metacognition, demonstrating that treatment increases metacognitive confidence alongside improving symptoms. The authors provide convincing evidence for the state-dependency of metacognitive confidence, based on a large longitudinal treatment dataset. However, it is unclear to what extent this effect is truly specific to treatment, as there was some improvement in metacognitive confidence in the control group.

Thank you for this assessment of the paper. As the change in confidence was not significant among the control group, the last sentence is not factually correct – could we suggest that it be amended to the following: “However, it is unclear to what extent this effect is truly specific to treatment, as changes in metacognitive bias in the iCBT group were not statistically different from those in the control group.”

Reviewer #1 (Public Review)

1) It has been shown previously that there are relationships between a transdiagnostic construct of anxious-depression (AD), and average confidence rating in a perceptual decision task. This study sought to investigate these results, which have been replicated several times but only in cross-sectional studies. This work applies a perceptual decision-making task with confidence ratings and a transdiagnostic psychometric questionnaire battery to participants before and after an iCBT course. The iCBT course reduced AD scores in participants, and their mean confidence ratings increased without a change in performance. Participants with larger AD changes had larger confidence changes. These results were also shown in a separate smaller group receiving antidepressant medication. A similar sized control group with no intervention did not show changes.

The major strength of the study is the elegant and well-powered data set. Longitudinal data on this scale is very difficult to collect, especially with patient cohorts, so this approach represents an exciting breakthrough. Analysis is straightforward and clearly presented. However, no multiple comparison correction is applied despite many different tests. While in general I am not convinced of the argument in the citation provided to justify this, I think in this case the key results are not borderline (p<0.001) and many of the key effects are replications, so there are not so many novel/exploratory hypothesis and in my opinion the results are convincing and robust as they are. The supplemental material is a comprehensive description of the data set, which is a useful resource.

The authors achieved their aims, and the results clearly support the conclusion that the AD and mean confidence in a perceptual task covary longitudinally. I think this study provides an important impact to the project of computational psychiatry.Sspecifically, it shows that the relationship between transdiagnostic symptom dimensions and behaviour is meaningful within as well as across individuals.

We thank the reviewer for their appraisal of our paper and positive feedback on the main manuscript and supplementary information. We agree with the reviewer that the lack of multiple comparison corrections can also justified by key findings being replications and not borderline significance. We have added this additional justification to the manuscript (Methods, Statistical Analyses, page 15, line 568: “Adjustments for multiple comparisons were not conducted for analyses of replicated effects”)

Reviewer #2 (Public Review)

The authors of this study investigated the relationship between (under)confidence and the anxious-depressive symptom dimension in a longitudinal intervention design. The aim was to determine whether confidence bias improves in a state-like manner when symptoms improve. The primary focus was on patients receiving internet-based CBT (iCBT; n=649), while secondary aims compared these changes to patients receiving antidepressants (n=82) and a control group (n=88).

The results support the authors' conclusions, and the authors convincingly demonstrated a weak link between changes in confidence bias and anxious-depressive symptoms (not specific to the intervention arm)

The major strength and contribution of this study is the use of a longitudinal intervention design, allowing the investigation of how the well-established link between underconfidence and anxious-depressive symptoms changes after treatment. Furthermore, the large sample size of the iCBT group is commendable. The authors employed well-established measures of metacognition and clinical symptoms, used appropriate analyses, and thoroughly examined the specificity of the observed effects.

However, due to the small effect sizes, the antidepressant and control groups were underpowered, reducing comparability between interventions and the generalizability of the results. The lack of interaction effect with treatment makes it harder to interpret the observed differences in confidence, and practice effects could conceivably account for part of the difference. Finally, it was not completely clear to me why, in the exploratory analyses, the authors looked at the interaction of time and symptom change (and group), since time is already included in the symptom change index.

We thank the author for their succinct summary of the main results and strengths of our study. We apologise for the confusion in how we described that analysis. We examine state-dependence., i.e. the relationship between symptom change and metacognition change, in two ways in the paper – perhaps somewhat redundantly. (1) By correlating change indices for both measures (e.g. as plotted in Figure 3D) and (2) by doing a very similar regression-based repeated-measures analysis, i.e. mean confidence ~ time * anxious-depression score change. Where mean confidence is entered with two datapoints – one for pre- and one for post-treatment (i.e. within-person) and anxious-depression change is a single value per person (between-person change score). This allowed us to test if those with the biggest change in depression had a larger effect of time on confidence. This has been added to the paper for clarification (Methods, Statistical Analysis, page 14, line 553-559: “To determine the association between change in confidence and change in anxious-depression, we used (1) Pearson correlation analysis to correlate change indices for both measures and, (2) regression-based repeated-measures analysis: mean confidence ~ time * anxious-depression score change, where mean confidence is entered with two datapoints (one for pre- and one for post-treatment i.e., within-person) and anxious-depression change is a single value per person (between-person change score)”).

The analyses have also been reported as regression in the Results for consistency (Treatment Findings: iCBT, page 5, line 197-204: ‘To test if changes in confidence from baseline to follow-up scaled with changes in anxious-depression, we ran a repeated measure regression analyses with per-person changes in anxious-depression as an additional independent variable. We found this was the case, evidenced by a significant interaction effect of time and change in anxious-depression on confidence (=-0.12, SE=0.04, p=0.002)… This was similarly evident in a simple correlation between change in confidence and change in anxious-depression (r(647)=-0.12, p=0.002)”).

2) This longitudinal study informs the field of metacognition in mental health about the changeability of biases in confidence. It advances our understanding of the link between anxiety-depression and underconfidence consistently found in cross-sectional studies. The small effects, however, call the clinical relevance of the findings into question. I would have found it useful to read more in the discussion about the implications of the findings (e.g., why is it important to know that the confidence bias is state-dependent; given the effect size of the association between changes in confidence and symptoms, is the state-trait dichotomy the right framework for interpreting these results; suggestions for follow-up studies to better understand the association).

Thank you for this comment. We have elaborated on the implications of our findings in the Discussion, including the relevance of the state-trait dichotomy to future research and how more intensive, repeated testing may inform our understanding of the state-like nature of metacognition (Discussion, Limitations and Future Directions, page 10, line 378-380: “More intensive, repeating testing in future studies may also reveal the temporal window at which metacognition has the propensity to change, which could be more momentary in nature.”).

Reviewer #3 (Public Review):

1) This study reports data collected across time and treatment modalities (internet CBT (iCBT), pharmacological intervention, and control), with a particularly large sample in the iCBT group. This study addresses the question of whether metacognitive confidence is related to mental health symptoms in a trait-like manner, or whether it shows state-dependency. The authors report an increase in metacognitive confidence as anxious-depression symptoms improve with iCBT (and the extent to which confidence increases is related to the magnitude of symptom improvement), a finding that is largely mirrored in those who receive antidepressants (without the correlation between symptom change and confidence change). I think these findings are exciting because they directly relate to one of the big assumptions when relating cognition to mental health - are we measuring something that changes with treatment (is malleable), so might be mechanistically relevant, or even useful as a biomarker?

This work is also useful in that it replicates a finding of heightened confidence in those with compulsivity, and lowered confidence in those with elevated anxious-depression.

One caveat to the interest of this work is that it doesn't allow any causal conclusions to be drawn, and only measures two timepoints, so it's hard to tell if changes in confidence might drive treatment effects (but this would be another study). The authors do mention this in the limitations section of the paper.

Another caveat is the small sample in the antidepressant group.

Some thoughts I had whilst reading this paper: to what extent should we be confident that the changes are not purely due to practice? I appreciate there is a relationship between improvement in symptoms and confidence in the iCBT group, but this doesn't completely rule out a practice effect (for instance, you can imagine a scenario in which those whose symptoms have improved are more likely to benefit from previously having practiced the task).

We thank the reviewer for commenting on the implications of our findings and we agree with the caveats listed. We thank the reviewer for raising this point about practice effects. A key thing to note is that this task does not have a learning element with respect to the core perceptual judgement (i.e., accuracy), which is the target of the confidence judgment itself. While there is a possibility of increased familiarity with the task instructions and procedures with repeated testing, the task is designed to adjust the difficulty to account of any improvements, so accuracy is stable. We see that we may not have made this clear in some of our language around accuracy vs. perceptual difficulty and have edited the Results to make this distinction clearer (Treatment Findings: iCBT, pages 4-5, lines 184-189: “Although overall accuracy remained stable due to the staircasing procedure, participants’ ability to detect differences between the visual stimuli improved. This was reflected as the overall increase in task difficulty to maintain the accuracy rates from baseline (dot difference: M=41.82, SD=11.61) to follow-up (dot difference: M=39.80, SD=12.62), (=-2.02, SE=0.44, p<0.001, r2=0.01)”.)

However, it is true that there can be a ‘practice’ effect in the sense that one may feel more confident (despite the same accuracy level) due to familiarity with a task. One reason we do not subscribe to the proposed explanation for the link between anxious-depression change and confidence change is that the other major aspect of behaviour that improved with practice did so in a manner unrelated to clinical change. As noted above in the quoted text, participants’ discrimination improved from baseline to follow-up, reflected in the need for higher difficulty level to maintain accuracy around 70%. Crucially, this was not associated with symptom change. This speaks against a general mechanism where symptom improvement leads to increased practice effects in general. Only changes in confidence specifically are associated with improved symptoms. We have provided more detail on this in the Discussion (page 9, lines 324-326: “This association with clinical improvements was specific to metacognitive changes, and not changes in task performance, suggesting that changes in confidence do not merely reflect greater task familiarity at follow-up.”).

2) Relatedly, to what extent is there a role for general task engagement in these findings? The paper might be strengthened by some kind of control analysis, perhaps using (as a proxy for engagement) the data collected about those who missed catch questions in the questionnaires.

Thank you for your comment. We included the details of data quality checks in the Supplement. Given the small number of participants that failed more than one attention checks (1% of the iCBT arm) and that all those participants passed the task exclusion criteria, we made the decision to retain these individuals for analyses. We have since examined if excluding these small number of individuals impacts our findings. Excluding those that failed more than one catch item did not affect the significance of results, which has now been added to the Supplementary Information (Data Quality Checks: Task and Clinical Scales, page 5, lines 181-185: “Additionally, excluding those that failed more than one catch item in the iCBT arm did not affect the significance of results, including the change in confidence (=0.16, SE=0.02, p<0.001), change in anxious-depression (=-0.32, SE=0.03, p<0.001), and the association between change in confidence and change in anxious-depression (r(638)=-0.10, p=0.011)”).

3) I was also unclear what the findings about task difficulty might mean. Are confidence changes purely secondary to improvements in task performance generally - so confidence might not actually be 'interesting' as a construct in itself? The authors could have commented more on this issue in the discussion.

Thank you for this comment and sorry it was not clear in the original paper. As we discussed in a prior reply, accuracy – i.e. proportion of correct selections (the target of confidence judgements) are different from the difficulty of the dot discrimination task that each person receives on a given trial. We had provided more details on task difficulty in the Supplement. Accuracy was tightly controlled in this task using a ‘two-down one-up’ staircase procedure, in which equally sized changes in dot difference occurred after each incorrect response and after two consecutive correct responses. The task is more difficult when the dot difference between stimuli is lower, and less difficult when the dot difference between stimuli is greater. Therefore, task difficulty refers to the average dot difference between stimuli across trials. Crucially, task accuracy did not change from baseline to follow-up, only task difficulty. Moreover, changes in task difficulty were not associated with changes in anxious-depression, while changes in confidence were, indicating confidence is the clinically relevance construct for change in symptoms.

We appreciate that this may not have been clear from the description in the main manuscript, and have added more detail on task difficulty to the Methods (Metacognition Task, page 14, lines 540-542: “Task difficulty was measured as the mean dot difference across trials, where more difficult trials had a lower dot difference between stimuli.”) and Results (Treatment Findings: iCBT, pages 4-5, lines 184-186: “Although overall accuracy remained stable due to the staircasing procedure, participants’ ability to detect differences between the visual stimuli improved.”). We have also elaborated more on how improvements in symptoms are associated with change in confidence, not task performance in the Discussion (page 9, lines 324-326: “This association with clinical improvements was specific to metacognitive changes, and not changes in task performance, suggesting that changes in confidence do not merely reflect greater task familiarity at follow-up”).

4) To make code more reproducible, the authors could have produced an R notebook that could be opened in the browser without someone downloading the data, so they could get a sense of the analyses without fully reproducing them.

Thank you for your comment. We appreciate that an R notebook would be even better than how we currently share the data and code. While we will consider using Notebooks in future, we checked and converting our existing R script library into R Notebooks would require a considerable amount of reconfiguration that we cannot devote the time to right now. We hope that nonetheless the commitment to open science is clear in the extensive code base, commenting and data access we are making available to readers.

5) Rather than reporting full study details in another publication I would have found it useful if all relevant information was included in a supplement (though it seems much of it is). This avoids situations where the other publication is inaccessible (due to different access regimes) and minimises barriers for people to fully understand the reported data.

We agree this is good practice – the Precision in Psychiatry study is very large, with many irrelevant components with respect to the present study (Lee et al., BMC Psychiatry, 2023). For this reason, we tried to provide all that was necessary and only refer to the Precision in Psychiatry study methods for fine-grained detail. Upon review, the only thing we think we omitted that is relevant is information on ethical approval in the manuscript, which we have now added (Methods, Participants, page 11, lines 412-417: “Further details of the PIP study procedures that are not specific to this study can be found in a prior publication (21). Ethical approval for the PIP study was obtained from the Research Ethics Committee of School of Psychology, Trinity College Dublin and the Northwest-Greater Manchester West Research Ethics Committee of the National Health Service, Health Research Authority and Health and Care Research Wales”). If any further information is lacking, we are happy to include it here also.

Reviewer #1 (Recommendations For The Authors):

Minor comments

The first line of the abstract refers to "metacognitive impairments", but the key result is a difference in the mean confidence rating - i.e. could be how participants are using the scale. It's not clear to me that lower mean confidence is necessarily an "impairment" (what's the "right" level of confidence 1-6 for a performance of 70% accuracy). The first line of discussion uses "metacognitive biases" which seems a more accurate description.

We agree that the term bias is more appropriate to use in the Abstract, given that there is not set level to indicate any level of ‘impairment’ associated with under- or over-confidence. This has been changed to ‘biases’ as per the reviewer’s request (Abstract, page 2, line 49). Thank you for this suggestion.

Reviewer #2 (Recommendations For The Authors):

I would suggest being more cautious in the wording relating to the simple effect tests on changes across different treatment arms in the abstract - since no interaction was found it may suggest a difference between arms that is not found significantly. Also since comparison between arms was the secondary aim, first describe interaction effects before simple effects in results.

Thank you for this suggestion, we agree that the lack of significant interaction effect of time and group on confidence is a key finding, which has now been included in the Abstract (page 2, lines 67-71). Additionally, we have rearranged the order of results so the interaction effects precede the simple effects (Results, Comparing iCBT, Antidepressant and Control Groups, page 7, lines 246 – 292:

"When comparing the three groups directly, ANOVA analysis predicting anxious-depression scores with group and time as independent variables revealed a main effect of time (F(1, 1632)=62.99, p<0.001), a main effect of group (F(2, 1632)=249.74, p<0.001), and an interaction effect of group and time (F(2, 1632)=9.23, p<0.001). Examining simple effects in the antidepressant arm, there was a significant reduction in anxious-depression from baseline to follow-up (=-0.61, SE=0.09, p<0.001). Among controls, levels of anxious-depression did not significantly change (=0.10, SE=0.06, p=0.096). Further details of transdiagnostic clinical changes for the antidepressant and controls groups are presented in Figure 4A and Table S4.

Predicting confidence scores using ANOVA analysis with group and time as independent variables revealed a main effect of time (F(1, 1632)=16.26, p<0.001), and no significant main effect of group (F(2, 1632)=2.35, p=0.096). The interaction effect of group and time on mean confidence was not significant (F(2, 1632)=0.60, p=0.550), suggesting that change in confidence did not differ across the three groups. Tests of simple effects revealed that mean confidence significantly increased from baseline (M=3.77, SD=0.88) to follow-up (M=4.07, SD=0.79) in the antidepressant arm (=0.31, SE=0.08, p<0.001) (Figure 4B). Among controls, there was no significant change in confidence from baseline (M=3.68, SD=0.86) to follow-up (M=3.79, SD=0.92) (=0.11, SE=0.07, p=0.103) (Figure 4B).

With respect to task performance, there was a significant main effect of time (F(1, 1632)=15.17, p=0.001) and group (F(2, 1632)=4.56, p=0.011) on mean dot difference when the three groups were included in the model. The interaction effect of time and group on mean dot difference was not significant (F(2, 1632)=1.91, p=0.148), suggesting no differences across the groups in task difficulty changes. In the antidepressant arm, mean dot difference decreased from baseline (M=41.2, SD=13.3) to follow-up (M=35.3, SD=13.1) (=-5.91, SE=1.25, p<0.001), indicating increased task difficulty. There was no significant change in task difficulty among controls from baseline (M=43.0, SD=11.8) to follow-up (M=41.4, SD=13.6) (=-1.64, SE=1.30, p=0.210) (Figure 4C).

While our sample was underpowered to examine individual differences, we conducted an exploratory analysis examining the connection between changes in anxious-depression symptoms and changes in confidence in the antidepressant and controls groups. When examining the effects of time, group and anxious-depression change on mean confidence, there was a significant interaction effect of time and anxious-depression change on mean confidence (F(1, 1626)=4.04, p=0.045), suggesting change in confidence is associated with change in anxious-depression. There was no significant three-way interaction of anxious-depression change, time and group on mean confidence when comparing the three groups (F(2, 1626)=0.08, p=0.928), indicating that the significant association between confidence change and anxious-depression change was not specific to any group. Although not significant, the association between change in confidence and change in anxious-depression was in the expected negative direction in the antidepressant arm (r(80)=-0.10, p=0.381), and among controls (r(86)=-0.17, p=0.111) (Figure 4D)."

Reviewer #3 (Recommendations For The Authors):

Some minor points:

Intro

1) Awkward wording on page 3: 'but little research on how it might impact on metacognition'

We have amended this sentence to make it more clear that relatively less research has been conducted on metacognitive changes following iCBT. We have also provided more detail on a prior study that examined changes in metacognitive beliefs with iCBT, and how this differs from the current study (Introduction, page 3, lines 137-141: “Additionally, iCBT has demonstrated clinical effectiveness in terms of symptom improvement (22–24). While one study found that iCBT modified self-reported metacognitive beliefs (25), it remains unknown if metacognitive confidence in decision-making improves following successful iCBT”).

2) On page 3 the authors note 'but studies typically lacked power to detect effects of antidepressants on cognitive abilities (30-33)' - however, surely this is a problem with this study too, and its relatively small sample of those taking antidepressants?

Thank you for highlighting this. The power comment was in the reference to the larger iCBT arm in this study, but we can appreciate that its placement means that it could be interpreted as being in relation to our smaller antidepressant arm (which we acknowledge is also potentially underpowered). We have reworded this sentence to make it clearer that prior antidepressant studies have not examined the impact of changes in metacognition specifically (Introduction, page 4, lines 147-149: “However, studies examining the impact of antidepressants on cognition have typically focused on cognitive capacities other than metacognition (30–33)”).

Results

3) Fig 2 - please clarify what the error bars indicate.

The error bars represent the standard error around the standardised beta coefficients, which I have added to the description of Figure 2 (page 4, lines 171-172: “The error bars represent the standard error around the standardised beta coefficient”).

4) Awkward wording: 'though it went in the same direction (Figure 4B)'.

This part of the sentence was removed to reduce confusion.

5) This description of the results is somewhat overstated: 'suggesting change in confidence was dependent on change in anxious-depression' (page 7) - this could also be the other way around, or related to a third factor.

We have changed this from ‘dependent’ to ‘is associated with’, which accounts for the unknown directionality and true dependency of confidence changes on changes in anxious-depression (Results, page 7, line 285: “…suggesting change in confidence is associated with change in anxious-depression”).

Methods

6) Please also show how the WSAS in a supplement.

Although this comment is unclear, we have provided additional information on how each item of the WSAS was scored and the overall score range (Supplemental methods, page 2, lines 53-55: “Each WSAS item was scored from 0 ‘not at all’ to 8 ‘very severely’, with overall scores ranging from 0 to 40. Higher WSAS scores indicating higher levels of functional impairment (11)”.

Author Response

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

Please find below our detailed point-by-point response to the eLife reviewer comments. As suggested by the reviewers, we have 1) replaced most of the Bar charts by Box plots, 2) highlighted the sucellular regions that are analyzed in the measurement experiments, and 3) have rewritten and toned down several subsections of the discussion.

Reviewer #1 (Recommendations For The Authors):

I suggest that the authors consider the following points in future versions of this manuscript:

1). The link between the striking plant phenotype and GXM misregulation is unclear since GXM overexpression doesn't alter plant phenotypes or lignin content (Yuan et al 2014 Plant Science), so misregulation of GXMs in msil2msil4 mutants clearly is not the whole story. The authors should discuss alternative interpretations of their results and other possible targets of MSIL2/4 that might be contributing to the plant phenotype.

We completely agree with the reviewer that the misregulation of GXMs in msil2/4 is not the whole story and we are currently developing specific strategies in order to characterize in an unbiased manner the full repertoire of MSIL mRNA targets in the stem, hoping we can identify other targets relevant to the formation of SCW. We have also toned-down our discussion concerning the possible impact of glucuronoxylan methylation level on lignin deposition (L546-552).

2) Similarly, it remains unclear why one particular secondary cell wall enzyme is regulated post-transcriptionally, while so much of the pathway is regulated at the transcriptional level. Please discuss.

We do not exclude that other genes encoding for SCW enzymes are impacted and it will be the subject of further investigations. We have extended the discussion concerning these points. We have extended the discussion concerning these points (L486-498).

3) Thirdly, it seems that MSIL2 and MSIL4 are expressed in tissues that are not synthesizing secondary cell walls. The authors should discuss other possible targets of MSIL2/4 from their work.

We have extended the discussion concerning the pleiotropic effects of MSIL mutation in Arabidopsis (L 416-425). The variability of the msil2/4 phenotype is so large that we expect these proteins to regulate various cellular functions through the binding of specific set of mRNA. The mRNA targets specifically involved in these regulations will need to be determined on a case-by-case basis.

4) The discussion is extremely speculative and introduces new abbreviations (LTAc, XTRe) that are only used in their model (Figure 7). I suggest replacing these with dashed lines and/or question marks in the model, since as currently depicted, it looks as if these could be known gene products, which could be very misleading.

We have removed the Ltac and XTRe abbreviations in Figure 7, and the corresponding text in the discussion section.

5) Similarly, the speculation that cellulose content somehow regulates glucuronoxylan levels via xylan-cellulose interactions, leading to degradation of excess glucuronoxylan after synthesis is, to my knowledge, completely unsupported by any evidence except the correlation between cellulose and xylan levels. Please either support this claim with references or remove it from the discussion.

We have removed the claim and have rewritten and toned down the text accordingly to the reviewer 1 comments (L 499-512).

6) Bar charts are rarely the most appropriate method for displaying biological data (Streit & Gehlenborg 2014 Nature Methods). Authors should replace bar charts with one of the following options: A) plot all individual datapoints and overlay summary statistics, B) box plots with all individual datapoints show, C) violin plots (when n is large, i.e. n > 50). R and R studio are free software that can generate such plots. Several excellent tools exist online to generate such plots via a free, graphical user interface, such as boxplotr (Spitzer et al 2014 Nature Methods): http://shiny.chemgrid.org/boxplotr/ and PlotsOfData (Postma & Goedhart 2019 PLoS Biology): https://huygens.science.uva.nl/PlotsOfData/

We have replaced the Bar charts in figure 4E,G and Fig 5E with Box plots and acknowledged the software used in the corresponding Materials and methods section.

Reviewer #2 (Recommendations For The Authors):

Minor points:

Which cells from Fig. 4b were measured for 4c? Some highlighted annotations to delineate the regions that were measured would help.

We have highlighted in figure 4B the subcellular regions cells analyzed in the measurement experiments.

In line 254, the phrase "not merely affected" in the mutant should be rephrased for clarity

We have replaced “not merely affected” by “not significantly” (L274).

Line 317: "we first performed glycome profiling", the data shows monosaccharide profile, not glycome profiling usually involving antibodies microarrays

We have corrected the text according to the reviewer comment (L339-340).

Reviewer #3 (Recommendations For The Authors):

Altogether, the study shows clear biological relevance of the MSL family of RNA-binding proteins, and provides good arguments that the underlying mechanism is control of mRNAs encoding enzymes involved in secondary cell wall metabolism (although concluding on translational control in the abstract is perhaps saying too much - post-transcriptional control will do given the evidence presented). One observation reported in the study makes it vulnerable to alternative interpretation, however, and I think this should be explicitly treated in the discussion:

The fact that immune responses are switched on in msl2/4 mutants could also mean that MSL2/4 have biological functions unrelated to cell wall metabolism in wild type plants, and that cell wall defects arise solely as an indirect effect of immune activation (that is known to involve changes in expression of many cell wall-modifying enzymes and components such as pectin methylesterases, xyloglucan endotransglycosylases, arabinogalactan proteins etc. Indeed, the literature is rich in examples of gene functions that have been misinterpreted on the basis of knockout studies because constitutive defense activation mediated by immune receptors was not taken into account (see for example Lolle et al., 2017, Cell Host & Microbe 21, 518-529).

With the evidence presented here, I am actually close to being convinced that the primary defect of msl2/msl4 mutants is directly related to altered cell wall metabolism, and that defense responses arise as a consequence of that, not the other way round. But I do not think that the reverse scenario can be formally excluded with the evidence at hand, and a discussion listing arguments in favor of the direct effect proposed here would be appropriate. Elements that the authors could consider to include would be the isolation of a cellulose synthase mutant as a constitutive expressor of jasmonic acid responses (cev1) as a clear example that a primary defect in cell wall metabolism can produce defense activation as secondary effect. The interaction of MSL4 with GXM1/3 mRNAs is also helpful to argue for a direct effect, and it would strengthen the argument if more examples of this kind could be included.

In accordance to Rev3 comments, we have extended the discussion, listing the arguments, that we believe, are not in favor of a primary effect of the MSIL2/4 proteins on the activation of plant defense pathways (L468-485).

SUGGESTIONS FOR IMPROVED ANALYSES & MINOR TEXT AND FIGURE CORRECTIONS.

(1) Unless there is a very good reason to use homology modelling such as SWISS-MODEL (for example ligand-bound proteins), Alphafold2 is now the tool to use for structure prediction. I would at least verify that Alphafold agrees with SWISS-MODEL on the predicted structures shown in Fig 2a.

We have analyzed the MSIL4 sequence using the Alphafold2 prediction software and the output of this analysis completely agrees with the SWISS-Model prediction. We have added an additional panel showing the Alphafold 2 prediction (see figure 2-figure supplement 1B).

(2) The plant pictures shown in Figure 2d are not publication quality in terms of resolution, mounting, size. They really should be redone before final publication.

We thank the reviewer for this important observation, and have improved the resolution of the figure 2D.

(3) The colocalization in Figure 3d/e would benefit from some statistical analysis of the data: How many foci were examined? How many showed colocalization? Is that fraction statistically significant? It can be done from the images at hand; I do not think that additional data acquisition is necessary.

We have used an ImageJ plugin to perform colocalization analysis on the microscopy images corresponding to the bottom panel of the figure 3D (heat stress). This analysis confirmed that most of the foci are actually colocalizing (see Author response image 1). However our initial image data acquisition do not allow us to perform statistical analysis on it. We have added a sentence indicating that colocalization is supported by an analysis using an ImageJ plugin.

Author response image 1.

4) Typographical and other writing errors:

Line 72 "prior to"

Line 77 "in the Arabidopsis model"

Line 97 "RBP-mediated..."

Line 110 "aspects of development"

Line 128 "little is known" (no yet)

Line 253 "Col-0"

Line 346 "previous"

All the writing errors have been corrected in the revised version.

Author Response

We thank the reviewers for their helpful comments and suggestions.

eLife assessment

This is an important contribution that extends earlier single-unit work on orientation-specific center-surround interactions to the domain of population responses measured with Voltage Sensitive Dye (VSD) imaging and the first to relate these interactions to orientation-specific perceptual effects of masking. The authors provide convincing evidence of a pattern of results in which the initial effect of the mask seems to run counter to the behavioral effects of the mask, a pattern that reversed in the latter phase of the response. It seems likely that the physiological effects of masking reported here can be attributed to previously described signals from the receptive field surround.

We thank the reviewers for bringing up the relation of our results to findings from previous orientation-specific center-surround interactions studies. In our revision, we will add a paragraph discussing this important issue. Briefly, for multiple reasons, we believe that the majority of the behavioral and neural masking effects that we observe may be from target-mask interactions at the target location rather than from the effect of the mask in the surround. First, in human subjects, perceptual similarity masking effects are almost entirely accounted for by target-mask interactions at the target location and are recapitulated when the mask has the same size and location as the target (Sebastian et al 2017). Second, in our computational model (Fig. 8), the effect of mask orientation on the dynamics of the response are qualitatively the same if the mask is restricted to the size and location of the target. Third, in our model, our results are qualitatively the same when the spatial pooling region for the normalization signal is the same as that for the excitation signal. These points will be elaborated in the revised manuscript and points 2 and 3 will be demonstrated in a supplementary figure.

We would also like to point out some key differences between the stimuli that we use and the ones used in most previous center-surround studies. First, in our experiments, the target and the mask were additive, while in most previous center-surround studies the target occludes the background. Such studies therefore restrict the mask effect to the surround, while in our study we allow target-mask interactions at the center. Second, most center-surround studies have a sharp-edged target/surround, while in our experiments no sharp edges were present. Unpublished results form our lab suggest that such sharp edges have a large impact on V1 population responses. We will expand on these issues in the revised manuscript. A third key difference is that our stimuli were flashed for a short interval of 250 ms corresponding to a typical duration of a fixation in natural vision, while most previous center-surround studies used either longer-duration drifting stimuli or very short-duration random-order stimuli for reverse-correlation analysis.

In addition, we would like to emphasize that our results go beyond previous studies in two important ways. First, we study the effect of similarity masking in behaving animals and quantitatively compare the effect of similarity masking on behavior and physiology in the same subjects and at the same time. Second, VSD imaging allows us to capture the dynamics of superficial V1 population responses over the entire population of millions of neurons activated by the target at two important spatial scales. Such results therefore complement electrophysiological studies that examine the activity of a very small subset of the active neurons.

Reviewer #1 (Public Review):

This is a clear account of some interesting work. The experiments and analyses seem well done and the data are useful. It is nice to see that VSDI results square well with those from prior extracellular recordings. But the work may be less original than the authors propose, and their overall framing strikes me as odd. Some additional clarifications could make the contribution more clear.

Please see our reply above regarding the agreement with previous studies and framing.

My reading is that this is primarily a study of surround suppression with results that follow pretty directly from what we already know from that literature, and although they engage with some of the literature they do not directly mention surround suppression in the text. Their major effect - what they repeatedly describe as a "paradoxical" result in which the responses initially show a stronger response to matched targets and backgrounds and then reverse - seems to pretty clearly match the expected outcome of a stimulus that initially evokes additional excitation due to increased center contrast followed by slightly delayed surround suppression tuned to the same peak orientation. Their dynamics result seems entirely consistent with previous work, e.g. Henry et al 2020, particularly their Fig. 3 https://elifesciences.org/articles/54264, so it seems like a major oversight to not engage with that work at all, and to explain what exactly is new here.

We thank the reviewer for the pointing out this previous work which we will cite in the revised version of the manuscript. For the reasons discussed above, while this study is interesting and related to our work, we believe that our results are quite distinct.

• In the discussion (lines 315-316), they state "in order to account for the reduced neural sensitivity with target-background similarity in the second phase of the response, the divisive normalization signal has to be orientation selective." I wonder whether they observed this in their modeling. That is, how robust were the normalization model results to the values of sigma_e and sigma_n? It would be useful to know how critical their various model parameters were for replicating the experimental effects, rather than just showing that a good account is possible.

Thank you for this suggestion. In the revised manuscript we will include a supplementary figure that will show how the model’s predictions are affected by the orientation tuning and spatial extent of the normalization signal, and by the size of the mask.

• The majority of their target/background contrast conditions were collected only in one animal. This is a minor limitation for work of this kind, but it might be an issue for some.

We agree that this is a limitation of the current study. These are challenging experiments and we were unable to collect all target/background contrast combinations from both monkeys. However, in the common conditions, the results appear similar in the two animals, and the key results seem to be robust to the contrast combination in the animal in which a wider range of contrast combinations was tested. We will add these points to the discussion in the revised manuscript.

• The authors point out (line 193-195) that "Because the first phase of the response is shorter than the second phase, when V1 response is integrated over both phases, the overall response is positively correlated with the behavioral masking effect." I wonder if this could be explored a bit more at the behavioral level - i.e. does the "similarity masking" they are trying to explain show sensitivity to presentation time?

We agree that testing the effect of stimulus duration on similarity masking is interesting, but unfortunately, it is beyond the scope of the current study. We would also like to point out that the duration of the presentation was selected to match the typical time of fixation during natural behaviors, so much shorter or much longer stimulus durations would be less relevant for natural vision.

• From Fig. 3 it looks like the imaging ROI may include some opercular V2. If so, it's plausible that something about the retinotopic or columnar windowing they used in analysis may remove V2 signals, but they don't comment. Maybe they could tell us how they ensured they only included V1?

We thank the reviewer for this comment. As part of our experiments, we extract a detailed retinotopic map for each chamber, so we were able to ensure that the area used for the decoding analysis lays entirely within V1. We will incorporate this information in the revised manuscript.

• In the discussion (lines 278-283) they say "The positive correlation between the neural and behavioral masking effects occurred earlier and was more robust at the columnar scale than at the retinotopic scale, suggesting that behavioral performance in our task is dominated by columnar scale signals in the second phase of the response. To the best of our knowledge, this is the first demonstration of such decoupling between V1 responses at the retinotopic and columnar scales, and the first demonstration that columnar scale signals are a better predictor of behavioral performance in a detection task." I am having trouble finding where exactly they demonstrate this in the results. Is this just by comparison of Figs. 4E,K and 5E,K? I may just be missing something here, but the argument needs to be made more clearly since much of their claim to originality rests on it.

We thank the reviewer for this comment. In the revised manuscript we will be more explicit and refer to the relevant figure panels (Fig 4D, E, J, & K vs. Fig 5D, E, J, & K) and report important values to substantiate this key claim.

Reviewer #2 (Public Review):

Summary

In this experiment, Voltage Sensitive Dye Imaging (VSDI) was used to measure neural activity in macaque primary visual cortex in monkeys trained to detect an oriented grating target that was presented either alone or against an oriented mask. Monkeys' ability to detect the target (indicated by a saccade to its location) was impaired by the mask, with the greatest impairment observed when the mask was matched in orientation to the target, as is also the case in human observers. VSDI signals were examined to test the hypothesis that the target-evoked response would be maximally suppressed by the mask when it matched the orientation of the target. In each recording session, fixation trials were used to map out the spatial response profile and orientation domains that would then be used to decode the responses on detection trials. VSDI signals were analyzed at two different scales: a coarse scale of the retinotopic response to the target and a finer scale of orientation domains within the stimulus-evoked response. Responses were recorded in three conditions: target alone, mask alone, and target presented with mask. Analyses were focused on the target evoked response in the presence of the mask, defined to be the difference in response evoked by the mask with target (target present) versus the mask alone (target absent). These were computed across five 50 msec bins (total, 250 msec, which was the duration of the mask (target present trials, 50% of trials) / mask + target (target present trials, 50% of trials). Analyses revealed that in an initial (transient) phase the target evoked response increased with similarity between target and mask orientation. As the authors note, this is surprising given that this was the condition where the mask maximally impaired detection of the target in behavior. Target evoked responses in a later ('sustained') phase fell off with orientation similarity, consistent with the behavioral effect. When analyzed at the coarser scale the target evoked response, integrated over the full 250 msec period showed a very modest dependence on mask orientation. The same pattern held when the data were analyzed on the finer orientation domain scale, with the effect of the mask in the transient phase running counter to the perceptual effect of the mask and the sustained response correlating the perceptual effect. The effect of the mask was more pronounced when analyzed at the scale.

Strengths

The work is on the whole very strong. The experiments are thoughtfully designed, the data collection methods are good, and the results are interesting. The separate analyses of data at a coarse scale that aggregates across orientation domains and a more local scale of orientation domains is a strength and it is reassuring that the effects at the more localized scale are more clearly related to behavior, as one would hope and expect. The results are strengthened by modeling work shown in Figure 8, which provides a sensible account of the population dynamics. The analyses of the relationship between VSDI data and behavior are well thought out and the apparent paradox of the anti-correlation between VSDI and behavior in the initial period of response, followed by a positive correlation in the sustained response period is intriguing.

Points to Consider / Possible Improvements

The biphasic nature of the relationship between neural and behavioral modulation by the mask and the surprising finding that the two are anticorrelated in the initial phase are left as a mystery. The paper would be more impactful if this mystery could be resolved.

We thank the reviewer for the positive comments. In our view, while our results are surprising, there may not be a remaining mystery that needs to be resolved. As our model shows, the biphasic nature of V1’s response can be explained by a delayed orientation-tuned gain control. Our results are consistent with the hypothesis that perception is based on columnar-scale V1 signals that are integrated over an approximately 200 ms long period that incorporates both the early and the late phase of the response, since such decoded V1 signals are positively correlated with the behavioral similarity masking effect (Fig. 5D, J). We will explain this more clearly in the discussion of our revised manuscript.

The finding is based on analyses of the correlation between behavior and neural responses. This appears in the main body of the manuscript and is detailed in Figures S1 and S2, which show the correlation over time between behavior and target response for the retinotopic and columnar scale.

One possible way of thinking of this transition from anti- to positive correlation with behavior is that it might reflect the dynamics of a competitive interaction between mask and target, with the initial phase reflecting predominantly the mask response, with the target emerging, on some trials, in the latter phase. On trials when the mask response is stronger, the probability of the target emerging in the latter phase, and triggering a hit, might be lower, potentially explaining the anticorrelation in the initial phase. The sustained response may be a mixture of trials on which the target response is or is not strong enough to overcome the effect of the mask sufficiently to trigger target detection.

It would, I think, be worth examining this by testing whether target dynamics may vary, depending on whether the monkey detected the target (hit trials) or failed to detect the target (miss trials). Unless I missed it I do not think this analysis was done. Consistent with this possibility, the authors do note (lines 226-229) that "The trajectories in the target plus mask conditions are more complex. For example, when mask orientation is at +/- 45 deg to the target, the population response is initially dominated by the mask, but then in mid-flight, the population response changes direction and turns toward the direction of the target orientation." This suggests (to this reviewer, at least) that the emergence of a positive correlation between behavioral and neural effects in the latter phase of the response could reflect either a perceptual decision that the target is present or perhaps deployment of attention to the location of the target.

It may be that this transition reflected detection, in which it might be more likely on hit trials than miss trials. Given the SNR it would presumably be difficult to do this analysis on a trial-by-trial basis, but the hit and miss trials (which make each make up about 1/2 of all trials) could be averaged separately to see if the mid-flight transition is more prominent on hit trials. If this is so for the +/- 45 degree case it would be good to see the same analysis for other combinations of target and mask. It would also be interesting to separate correct reject trials from false alarms, to determine whether the mid-flight transition tends to occur on false alarm trials.

If these analyses do not reveal the predicted pattern, they might still merit a supplemental figure, for the sake of completeness.

We thank the reviewer for suggesting this interesting possibility. The analysis in the manuscript was based on both correct and incorrect trials, raising the possibility that our results reflect some contribution from decision- and/or attention-related signals rather than from low-level nonlinear encoding mechanisms in V1 that we postulate in our model (Fig. 8). To explore this possibility, we re-examined our results while excluding error trials. We found that our key results from Figs 4 and 5 – namely that there is an early transient phase in which the neural and behavioral similarity effects are anti-correlated, and a later sustained phase in which they are positively correlated – hold even for the subset of correct trials, reducing the possibility that decision/attention-related signals play a major role in explaning our results. We will include the results of this analysis as a supplementary figure in the revised manuscript. This analysis, however, does seem to reveal interesting differences between correct and incorrect trials which we will discuss in the revised manuscript. s

References

Sebastian S, Abrams J, Geisler WS. 2017. Constrained sampling experiments reveal principles of detection in natural scenes. Proc Natl Acad Sci U S A 114: E5731-e40

Author Response

The following is the authors’ response to the previous review

In response to the additional concerns voiced by Reviewer# 2, we have conducted control simulations. The outcomes are summarized in the new supplements to Figure 3. They show that the model is robust under changes of short-term plasticity parameters and running speed.

Below, we give a point-by-point response to the remaining comments of the editors and reviewers.

Editorial Assessment: This important work presents an interesting perspective for the generation and interpretation of phase precession in the hippocampal formation. Through numerical simulations and comparison to experiments, the study provides a convincing theoretical framework explaining the segregation of sequences reflecting navigation and sequences reflecting internal dynamics in the DG-CA3 loop. This study will be of interest for researchers in the spatial navigation and computational neuroscience fields.

We would like to thank the Editors very much for this positive assessment of our work!

Reviewer #1

In the manuscript entitled ”A theory of hippocampal theta correlations”, the authors propose a new mechanism for phase precession and theta-time scale generation, as well as their interpretation in terms of navigation and neural coding. The authors propose the existence of extrinsic and intrinsic sequences during exploration, which may have complementary functions. These two types of sequences depend on external input and network interactions, but differ on the extent to which they depend on movement direction. Moreover, the authors propose a novel interpretation for intrinsic sequences, namely to signal a landmark cue that is independent of direction of traversal. Finally, a readout neuron can be trained to distinguish extrinsic from intrinsic sequences.

• The study puts forward novel computational ideas related to neural coding, partly based on previous work from the authors, including published (Leibold, 2020, Yiu et al., 2022) and unpublished (Ahmedi et al., 2022. bioRxiv) work. The manuscript will contribute to the understanding of the mechanisms behind phase precession, as well as to how we interpret hippocampal temporal coding for navigation and memory.

I am very pleased to have seen major improvements in the manuscript regarding i) a clarification of the concepts of extrinsic and intrinsic mechanisms, and ii) overall arrangement of Figures but also iii) expanding on some important concepts such as the role of experience in determining the asymmetric connectivity that is necessary for intrinsic models of sequence generation.

We are delighted to have been able to amend the Reviewer’s concerns voiced after the initial submission. We are very grateful for their many good suggestions that allowed us to make important additions to the revised manuscript.

Reviewer #2

• Place cells fire sequentially during hippocampal theta oscillations, forming a spatial representation of behavioral experiences in a temporally-compressed manner. The firing sequences during theta cycles are widely considered as essential assemblies for learning, memory, and planning. Many theoretical studies have investigated the mechanism of hippocampal theta firing sequences; however, they are either entirely extrinsic or intrinsic. In other words, they attribute the theta sequences to external sensorimotor drives or focus exclusively on the inherent firing patterns facilitated by the recurrent network architectures. Both types of theories are inadequate for explaining the complexity of the phenomena, particularly considering the observations in a previous paper by the authors: theta sequences independent of animal movement trajectories may occur simultaneously with sensorimotor inputs (Yiu et al., 2022).

In this manuscript, the authors concentrate on the CA3 area of the hippocampus and develop a model that accounts for both mechanisms. Specifically, the model generates extrinsic sequences through the short-term facilitation of CA3 cell activities, and intrinsic sequences via recurrent projections from the dentate gyrus. The model demonstrates how the phase precession of place cells in theta sequences is modulated by running direction and the recurrent DG-CA3 network architecture. To evaluate the extent to which firing sequences are induced by sensorimotor inputs and recurrent network architecture, the authors use the Pearson correlation coefficient to measure the ”intrinsicity” and ”extrinsicity” of spike pairs in their simulations.

I find this research topic to be both important and interesting, and I appreciate the clarity of the paper. The idea of combining intrinsic and extrinsic mechanisms for theta sequences is novel, and the model effectively incorporates two crucial phenomena: phase precession and directionality of theta sequences. I particularly commend the authors’ efforts to integrate previous theories into their model and conduct a systematic comparison. This is exactly what our community needs: not only the development of new models, but also understanding the critical relationships between different models.

We also would like to express our gratitude to Reviewer 2 for their numerous constructive criticisms that led to a very much improved revised manuscript!

Reviewer #2

1) The choice of timescale parameters for input facilitation and synaptic depression is still not fully justified in my opinion. The authors themselves mention that previous experiments suggest wide ranges for both timescales. Given that the generation of intrinsic and extrinsic sequences in their model is primarily driven by these two mechanisms, their chosen timescales should significantly impact the simulation results. I urge the authors to discuss the potential effects of selecting different sets of timescales and the possible limitations of the current selection of 500ms for both.

For instance, the authors state in the caption of Fig 1 that all simulated rat trajectories were set at a speed of 20cm/s, which is a rat’s walking speed. However, the running speed of rats can exceed 3m/s. In this case, none of the CA3 cells in the model would produce any extrinsic sequences since the animal would traverse the place fields much more rapidly, preventing the sensorimotor input from increasing as it does in the model.

The reviewer raised the valid point that our simulations may be sensitive to the short-term plasticity time constants and running speeds. We therefore conducted new simulations illustrated in Figure 3—figure supplements 1 and 2.

In agreement with the reviewer’s assertion, using the current model parameters, a higher running speed would not elicit extrinsic sequences due to the lack of depolarization from spatial input (Figure 3—figure supplement 2A). However, an increase of running speed also requires sensory inputs to be available on a larger spatial scale (width of the spatial input box in our case). Parra-Barrero et al., eLife 10:e70296 and Parra-Barrero & Cheng 2023, PLOS Comput. Bio. 19:e1011101, e.g., showed that place field sizes become larger under higher running speeds and consequently lengthen the theta sequences. With such modification, along with a longer DG projection length (|r|), we were able to recover the theta sequence at a higher speed (100 cm/s), using the same STD and STF time constants (Figure 3—figure supplement 2B). Furthermore, it has been shown that theta frequency increases with running speed (e.g., Rivas et al., 1996, Exp Brain Res 108:113-8). In our analysis, a higher theta frequency (12Hz instead of 10Hz) is also able to counteract the effect of running speed and leads to control-level like phase precession Figure 3—figure supplement 2C).

Consistent with this finding, the original study of Romani & Tsodyks 2015, Hippocampus 25:94-105, found a fourfold increase of speed (from 0.05 to 0.2 fraction of the track per second) to not affect phase-position relations (with UD = 0.8 and 800ms STD time constant), likely due to the large place field sizes covering 1/3 of the track. Thus, phase precession may only be affected by high speeds in narrow place fields in which activity would only be present for few theta cycles thus naturally having limited capacity for phase coding.

We further refrain from increasing the running speed beyond 1m/s (e.g. 3m/s as suggested by the reviewer), as the typical running speed of a rat in an 80cm square environment is between 20-40cm/s (Mankin et al. 2012, PNAS, 109:19462-19467). Even on linear tracks, reported running speeds hardly exceed 120 cm/s (e.g. Ahmed and Mehta, 2018, J Neurosci 32:73737383; Schmidt et al., 2009 J Neurosci 29:13232-13241). To our knowledge phase precession for speeds above 1.2 m/s has not been reported so far at all, certainly also owing to experimental challenges. We, however, would speculate that beyond 120 cm/s phase precession could be meaningful in large environmental enclosures with wide place cells. Thus a version of our input model with very large place field sizes should generally be able to also cover very high running speeds.

To conclude, STD and STF time constants do not need to be in a precise range to accommodate the behavioural time scales if the sensory input changes on accordingly larger spatial scales.

Following up on the reviewer’s additional concern, we also checked the effect of time constants on the theta sequences (while keeping the running speed unchanged). Decreasing the time constant of STF (τF) to 100ms would degrade the theta sequence due to a lack of depolarization, as sensory input reverts to its resting value ( =0) too fast, but at 250ms, the temporal correlation of theta sequences is largely maintained (Figure 3—figure supplement 1A). However, such effects can be compensated for by an increase in sensory input which promotes input facilitation (Figure 3—figure supplement 1B). Further increasing τF does not significantly affect theta sequences as the sensory input amplitude have asymptotically reached their target values (Figure 3—figure supplement 1A bottom). The temporal correlation of theta sequences is not sensitive to the change in the time constant of STD (τD) (Figure 3—figure supplement 1C), possibly because the synaptic resource of the place cells behind the animal is reliably depleted by strong depolarization despite a fast recovery time (τD=100ms).

Since the relation between running speed and theta sequences has been thoroughly studied in Parra-Barrero et al. 2021 and Parra-Barrero & Cheng 2023, and the precise range of STD and STF time scales does not play a critical role in the temporal structure of theta sequence, we refrain from substantially revising the manuscript and only briefly add these points after Figure 3.

2) This is a point I overlooked in the initial review. The synaptic depression fraction UD is set at 0.9 or 0.7, implying that the synaptic coupling weight between CA3 excitatory cells (and CA3 to DG) is almost entirely depleted within a few hundred milliseconds. To my limited neuroscience knowledge, I am not aware of any experimental results that corroborate this potentially bold setup, and I urge the authors to provide relevant experimental and theoretical references if they exist.

Most crucially, I find this setup biased towards supporting the authors’ theory for intrinsic sequences because it essentially eliminates the possibility of any CA3 cell producing an effective output to other neurons after it fires. Hence, I question whether the simulation results would be much less clean if a more moderate depression factor UD were utilized.

We thank the reviewer for giving us the opportunity to further clarify. 1) Probabilties of synaptic release (here called UD for consistency with the original work by Romani and Tsodyks), can attain a very wide range and indeed achieve values up to 0.9 (for review see e.g. Dobrunz LE, Stevens CF, 1997, Neuron, 18: 995-1008). 2) Contrary to the reviewer’s impression, a higher UD (0.7-0.9 in our case) would bias the simulation towards even more extrinsicity. Larger UD produces steeper phase precession in extrinsic sequences, because it (temporarily) generates an even stronger asymmetrical connectivity. 3) The extreme value of 0.9 was only used in Figure 1 to best illustrate the original Romani and Tsodyks 2015 idea. 4) Our simulations without recurrent synaptic connections (Figure 6) do not even require short-term synaptic depression. In view of these arguments we refrained from making further additions to the paper and refer the critical reader to this comment.

• I have a few final suggestions for the authors in the hopes of further improving the manuscript for the neuroscience community:

• line 62: sensorimotor input is present or ABSENT?

Intrinsic activity signatures are found ”EVEN when sensorimotor feedback is present”, as one may assume that this input may be able to completely override the intrinsic patterns.

• line 76: played out. colloquial, consider rewriting/explaining

We use ”evoked” now.

• line 104: second part of motivation for Izhikevich-type model is wordy, and grammatically incorrect.

We have shortened the sentence.

• on potential limitations of the model lines 116-120: is the use of a box an important assumption, as opposed to a more graded function, exponential or gaussian?

Using-spike based input, it is not straight-forward how to implement a graded input. One way would be to employ a stochastic point process with graded firing probability. We, however, chose to use a nonlinear facilitation function (see below).

• line 124 (equation) and 129-130: How crucial is the non-linearity in the synaptic variable for the results? This is a strong assumption, as the nonlinearity is the dominant effect (as opposed to a correction/perturbation). Are there any other contributions for this ramp of activity due to sensory input?

We found results to fit best with a non-linear facilitation function (see above), and, as argued in the manuscript, facilitation indeed acts non-linearly owing to the calcium-dependence of synaptic release. We have added a comment to the Methods section explaining that we use facilitation to generate a graded spatial input.

• line 187: ’...neglecting gamma activity in the model.’ I suggest removing this part of the sentence, unless you motivate why gamma would be relevant and the conditions for its generation.

We have followed the reviewer’s suggestion.

Author Response

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

We thank you for the time you took to review our work and for your feedback!

The major changes to the manuscript are:

1) Promoted by multiple reviewers, we have replaced the statistical analysis in Figure 1L with a bootstrap analysis, added an ANOVA (in Table S1), and have also added the same analysis with mice as a statistical unit as Figure S4J to the manuscript.

2) In response to reviewer 1, comment 3, we have replaced the response latency maps previously shown in Figures 3B, 3C, 3E and 3F with response amplitude maps.

3) In response to reviewer 2, comment 1, we have added a variant of the response traces shown in Figures 3B, 3C, 3E and 3F with mice as the statistical unit as Figures S2C and S2D.

4) In response to reviewer 2, public review, we have added data from additional experiments as Figures S6F-S6H, that control for the effect of a saline injection.

A detailed point-by-point response to all reviewer concerns is provided in the following.  

Reviewer #1 (Public Review):

The authors present a study of visuo-motor coupling primarily using wide-field calcium imaging to measure activity across the dorsal visual cortex. They used different mouse lines or systemically injected viral vectors to allow imaging of calcium activity from specific cell-types with a particular focus on a mouse-line that expresses GCaMP in layer 5 IT (intratelencephalic) neurons. They examined the question of how the neural response to predictable visual input, as a consequence of self-motion, differed from responses to unpredictable input. They identify layer 5 IT cells as having a different response pattern to other cell-types/layers in that they show differences in their response to closed-loop (i.e. predictable) vs open-loop (i.e. unpredictable) stimulation whereas other cell-types showed similar activity patterns between these two conditions. They analyze the latencies of responses to visuomotor prediction errors obtained by briefly pausing the display while the mouse is running, causing a negative prediction error, or by presenting an unpredicted visual input causing a positive prediction error. They suggest that neural responses related to these prediction errors originate in V1, however, I would caution against overinterpretation of this finding as judging the latency of slow calcium responses in wide-field signals is very challenging and this result was not statistically compared between areas. Surprisingly, they find that presentation of a visual grating actually decreases the responses of L5 IT cells in V1. They interpret their results within a predictive coding framework that the last author has previously proposed. The response pattern of the L5 IT cells leads them to propose that these cells may act as 'internal representation' neurons that carry a representation of the brain's model of its environment. Though this is rather speculative. They subsequently examine the responses of these cells to anti-psychotic drugs (e.g. clozapine) with the reasoning that a leading theory of schizophrenia is a disturbance of the brain's internal model and/or a failure to correctly predict the sensory consequences of self-movement. They find that anti-psychotic drugs strongly enhance responses of L5 IT cells to locomotion while having little effect on other cell-types. Finally, they suggest that anti-psychotics reduce long-range correlations between (predominantly) L5 cells and reduce the propagation of prediction errors to higher visual areas and suggest this may be a mechanism by which these drugs reduce hallucinations/psychosis.

This is a large study containing a screening of many mouse-lines/expression profiles using wide-field calcium imaging. Wide-field imaging has its caveats, including a broad point-spread function of the signal and susceptibility to hemodynamic artifacts, which can make interpretation of results difficult. The authors acknowledge these problems and directly address the hemodynamic occlusion problem. It was reassuring to see supplementary 2-photon imaging of soma to complement this data-set, even though this is rather briefly described in the paper. Overall the paper's strengths are its identification of a very different response profile in the L5 IT cells compared other layers/cell-types which suggests an important role for these cells in handling integration of self-motion generated sensory predictions with sensory input. The interpretation of the responses to anti-psychotic drugs is more speculative but the result appears robust and provides an interesting basis for further studies of this effect with more specific recording techniques and possibly behavioral measures.

We thank the reviewer for the feedback and the help with improving the manuscript. We agree, the findings presented in this study are merely a starting point. The two questions we are currently pursuing in follow up work are:

1) Do the findings generalize to all known antipsychotic drugs?

2) What is the mechanism by which these drugs induce a decorrelation of activity, specifically in layer 5 neurons?

But we suspect these questions will take at least a few more years of research to answer.

Reviewer #2 (Public Review):

Summary:

This work investigates the effects of various antipsychotic drugs on cortical responses during visuomotor integration. Using wide-field calcium imaging in a virtual reality setup, the researchers compare neuronal responses to self-generated movement during locomotion-congruent (closed loop) or locomotionincongruent (open loop) visual stimulation. Moreover, they probe responses to unexpected visual events (halt of visual flow, sudden-onset drifting grating). The researchers find that, in contrast to a variety of excitatory and inhibitory cell types, genetically defined layer 5 excitatory neurons distinguish between the closed and the open loop condition and exhibit activity patterns in visual cortex in response to unexpected events, consistent with unsigned prediction error coding. Motivated by the idea that prediction error coding is aberrant in psychosis, the authors then inject the antipsychotic drug clozapine, and observe that this intervention specifically affects closed loop responses of layer 5 excitatory neurons, blunting the distinction between the open and closed loop conditions. Clozapine also leads to a decrease in long-range correlations between L5 activity in different brain regions, and similar effects are observed for two other antipsychotics, aripripazole and haloperidol, but not for the stimulant amphetamine. The authors suggest that altered prediction error coding in layer 5 excitatory neurons due to reduced longrange correlations in L5 neurons might be a major effect of antipsychotic drugs and speculate that this might serve as a new biomarker for drug development.

Strengths:

• Relevant and interesting research question:

The distinction between expected and unexpected stimuli is blunted in psychosis but the neural mechanisms remain unclear. Therefore, it is critical to understand whether and how antipsychotic drugs used to treat psychosis affect cortical responses to expected and unexpected stimuli. This study provides important insights into this question by identifying a specific cortical cell type and long-range interactions as potential targets. The authors identify layer 5 excitatory neurons as a site where functional effects of antipsychotic drugs manifest. This is particularly interesting as these deep layer neurons have been proposed to play a crucial role in computing the integration of predictions, which is thought to be disrupted in psychosis. This work therefore has the potential to guide future investigations on psychosis and predictive coding towards these layer 5 neurons, and ultimately improve our understanding of the neural basis of psychotic symptoms.

• Broad investigation of different cell types and cortical regions:

One of the major strengths of this study is quasi-systematic approach towards cell types and cortical regions. By analysing a wide range of genetically defined excitatory and inhibitory cell types, the authors were able to identify layer 5 excitatory neurons as exhibiting the strongest responses to unexpected vs. expected stimuli and being the most affected by antipsychotic drugs. Hence, this quasi-systematic approach provides valuable insights into the functional effects of antipsychotic drugs on the brain, and can guide future investigations towards the mechanisms by which these medications affect cortical neurons.

• Bridging theory with experiments

Another strength of this study is its theoretical framework, which is grounded in the predictive coding theory. The authors use this theory as a guiding principle to motivate their experimental approach connecting visual responses in different layers with psychosis and antipsychotic drugs. This integration of theory and experimentation is a powerful approach to tie together the various findings the authors present and to contribute to the development of a coherent model of how the brain processes visual information both in health and in disease.

Weaknesses:

• Unclear relevance for psychosis research

From the study, it remains unclear whether the findings might indeed be able to normalise altered predictive coding in psychosis. Psychosis is characterised by a blunted distinction between predicted and unpredicted stimuli. The results of this study indicate that antipsychotic drugs further blunt the distinction between predicted and unpredicted stimuli, which would suggest that antipsychotic drugs would deteriorate rather than ameliorate the predictive coding deficit found in psychosis. However, these findings were based on observations in wild-type mice at baseline. Given that antipsychotics are thought to have little effects in health but potent antipsychotic effects in psychosis, it seems possible that the presented results might be different in a condition modelling a psychotic state, for example after a dopamine-agonistic or a NMDA-antagonistic challenge. Therefore, future work in models of psychotic states is needed to further investigate the translational relevance of these findings.

• Incomplete testing of predictive coding interpretation

While the investigation of neuronal responses to different visual flow stimuli Is interesting, it remains open whether these responses indeed reflect internal representations in the framework of predictive coding. While the responses are consistent with internal representation as defined by the researchers, i.e., unsigned prediction error signals, an alternative interpretation might be that responses simply reflect sensory bottom-up signals that are more related to some low-level stimulus characteristics than to prediction errors. Moreover, This interpretational uncertainty is compounded by the fact that the used experimental paradigms were not suited to test whether behaviour is impacted as a function of the visual stimulation which makes it difficult to assess what the internal representation of the animal actual was. For these reasons, the observed effects might reflect simple bottom-up sensory processing alterations and not necessarily have any functional consequences. While this potential alternative explanation does not detract from the value of the study, future work would be needed to explain the effect of antipsychotic drugs on responses to visual flow. For example, experimental designs that systematically vary the predictive strength of coupled events or that include a behavioural readout might be more suited to draw from conclusions about whether antipsychotic drugs indeed alter internal representations.

• Methodological constraints of experimental design

While the study findings provide valuable insights into the potential effects of antipsychotic drugs, it is important to acknowledge that there may be some methodological constraints that could impact the interpretation of the results. More specifically, the experimental design does not include a negative control condition or different doses. These conditions would help to ensure that the observed effects are not due to unspecific effects related to injection-induced stress or time, and not confined to a narrow dose range that might or might not reflect therapeutic doses used in humans. Hence, future work is needed to confirm that the observed effects indeed represent specific drug effects that are relevant to antipsychotic action.

Conclusion:

Overall, the results support the idea that antipsychotic drugs affect neural responses to predicted and unpredicted stimuli in deep layers of cortex. Although some future work is required to establish whether this observation can indeed be explained by a drug-specific effect on predictive coding, the study provides important insights into the neural underpinnings of visual processing and antipsychotic drugs, which is expected to guide future investigations on the predictive coding hypothesis of psychosis. This will be of broad interest to neuroscientists working on predictive coding in health and in disease.

We thank the reviewer for the feedback and the help with improving the manuscript.

Regarding the concern of a lack of a negative control, we have repeated the correlation measurement experiments in a cohort of Tlx3-Cre x Ai148 mice that received injections of saline. This analysis is now shown in Figure S6F-S6H. Saline injections did not change correlations in L5 IT neurons. Combined with the absence of changes in the L5 IT correlation structure following amphetamine injections (Figures 7G – 7I), this suggests that unspecific effects related to stress of injection, or simply time, cannot explain the observed decorrelation effect of the antipsychotic drugs.

And we fully agree, a lot more work is needed to confirm that the observed effects are specific and relevant to antipsychotic action.

Reviewer #3 (Public Review):

The study examines how different cell types in various regions of the mouse dorsal cortex respond to visuomotor integration and how antipsychotic drugs impacts these responses. Specifically, in contrast to most cell types, the authors found that activity in Layer 5 intratelencephalic neurons (Tlx3+) and Layer 6 neurons (Ntsr1+) differentiated between open loop and closed loop visuomotor conditions. Focussing on Layer 5 neurons, they found that the activity of these neurons also differentiated between negative and positive prediction errors during visuomotor integration. The authors further demonstrated that the antipsychotic drugs reduced the correlation of Layer 5 neuronal activity across regions of the cortex, and impaired the propagation of visuomotor mismatch responses (specifically, negative prediction errors) across Layer 5 neurons of the cortex, suggesting a decoupling of long-range cortical interactions.

The data when taken as a whole demonstrate that visuomotor integration in deeper cortical layers is different than in superficial layers and is more susceptible to disruption by antipsychotics. Whilst it is already known that deep layers integrate information differently from superficial layers, this study provides more specific insight into these differences. Moreover, this study provides a first step into understanding the potential mechanism by which antipsychotics may exert their effect.

Whilst the paper has several strengths, the robustness of its conclusions is limited by its questionable statistical analyses. A summary of the paper's strengths and weaknesses follow.

Strengths:

The authors perform an extensive investigation of how different cortical cell types (including Layer 2/3, 4 , 5, and 6 excitatory neurons, as well as PV, VIP, and SST inhibitory interneurons) in different cortical areas (including primary and secondary visual areas as well as motor and premotor areas), respond to visuomotor integration. This investigation provides strong support to the idea that deep layer neurons are indeed unique in their computational properties. This large data set will be of considerable interest to neuroscientists interested in cortical processing.

The authors also provide several lines of evidence that visuomotor information is differentially integrated in deep vs. superficial layers. They show that this is true across experimental paradigms of visuomotor processing (open loop, closed loop, mismatch, drifting grating conditions) and experimental manipulations, with the demonstration that Layer 5 visuomotor integration is more sensitive to disruption by the antipsychotic drug clozapine, compared with cortex as a whole.

The study further uses multiple drugs (clozapine, aripiprazole and haloperidol) to bolster its conclusion that antipsychotic drugs disrupt correlated cortical activity in Layer 5 neurons, and further demonstrates that this disruption is specific to antipsychotics, as the psychostimulant amphetamine shows no such effect.

In widefield calcium imaging experiments, the authors effectively control for the impact of hemodynamic occlusions in their results, and try to minimize this impact using a crystal skull preparation, which performs better than traditional glass windows. Moreover, they examine key findings in widefield calcium imaging experiments with two-photon imaging.

Weaknesses:

A critical weakness of the paper is its statistical analysis. The study does not use mice as its independent unit for statistical comparisons but rather relies on other definitions, without appropriate justification, which results in an inflation of sample sizes. For example, in Figure 1, independent samples are defined as locomotion onsets, leading to sample sizes of approx. 400-2000 despite only using 6 mice for the experiment. This is only justified if the data from locomotion onsets within a mouse is actually statistically independent, which the authors do not test for, and which seems unlikely. With such inflated sample sizes, it becomes more likely to find spurious differences between groups as significant. It also remains unclear how many locomotion onsets come from each mouse; the results could be dominated by a small subset of mice with the most locomotion onsets. The more disciplined approach to statistical analysis of the dataset is to average the data associated with locomotion onsets within a mouse, and then use the mouse as an independent unit for statistical comparison. A second example, for instance, is in Figure 2L, where the independent statistical unit is defined as cortical regions instead of mice, with the left and right hemispheres counting as independent samples; again this is not justified. Is the activity of cortical regions within a mouse and across cortical hemispheres really statistically independent? The problem is apparent throughout the manuscript and for each data set collected. An additional statistical issue is that it is unclear if the authors are correcting for the use of multiple statistical tests (as in for example Figure 1L and Figure 2B,D). In general, the use of statistics by the authors is not justified in the text.

Finally, it is important to note that whilst the study demonstrates that antipsychotics may selectively impact visuomotor integration in L5 neurons, it does not show that this effect is necessary or sufficient for the action of antipsychotics; though this is likely beyond the scope of the study it is something for readers to keep in mind.

We thank the reviewer for the feedback and the help with improving the manuscript.

Regarding the concerns of statistical analysis, this may partially be a misunderstanding. We apologize for the lack of clarity. For example, the data in Figures 1F-1K is indeed shown as averaged over locomotion onsets, but there is no statistical analysis performed in these panels. The unit for the statistical analysis shown in Figure 1L is brain area (not locomotion onset). A central tenet of the analysis shown in Figures 1L and 2 is that the effect of differential activation during closed and open loop locomotion onsets is not specific to visual areas of cortex. In visual areas of cortex, one would expect to find a difference. In essence, the surprising finding here is the lack of a difference in other cell types but L5 IT neurons. Thus, in the analyses of those figure panels we are testing whether the effect is present on average across all cortical areas. Hence, we chose the statistical unit of Figure 1L to be cortical areas, not mice. We have added the same analysis with mice as a statistical unit as Figure S4J.

Reviewer #1 (Recommendations For The Authors):

I have a few concerns and questions that I would like to see addressed:

1) Figure 1L - the statistics are a little unusual here as the errors are across visual areas rather than across mice or hemispheres. This isn't ideal as ideally, we want to generalize the results across animals, not areas, and the results seem to be driven mostly by V1/RSC. I would like to see comparisons using mice as the statistical unit either in an ANOVA with areas as factors or post-hoc comparisons per area.

Based on the assumption that visual cortex should respond to visual stimuli, we would have expected to find a difference between closed and open loop locomotion onset responses in all cell types in visual areas of cortex (a closed loop locomotion onset being the combination of locomotion and visual flow onset, while an open loop locomotion onset lacks the visual flow component). Thus, the first surprise was that in most cell types we found very little difference between these two locomotion onset types. Conversely, in Tlx3-positive L5 IT neurons the difference was apparent well outside of the visual areas of cortex (even though the difference was indeed strongest in V1/RSC). To quantify the extent to which closed and open loop locomotion onsets result in different activity patterns across dorsal cortex we performed the analyses shown in Figures 1L and 2. To make the point that the effect was observable on average across cortical areas, we used cortical area as a unit in Figure 1L. We have added the analysis shown in Figure 1L with mice as the statistical unit as Figure S4J and have added the ANOVA information to Table S1, as suggested.

2) The reduction of activity of L5 IT cells in V1 after the presentation of gratings is curious. The authors suggest it might have been due to one population of cells tuned for the orientation of the presented grating suppressing the remaining cells leading to an aggregate negative response. However, they also observed this negative response in the 2p signal for individual somata. Presumably in the 2p data they could check their hypothesis - is there a group of cells that were tuned for the grating? Is it possible that for some reason the L5 IT cells in the 2p were not being activated by the grating because of their RF locations? How large were the gratings - I didn't see this in the methods section?

We can certainly identify neurons that selectively increase activity to one particular grating. See Author response image 1, for vertical and horizontal gratings. The gratings were presented full-field on a toroidal screen that surrounded the mouse (240 degrees horizontal and 100 degrees vertical coverage of the visual field). This covered a large fraction of the field of view of the mouse. While we did not map receptive fields of individual neurons in this study, it is unlikely that the receptive fields of the neurons recorded were outside the stimulated area. We have made this clearer in the manuscript.

Author response image 1.

The population L5 IT neuron response to full-field drifting grating stimuli was a decrease of activity, yet there were increasing responses in a subset of neurons. (A) Heatmap of responses of all L5 IT neuron somata recorded with two-photon imaging in 7 Tlx3-Cre x Ai148 mice to drifting gratings of vertical orientation, sorted by their response. Data were sorted on odd trials and plotted on even trials to avoid regression to the mean artifacts. Dashed black box marks the top 10% responsive neurons. The data are a subset of the data shown in Figure S3D. (B) As in A, but for responses to drifting gratings of horizontal orientation. (C) Responses of top 10% vertical grating responsive neurons (dashed black box in A) to vertical (orange) or horizontal gratings (green). Neurons were selected on odd trials, and the average response of even trials is shown. (D) As in A, but sorted to the response of horizontal drifting gratings. (E) As in D, but for the horizontal grating stimulus. (F) As in C, but for the top 10% horizontal grating responsive neurons.

3) I would caution against over-interpretation of latencies from wide-field GCaMP activity (Figure 3). A weaker response in a smaller population of neurons that has the same latency as a strong response in a large population of neurons will appear to have different latencies when convolved with the GCaMP kernel. Also there doesn't appear to be any statistical support for different latencies in different cortical areas. Either this should be correctly treated (ideally with linear mixed effects models to account for the increased correlation within animals) or the latency conclusions should be removed from the manuscript (my recommendation).

We suspect that by “latency conclusions” the reviewer means “latency analysis”. The only time we mention latency differences is to state that: “In C57BL/6 mice that expressed GCaMP brain wide, both visuomotor mismatch and grating stimuli resulted in increases of activity that were strongest and appeared first in visual regions of dorsal cortex (Figures 3A-3C).”

Nevertheless, we agree with the reviewer that response latency and response amplitude are not independent in our measurements and have replaced the latency plots in Figures 3B, 3C, 3E and 3F with average response maps.

4) Given that the data is baseline corrected, is it possible that the effects of the anti-psychotic drugs on L5IT cells was due to a change in the baseline activity of this population?

While we do find a small increase in average activity as a result of antipsychotic drug injections (Author response image 2), these effects are much smaller than those on locomotion onset responses.

Author response image 2.

On average, activity was increased in dorsal cortex after administration of antipsychotic drugs. Average calcium activity over the entire recording session before (naïve) and after (antipsy.) the administration of antipsychotic drugs. Colored lines indicate paired data for individual mice (Blue: 5 mice that had received clozapine, green: 3 mice that had received aripiprazole, red: 3 mice that had received haloperidol).

To illustrate that the clozapine induced change in locomotion related activity cannot be explained by baseline activity differences, we have replotted the responses shown in Figures 4D and 4E, S3B, S5F without baseline subtraction (Author response image 3).

Author response image 3.

Antipsychotic drug injection only modestly shifts the baseline before locomotion onsets. (A) Average response expressed as F/F0 (wherein F0 was defined as the median of a recording session) during closed (solid line, 1101 onsets) and open loop (dashed line, 348 onsets) locomotion onsets in 5 Tlx3-Cre x Ai148 mice that expressed GCaMP6 in layer L5 IT neurons. Shading indicates SEM over onsets. Dashed horizontal line marks a value of F/F0 of 1.005 for comparison with panel B. Underlying data were the same as in Figures 4D and 4E. (B) As in A, but after a single intraperitoneal injection of the drug clozapine and for 707 closed and 350 open loop locomotion onsets. (C) Average response expressed as F/F0 (wherein F0 was defined as the median of a recording session) of L5 soma in V1, recorded with two-photon imaging in 7 Tlx3-Cre x Ai148 mice that expressed GCaMP6 in L5 IT neurons, during either closed (solid) or open loop (dashed) locomotion onsets. Shading indicates SEM over 8434 neurons. Dashed horizontal line marks a value of F/F0 of 1.045 for comparison with panel D. Underlying data were the same as in Figure S3B. (D) As in C, but for the 3 Tlx3 x Ai148 mice that had received a single intraperitoneal injection of clozapine. Underlying data were from Figure S5F.

5) Figure 5/Figure S6 - Do the results really reflect an effect of distance or is it driven by areas from different hemispheres. Does the result hold if they factor out the effect of hemisphere or calculate the results within hemisphere?

The effect appears qualitatively unchanged when we exclude interhemispheric connections from the analysis (Author response image 4).

Author response image 4.

As in Figures 6D-6F, but with the exclusion of interhemispheric connections. The decorrelation effect appears qualitatively unchanged.

Reviewer #2 (Recommendations For The Authors):

In addition to my public review, I only have one statistics-related and a few minor editing suggestions for the abstract. I hope that these might help the authors to improve their manuscript.

1) It seems that the researchers are combining observations across different subjects, as seen in Figure 1F-L as well as in all of the other figures. While this has been a common practice in their field, it is now widely recognized that this approach can result in biased statistical inferences since it violates the assumptions of most statistical tests (see this recent discussion: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7906290/). As such, it may be beneficial for the authors to consider utilizing statistical tests that are designed to accurately deal with hierarchical data sets, like linear mixed models or hierarchical bootstrap, to confirm their key results. Additionally or alternatively, presenting data grouped by subject would help demonstrate the consistency of their findings across subjects.

Please note, in Figures 1F-1K, there are no statistical tests – but the data are indeed averaged over locomotion onsets across all mice. We could use hierarchical sampling to calculate a bootstrap estimate of the mean response curves and show those instead, but that is also not standard practice in the field. We suspect this is also not what the reviewer is suggesting. In Figure 1L, the unit is indeed brain areas (see also our response to comment 1 of reviewer 1), but it is not areas x mice (i.e., the analysis is not hierarchical).

We have now added a supplementary panel (Figure S4J) that shows the data of Figure 1L with mouse as the statistical unit (note, this is also not hierarchical). We have replaced the statistical test data using bootstrapping, as the reviewer suggests. This information can be found in Table S1.<br /> In Figures 2B and 2D, we have replaced the statistical test with hierarchical bootstrap, and updated the corresponding information in Table S1.

For Figure 3, in which we show mismatch and grating onset responses averaged using onsets as the base unit, we have added supplementary panels (Figure S2) that show the same analysis using mice as the statistical unit. This did not change any of the conclusions. Note, there was no statistical testing in Figure 3.

For the decorrelation effect of the different antipsychotic drugs that we show in Figures 6 and 7 the statistical unit is mice x region pairs (that is, while the structure is hierarchical, all mice contribute the same number of pairs). Our data are underpowered to use hierarchical bootstrap for testing the drug effects individually. However, if we combine all antipsychotic drug data (clozapine, aripiprazole, and haloperidol) we reach the same conclusions with hierarchical bootstrap as with the statistical tests (ttest and ranksum) used in the paper (Author response image 5).

Author response image 5.

Hierarchical bootstrap of the combined distribution of correlation values shown in Figures 6F, 7C and 7F did not change the conclusion that administration of antipsychotic drugs reduces L5 IT neuron correlations. Statistical comparisons using hierarchical bootstrap: Short-range vs no change, p < 0.001; long-range vs no change, p < 0.001; short-range vs longrange, p < 0.05.

2) Given the impressive amount of data, I found it sometimes a little difficult to follow the manuscript. The authors might want to consider including a high-level overview of their results and rationales at the end of the introduction, and start each Results subsection with a sentence referring back to that highlevel overview ("To test whether X, we did Y and present it in this section.")

We have attempted to improve the writing along these lines.

3) Some suggestions that might further improve the clarity of writing.

Abstract: Does the brain really distinguish between different "activity patterns", or would externallygenerated and self-generated "stimuli" be a slightly more accurate term to describe the observed alterations in schizophrenia?

We would argue that (outside of sensory organs) the brain only has access to activity patterns, not stimuli directly. We would prefer to keep the phrasing with activity patterns here.

Line 12: It might be easier to follow if the authors explicitly related that sentence back to the previous sentence "their ability to identify self-generated activity patterns" -> "their ability to distinguish between externally and self/internally generated ..."

Absolutely correct – we have improved the writing here.

Line 14: It remains unclear how visuomotor integration relates to the problem of distinguishing between self- and externally generated stimuli.

We have attempted to expand on this in the abstract.

Line 26: it remains unclear how the results support the activation of "internal representations" as this term has not been defined previously

We have removed “internal representation” from the abstract.

Results, line 80ff: I was confused by the description of all the different investigated cell types, as the first figure panels then only talk about brain wide and L5. Maybe the authors might find that shortening this with a reference to the methods might improve the flow.

We have moved the list of cell types and mouse lines to the methods, as suggested.  

Reviewer #3 (Recommendations For The Authors):

The authors should strongly consider reassessing their statistics as outlined in the Public Review.

Specifically:

1) They should justify their definition of independent statistical unit; if this is not the mouse, they should justify why another definition (i.e. locomotion onset) is used, and show that their defined statistical unit achieves the requirements of being statistically independent (i.e. variance of the unit within a mouse is statistically indistinguishable from variance found between mice; more formally they could calculate the intraclass correlation (ICC)).

We assume the reviewer is referring mainly to Figure 1 and therein to panel 1L.

Since we did not perform statistical tests on the calcium traces, we are not sure why we would need to justify the choice of the unit we were showing. Moreover, Figure S2 shows the data of the V1 ROI averaged over mice to address this concern. As also mentioned to reviewer 2, we have amended this Figure S2 for the mouse-averaged traces of the V1 ROI data shown in main Figure 3.

3) They should justify the statistical tests they use and whether they corrected for multiple comparisons; why for example was an ANOVA not used for Figure 1L and Figure 2B,D?

We did not rely on ANOVA statistics for Figure 1L because we were mainly interested in carving out that Tlx3- (and Ntsr1-) positive mice inhabit a unique space when comparing the similarity of activity during closed and open loop locomotion onsets. We appreciate the reviewer taking a slightly different point of view on the data and now additionally report the ANOVA test result in Table S1. We have also opted to replace the statistical test in Figure 1L with bootstrapping. Lastly, we added Figure S4J which now shows the data in Figure 1L but with mice as the statistical unit.

With similar logic, in Figure 2, we were not interested in comparing how the correlation of activity in cortical regions with locomotion behavior evolves over regions within a visuomotor feedback condition (closed loop, open loop or dark) but rather how a given region compares across feedback conditions.

Still, we have opted to replace the statistical test in Figures 2B and 2D with hierarchical bootstrap, as also suggested by reviewer #2, comment 1. This did not change the significance indicator bars. We have accordingly updated Table S1 in which we report the full statistics.

Author Response

Summary of reviewers recommendations.

Reviewer 1

Point# 1. Make a new section in the text with a figure about the improvement of the genomic information (gene modeling) of ferrets ".

Point# 2. the references to figure S8A, B alright (line 306)?

Point# 3. Revise the main text and figure legends of the section dealing with the human-ferret comparison for clarity.

Reviewer 2

Point# 4. Weaken (change the text from “conclusive” to suggestive” ) the expression that we identified that tRG become ependymal cells, because we have not demonstrated the morphological transformation of a tRG cell into an ependymal cell, which is practically difficult although we have shown morphological change in terms of the single-cilia to multi-cilia form transition (Fig. S6A).

Point# 5. Correct several typos throughout the manuscript that I would recommend fixing for example, page 5 line 123 says "OLIGO2" instead of “OLIG2.

Provisional revision plan and our responses.

Point #1 The new section for the improvement of gene models will be made by transferring the part of methods to the main text and Fig S2B,C to new Figure 1 with one schematic panel.

Point #2; We cited (Bhaduri et al., 2020) as a reference in the figure S8A , while "Bhaduri et, al, 2021” was cited in the text. Which is correct? We will correct this, by choosing the correct one. Descriptions are indeed poor regarding Fig. S8A and S8B in the text as well as in the legends.

Point #3 : We will describe the methods of comparison between ferrets and humans more thoroughly, by adding definition of words such as gene scores, subtype scores in the main text. (as well, the explanation of (Figure S3C) will be improved. ). Legends for Fig. 6 are too simple. So we would explain more in these legends. Explanations of analysis and figures, which we made, responding to the reviewer comments of “review commons” are generally not easy to understand with too short explanations, comparing with complexity of figures and contents, let’s say, Figure S8A-D. We will give more explanations for each of panel in Figure S8A-D, and E and F.

Point #4; The authors' response to this point goes like this; we totally agree that we need to genetically labeling (knocking in the Cryab gene) to prove “tRG cells differentiate ependymal cells”. We tried many times but eventually failed. We have partially show single-cilia to multi-cilia transition which is characteristic to epithelial-ependymal transition. This process appears to take a long time and therefore, morphological tracing by time-lapse imaging in tissue culture is not a realistic way, Therefore, we weakened the conclusion; it is "highly likely" that tRG cells differentiate to be ependymal cells.

Point#5: We will survey typos-> correct them, by all authors read the manuscript carefully again.

Author Response

Thank you for allowing us to submit our manuscript to eLife and for the valuable feedback you have provided. We appreciate your recognition of the importance of our research question and the strengths of this study, including the use of a large sample size and heterogenous male and female rats, as well as the extensive behavioral data. We understand the concerns raised, and we believe that by addressing these concerns, we can further strengthen our manuscript and its contribution to the field of addiction research.

Reviewer #1:

Weaknesses: Language and statistical analysis can be improved.

We acknowledge the concerns regarding language and statistical analysis. In the revised manuscript, we will thoroughly review and improve the language, ensuring clarity and coherence throughout the text. Additionally, we will reevaluate our statistical analysis, address any inconsistencies or shortcomings, and provide a clear explanation of our methods and results.

Reviewer #2:

Because the authors used so many rats (~600), it is not clear how strong the effects are. That is, a large n makes it easy to identify small effect sizes, but no effect sizes are presented regarding the findings.

Concerning the effect sizes, we understand the importance of providing this information. In the revised manuscript, we will include effect sizes for our findings to better illustrate the magnitude of the observed effects and their practical significance.

The Discussion includes parts that argue that the extended access model is a better model of addiction than short access and suggests that this paper provides support for that. However, there were no rats given short-access for the same period of time as the rats in this paper - i.e., no comparison group. Rather, the only comparison that can be made is as the rats transition from short to long access. The data in Figure 1B appear to show that the rats continue their increase in cocaine intake when they transition from short access to long access. The authors do not provide any statistical analyses about this escalation of intake during short access. However, they claim that "measures related to short-term cocaine intake" were orthogonal to those collected during longer access periods, yet it is not clear to me what measures those are. Nonetheless, as indicated in Figure 1H, it appears that the rats consistently shift from PC1 to PC2 across self-administration, regardless of whether they are in the short or long access period.

That is, the long-access measures appear to simply be a continuation of the pattern begun during short access. As a result, notwithstanding the lack of a true short-access control group, it is difficult to see how the authors can draw conclusions about short vs. long access in this paper. Moreover, as illustrated in Figure 3A, the resilient vs. vulnerable subtypes are apparent during short access self-administration (i.e., they do not require long-access self-administration to develop or be revealed). This suggests, if anything, that short access would be sufficient for identifying such groups. Similarly, Figure 5 shows that short access would be sufficient to identify the "low" vulnerability quartile vs. the other three groups.

We appreciate the concerns raised regarding the comparison between short and long access conditions. Note that the goal of the study was not to specifically compare short vs long access, but instead evaluate the relationship between addiction-like behaviors after long access. In the revised manuscript, we will focus on these findings and present a more accurate representation of the behavioral changes observed between short and long access conditions. By doing so, we believe that our conclusions will be better supported by the data, and our manuscript will provide a more comprehensive understanding of the factors contributing to addiction-like behaviors.

During the discussion, the authors briefly discuss gender differences with regard to cocaine use disorder, with the authors trying to claim that women may be more vulnerable to cocaine use disorder. However, the two papers cited do not support that, as they are papers with rodents. A recent comprehensive review on humans with regard to cocaine craving and relapse noted no reliable gender differences (Nicolas et al., 2022, Pharmacological Reviews) and, as the authors themselves noted, men suffer from cocaine use disorder at higher rates than women.

We apologize for any confusion regarding the discussion of sex differences in cocaine use disorder. We will revise this section in the manuscript to better reflect the current literature on human sex differences in cocaine craving and relapse, as well as the prevalence of cocaine use disorder.

The authors noted that the rats received 0.5 mg/kg/infusion of cocaine but provided no explanation for how this dosing was maintained (or whether it was maintained) across the length of the study. Considering that rats, especially males, increase in size quite a bit during this stage, this could affect measures like intake as well as skew sex difference results. Likewise, the data are presented strictly in the number of cocaine infusions, which does not allow for consideration of body weight.

In response to the concern about maintaining the 0.5 mg/kg/infusion cocaine dose throughout the study, we will explain our dosing procedures and any adjustments made to account for changes in body weight. Additionally, we will consider presenting data in terms of total cocaine intake (mg/kg) to account for potential differences in body weight between animals and sexes.

In the Introduction, the authors make a number of arguments in the second paragraph that have no citations and, therefore, are unsupported.

We will ensure that all statements in the Introduction are supported by appropriate citations, providing a solid foundation for our research question and the significance of our study.

Reviewer #3:

There are a number of factors - such as behavioral rate - that are not considered and likely co-vary with other measures. This is critical as previous work has shown that rate of behavior in reinforcement tasks is a large determinant of sensitivity to both drug effects on that behavior and punishers. This is not considered and but additional information and tempering the interpretation of the data would further strengthen the manuscript.

We understand the concern regarding the potential influence of behavioral rates on our findings. In the revised manuscript, we will consider the impact of behavioral rates on our measures and discuss how they may have affected the results. By addressing this concern, we believe it will further strengthen the manuscript and provide a more comprehensive understanding of the factors contributing to addiction-like behaviors.

We are confident that addressing these concerns will significantly improve our manuscript and provide a more robust and accurate representation of our findings. We appreciate the constructive feedback from the reviewers and look forward to submitting our revised manuscript to eLife.

Author Response

The following is the authors’ response to the original reviews

Reviewer #1 (Recommendations for the authors):

Major Concerns:

1) There are numerous grammatical issues throughout the manuscript, and too much awkward jargon is used, such as "status of energy stresses", "ES-acetate". The characterization of acetate as an "energy stress" gives a negative connotation, which is unnecessary and confusing. Ketones are produced under the same circumstances but are a vital adaptive response, except for ketoacidosis. The terminology used throughout the manuscript is also vague, and some methodology is not adequately described in the Methods section. For example, the meaning of "preprandial" and "postprandial" is unclear, and there is no explanation of the related methodology.

Thank you for your comments. We have replaced "status of energy stresses" with "energy stresses", in our revised manuscript. We agree with you that acetate and Ketone Bodies are produced under the same circumstances and their production is a result of a vital adaptive response. It is well known that the production of large amount of acetate and Ketone Bodies is an important physiological adaption of body in response to energy stresses such as prolonged starvation and untreated diabetes mellitus. In this context, we use “energy stress-acetate”, a term coined by ourselves to emphasize the condition of acetate production and its role under such condition. Based on your concerns, we have addressed the issues and provided a thorough description of the modifications made in the Methods section.

2) The authors claim that acetate is a ketone body, which is incorrect. As the authors show, it is not produced by the ketogenic pathway or from the breakdown of ketones. Acetate is a carboxylic acid and specifically a short-chain fatty acid.

We agree with you that our description of acetate as a ketone body is seemingly incorrect. Indeed, acetate is a short-chain fatty acid in terms of molecular structure. The classic Ketone Bodies include acetone, acetoacetate and beta-hydroxybutyrate, among which acetone and acetoacetate contain carbonyl group and can be considered as ketone, however beta-hydroxybutyrate which contains only hydroxyl and carboxyl groups is actually not a ketone but a short-chain fatty acid. Noteworthily, here our description of acetate as an emerging novel “ketone body” is not aimed to consider it as a real ketone in structure, but to emphasize the high similarity of acetate and the classic Ketone Bodies in the organ (liver) and substrate (fatty acids-derived acetyl-CoA) of their production, the roles they played (as important sources of fuel and energy for many extrahepatic peripheral organs), the feature of their catabolism (converted back to acetyl-CoA and degraded in TCA cycle), as well as the physiological conditions of their production (energy stresses such as prolonged starvation and untreated diabetes mellitus). To prevent any potential misunderstanding, we annotate the usage of "ketone body" with double quotation marks in our revised manuscript.

3) The human subjects are not sufficiently characterized, and it is unclear whether they are T1DM or T2DM subjects. No information is provided on morphometrics, how and when serum was collected, exclusion criteria, medicines, etc. Proper characterization of human subjects is necessary before publishing such data.

Thank you very much for your comments. We have added the description of subjects you mentioned in the Methods section.

4) While Figure 4 is an essential set of experiments that demonstrate that ACOT12 is necessary for the induction of acetate during starvation in mice, the authors do not explain the source of basal levels of acetate that persist in mice lacking ACOT12. It is unclear whether this source is from other tissue or microbiota. Since loss of ACOT by ShRNA treatment resulted in ~25% reduction in acetate, it is very difficult to conceive how this produces the profound neurological and strength deficits presented in Supplemental Figure 8 (see last point below).

Additionally, it is not clear how the control mice for the knockout studies were generated. Please clarify.

In normal condition, the serum acetate level in mice is around 200 μM. Hepatic ACOT12 and ACOT8 enzymes seems to provide a serum acetate concentration of 60-90 μM, individually (Figure 4). The intestinal microbiota contributes a serum acetate concentration of 60-80 μM (Figure 2 and Figure supplement 1).

During energy stress, the protein levels of ACOT12 and ACOT8 in the mouse liver were significantly upregulated (Figure 3 and Figure supplement 1), resulting in an significant increase of serum acetate level to approximate 400 μM. The acetate produced by ACOT12 (~200 μM) and ACOT8 (~200 μM) constitutes the main portion of serum acetate concentration under such condition (Figure 2), while the contribution of intestinal microbiota to serum acetate level is minimized (Figure 2 and Figure supplement 1). Elimination of either ACOT12 or ACOT8 reduces serum acetate level by up to 50% (Figure 4). However, such estimation is only a rough approximation and does not consider the possibility of compensatory upregulation of ACOT12 and ACOT8 in kidney when ACOT12 or ACOT8 is knocked out in liver.

Acetate assumes the role as an important energy source in the case of reduced glucose utilization associated with diabetes. In this case, knockdown of ACOT12 or ACOT8 (shACOT12 or shACOT8) can remarkably reduce acetate production and consequently influence the Motor Function of mice to a certain extent.

5) The results presented in Figure 5 are confusing, and the authors' interpretation needs elaboration. The FAO assay detects water-soluble 3H-metabolites and 3H2O, and etimoxir or CPT1 knockout completely inhibits FAO. Therefore, it is unclear how peroxisomes can produce acetate without generating water-soluble intermediates that are detectable in the assay. Further explanation and rationale for the authors' interpretation are necessary.

Mitochondria serve as the primary organelle for the catabolism of oleic acid. However, in certain instances, fatty acid oxidation (FAO) can occur in the peroxisome, resulting in the production of medium-chain fatty acids and acetyl-CoA. Nevertheless, these medium-chain fatty acids cannot undergo further oxidation within the peroxisome. Instead, they must be transported out of the peroxisome and then into the mitochondria through CPT1 (carnitine palmitoyltransferase 1) for further oxidation.

To assess FAO, we utilized a detection method based on 3H labeling in H2O in cells treated with [9,10-3H(N)]-oleic acid. The introduction of [9,10-3H(N)]-oleic acid leads to the production of 3H-labeled medium-chain fatty acids and acetyl-CoA within the peroxisome. The further oxidation of 3H-labeled medium-chain fatty acids in the mitochondria was inhibited by impeding the activity of CPT1, leading to the eventual decrease of 3H-labeled H2O. However, acetyl-CoA can still be converted to acetate by ACOT8. As a result, knockdown or etomoxir inhibition of CPT1, decreased more than one-half of U-13C-palmitate-derived U-13C-acetate production, in spite of mitochondria β-oxidation being nearly completely abolished.

6) Figure 6F, which shows various fatty acyl-CoAs in MPHs, is not helpful on its own. It would be useful to compare this data to loss of function MPH data and to measure these acyl-CoAs in knockout liver. Additionally, since it is normal for liver acetyl-CoA concentration to change by several-fold in fasted and fed liver, this data from snap frozen liver tissue of ACOT12/8 KO mice would help prove the authors' point.

We are grateful for your valuable advice. As you mentioned there are indeed several outstanding questions that require further clarification. To address these questions, we are currently in the process of developing an experimental mouse model in which ACOT12 and ACOT8 are conditionally knocked out. By virtue of this approach, we aim to acquire more substantial evidence to substantiate the aforementioned conclusions.

7) Figure 7 suggests that loss of ACOT inhibits ketogenesis by decreasing HMGCS2 expression and increasing its acetylation. However, it is difficult to imagine that this the main mechanism considering the extraordinary ability of liver to handle high rates of acetyl-CoA conversion to ketones during fasting which, as the authors know, is the canonical mechanism by which mitochondrial CoA is preserved during elevated FAO. The manuscript (Figure 6 and 7) argues that it is the conversion of acetyl-CoA to acetate which is more important. A critical limitation of this argument is that ACOT12 is in cytosol (Figure 5), so while it spares CoA for fatty acid activation, it does not spare CoA for beta oxidation in mitochondria. That latter function is carried out by the ketogenic pathway. A second limitation is that the mechanism relies on citrate transport and ACLY activity, which is not generally thought to be very active in the ketogenic states of fasting and T1DM studied here. In essence, the mechanism relies on circular logic, whereby mitochondrial acetyl-CoA accumulates in the setting of impaired FAO, which then impairs ketogenesis and depletes CoA which then impairs FAO without lowering acetyl-CoA. I don't have a solution, but I think it is important to acknowledge the flaws in this proposed mechanism.

As the Reviewer suggested, ACLY indeed plays a crucial role in fatty acid synthesis. Acetyl-CoA is transported out of the mitochondria in the form of citrate, which is subsequently broken down into acetyl-CoA by ACLY. Under conditions of sufficient nutrition, acetyl-CoA carboxylase 1 further activates acetyl-CoA to participate in fatty acid synthesis.

In the context of an energy crisis resulting from low glucose utilization, we propose that ACLY might serve another pivotal role in addressing this energy deficit. In conditions such as untreated diabetes or prolonged starvation, glucose utilization is significantly reduced, leading to a reliance of body on fatty acid oxidation in liver to generate Ketone Bodies and acetate to fuels extrahepatic peripheral tissues and thus cope with the energy crisis. However, excessive fatty acid oxidation disrupts the balance between oxidized and reduced CoA, necessitating the production of both acetate and Ketone bodies to restore this equilibrium. Conventionally, fatty acid synthesis is inhibited during this period as AMPK is activated to suppress acetyl-CoA carboxylase 1 activity via phosphorylation in low-energy states. Based on our preliminary experimental results, the activity of ACLY and citrate transporter still appear to work well. It is possible that citrate-ACLY-ACOT12-acetate pathway is important for downregulating the level of mitochondria acetyl-CoA in energy crisis. According to previous studies, cytosolic reduced CoA has the capability to be transported into the mitochondria, thereby replenishing the acetyl-CoA pool within the mitochondria (PMID: 32234503). It is important to note that this remains a hypothesis requiring further testing.

8) Figure 8 presents some deceptively complex MS data following a 13C-acetate injection. The data is presented in an unorthodox manner, as 13C-metabolite intensities, making it nearly impossible to properly interpret. Enrichment of TCA cycle intermediates are not always easy to interpret, but at minimum, this data needs to be presented as MIDs or fractional enrichments. If the data is not modeled, then it might be useful to at least perform a rudimentary precursor-product analysis (i.e. normalized to plasma acetate enrichment).

Supplemental Figure 8 also introduces evidence for neurological and strength deficits in shACOT12/8 knockdown mice. It is an interesting observation, but there is no direct link to the metabolic studies in the main figure, which does not present data in the loss of function mice. Nor is this part of the story investigated in liver specific knockout mice. Figure 8 is the least developed part of the manuscript and could be removed without losing the impact of the story.

We deeply appreciate your valuable suggestions. As mentioned previously, we are currently engaged in the development of an experimental mouse model where ACOT12 and ACOT8 are selectively knocked out. Subsequent experiments will be conducted to validate this model, and the resulting data will be presented in the form of MIDs or fractional enrichments, as per your suggestion.

The evaluation of anxiety-related behavior is commonly done using the Elevated Plus Maze Test (EPMT), while working memory and cognitive functions are assessed through the Y-maze Test (YMZT) and Novel Object Recognition (NOR) Test. Measures such as forelimb strength and running time in the rotarod test, total distance in YMZT, total entries in YMZT, and total distance in the NOR test are indicators of muscle force and movement ability. Our data demonstrate that acetate plays a significant role in enhancing muscle force and facilitating coordinated neuromuscular movement. Interestingly, we found that ACOT12/8 knockdown in the early stages of diabetes mellitus does not have a pronounced impact on psychiatric, memory, and cognitive behaviors (Figure 8 and figure supplement 2). However, it is important to note that our study primarily focuses on elucidating the utilization of acetate during energy crises, such as untreated diabetes and chronic hunger. Our findings suggest that acetate is primarily utilized to enhance motor capacity rather than cognitive or neural activity.

Reviewer #2 (Recommendations for the authors):

The statement that acetate is an emerging ketone body is not correct. It is not a ketone, it is a carboxylic acid or a short-chain fatty acid. In my opinion, to avoid confusion this should be clarified.

We agree with you that our description of this is not clear enough. Acetate is a short-chain fatty acid in terms of molecular structure indeed.

The classic Ketone Bodies include acetone, acetoacetate and beta-hydroxybutyrate, among which acetone and acetoacetate contain carbonyl group and can be considered as ketone, however beta-hydroxybutyrate which contains only hydroxyl and carboxyl groups is actually not a ketone but a short-chain fatty acid.

Noteworthily, here our description of acetate as an emerging novel “ketone body” is not aimed to consider it as a real ketone in structure, but to emphasize the high similarity of acetate and the classic Ketone Bodies in the organ (liver) and substrate (fatty acids-derived acetyl-CoA) of their production, the roles they played (as important sources of fuel and energy for many extrahepatic peripheral organs), the feature of their catabolism (converted back to acetyl-CoA and degraded in TCA cycle), as well as the physiological conditions of their production (energy stresses such as prolonged starvation and untreated diabetes mellitus). To prevent any potential misunderstanding, we annotate the usage of "ketone body" with double quotation marks in our revised manuscript.

The reason for increased fatty acid delivery to the liver is explained by insulin resistance rather than by reduced carbohydrate availability.

Patient characteristics should be provided.

Thank you for your suggestions. We have revised our manuscript accordingly.

Reviewer #3 (Recommendations for the authors):

• Please include the rationale for having data from both C57BL/6 and BALC/c. In metabolic research, C57BL/6 is more commonly studied. The data between these two strains are similar, and one could be easily removed to limit redundancy.

Thank you for bringing this issue to our attention in the manuscript. In metabolic research, C57BL/6 mice are more commonly utilized as a model organism than BALC/c mice indeed. In this study we try to elucidate a characteristic may be shared among different mammalian species, namely the ability to produce a substantial amount of acetate during energy crises. However, given the constraints of our experimental setup, we opted to employ C57BL/6 mice as the main animal model to investigate the underlying mechanism. BALC/c mice were used to confirm the underlying mechanisms governing acetic acid production.

• In the experiments where ACOT8 and ACOT12 are selectively knocked out or knocked down, please include the levels of other ketone bodies, such as 3-HB and AcAC, from these experiments. While acetate production is diminished, there might or might not be a compensatory increase in the production of these metabolites. This would include experiments related to Figures 3, 4, and 5.

Thank you for your valuable comments. As you mentioned, in diabetic mice where ACOT12 and ACOT8 are knocked down in liver, there is a significant down-regulation of 3-HB and AcAc (Figure 7B, C). Based on this observation, we hypothesize that ACOT12 and ACOT8 might also play a regulatory role in the formation and metabolism of ketone bodies during an energy crisis. However, the precise regulatory mechanism underlying this phenomenon requires further investigation.

• From Figure 1 (source data 1), two patients with diabetes have concurrent cancer. Cancer cells have altered metabolism compared to native cells. Thus, it is possible that circulating acetate cells may be altered in these cancer patients, regardless of the presence of diabetes. This should be acknowledged. Otherwise, these two subjects should be taken out.

Thank you for your suggestions. We have taken out these two subjects in our revised manuscript.

• Can the authors expand on their thoughts on why some results from the behavioral tests are statistically significant while others are not? For example, many motor tasks such as forelimb strength, running time, total distance, and total entries significantly differ with ACOT8 and ACOT12 knockdown. However, more anxiety-based measures such as time in open arms, correct alteration, and object recognition are not statistically different.

Thank you for your comments. The evaluation of anxiety-related behavior is commonly done using the Elevated Plus Maze Test (EPMT), while working memory and cognitive functions are assessed through the Y-maze Test (YMZT) and Novel Object Recognition (NOR) Test. Measures such as forelimb strength and running time in the rotarod test, total distance in YMZT, total entries in YMZT and total distance in the NOR test are indicators of muscle force and movement ability. Our data demonstrate that acetate plays a significant role in enhancing muscle force and facilitating coordinated neuromuscular movement. Interestingly, we found that ACOT12/8 knockdown in the early stages of diabetes mellitus does not have a pronounced impact on psychiatric, memory, and cognitive behaviors (Figure 8 and figure supplement 2). However, it is important to note that our study primarily focuses on elucidating the utilization of acetate during energy crises, such as untreated diabetes and chronic hunger. Our findings suggest that acetate is primarily utilized to enhance motor capacity rather than cognitive or neural activity.

Author Response

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

We want to thank you for organizing the review process a of our manuscript ‘Human skeletal muscle organoids model fetal myogenesis and sustain uncommitted PAX7+ myogenic progenitor’ for eLife and the reviewers for providing their criticisms.

We have changed some Figures within the manuscript and added two new Supplementary Figures as outlined below

Reviewer #1 (Public Review):

The authors aimed to establish a cell culture system to investigate muscle tissue development and homeostasis. They successfully developed a complex 3D cell model and conducted a comprehensive molecular and functional characterization. This approach represents a critical initial step towards using human cells, rather than animals, to study muscular disorders in vitro. Although the current protocol is time-consuming and the fetal cell model may not be mature enough to study adult-onset diseases, it nonetheless provides a valuable foundation for future disease modelling studies using isogenic iPSC lines or patient-derived cells with specific mutations. The manuscript does not explore whether or how this stem cell model can advance our understanding of muscular diseases, which would be an exciting avenue for future research. Overall, the detailed protocol presented in this paper will be useful for informing future studies and provides an important resource to the stem cells community. The inclusion of data on disease modelling using isogenic iPSC lines or patient-derived cells would further enhance the manuscript's impact.

We agree, that data on disease modelling using patient-derived cells would further enhance the manuscript's impact. The manuscript in its current form should present our skeletal muscle organoid differentiation protocol to the community with a focus of the developmental processes which are mimiced by this model. We are not aiming to disease model e.g. LGMD or Duchenne within the context of this study. Our protocol is just the starting point of us and others to use this organoid protocol for skeletal muscle disease modelling in further studies. We already have a study of Duchenne musculular dystrophy modelling using our organoid system under way.

Reviewer #2 (Public Review):

This paper illustrates that PSCs can model myogenesis in vitro by mimicking the in vivo development of the somite and dermomyotome. The advantages of this 3D system include (1) better structural distinctions, (2) the persistence of progenitors, and (3) the spatial distribution (e.g. migration, confinement) of progenitors. The finding is important with the implication in disease modeling. Indeed the authors tried DMD model although it suffered the lack of deeper characterization.

The differentiation protocol is based on a current understanding of myogenesis and compelling. They characterized the organoids in depth (e.g. many time points and immunofluorescence). The evidence is solid, and can be improved more by rigorous analyses and descriptions as described below.

Major comments:

1) Consistency between different cell lines.

I see the authors used a few different PSC lines. Since organoid efficiency differ between lines, it is important to note the consistency between lines.

2) Heterogeneity among each organoid

Let's say authors get 10 organoids in one well. Are they similar to each other? Does each organoid possess similar composition of cells? To determine the heterogeneity, the authors could try either FACS or multiple sectioning of each organoid.

Concerning the raised issue of consistency between different PSC lines we stated under Material and Methods that skeletal muscle organoids were generated from six hiPSC lines: CB-CD34 iPSC, DMD iPSC, DMD_iPS1, BMD_iPS1, LGMD2A iPSC, LGMD2A-isogenic iPSC. We have evaluated the organoid approach with six hiPSC lines with independent genetic backgrounds with more than 5 independent derivations per line, for the control line (CB CD34+) with more than 20 derivations. At the time of creating the first preprint in 2020 our reported protocol was based on about 45 independent differentiation inductions.

The heterogeneity among each organoid is a valid point, however very cumbersome to address with FACS or multiple sectioning.

We have now addressed the heterogeneity of organoids within a line and the consistency of organoids between different lines by diffusion map analysis for early organoid stages and further single cell RNA seq analyses for mature stages and include this data as Figure 4 – figure supplement 6.

3) Consistency of Ach current between organoids.

Related to comment 2, are the currents consistent between each organoid? How many organoids were recorded in the figures? Also, please comment if the current differ between young and aged organoids.

The acetylcholine (ACh)-induced changes in holding currents in Figure 3K are representative recordings with n=6. The further recordings in Figure 3 – Figure Supplemental 3 for organoids derived from three additional lines, were also recorded with n=6. Cells were taken for electrophysiological characterization in all analyses from 8 weeks organoids.

4) Communication between neural cells and muscle?

The authors did scRNAseq, but have not gone deep analysis. I would recommend doing Receptorligand mapping and address if neural cells and muscle are interacting.

We are now providing a characterization of the cell-cell communication network for all clusters at week 12 of human skeletal muscle organoid development as the new Figure 4 – figure supplement 5.

5) More characterization of DMD organoids.

One of the key applications of muscle organoids is disease model. They have generated DMD muscle organoids, but rarely characterized except for currents. I recommend conducting immunofluorescence of DMA organoids to confirm structure change. Very intriguing to see scRNAseq of DMD organoids and align with disease etiology.

We agree, that data on disease modelling using DMD patient-derived cells would further enhance the manuscript's impact. The manuscript in its current form should present our skeletal muscle organoid differentiation protocol to the community with a focus of the developmental processes which are mimiced by this model. We already have a study of Duchenne muscular dystrophy modelling using our organoid system under way.

6) More characterization of engraft.

Authors could measure the size of myotube between mice and human.

We have quantitatively evaluated the myotubes in the transplantation experiment illustrated in Figure 4I,J. The mean diameter is 41+/-6 µm for the human and 63+/-7 µm for the mice fibers (n=15 each). See Author response image 1.

Author response image 1.

Does PAX7+ satellite cell exist in engraft? To exclude cell fusion events make up the observation, I recommend to engraft in GFP+ immunodeficient mice. Could the authors comment how long engraft survive.

We would claim satellite cells within our engrafts with the DAPI-blue nuclei surrounded by green human lamin A/C as in Author response image 2. We have analysed all our mice six weeks post transplantation for engrafting similar to other groups in the field.

Author response image 2.

Reviewer #1 (Recommendations For The Authors):

The manuscript ends abruptly with the mouse transplantation experiment that appears a bit preliminary. It basically shows that cells survive but functional (or ultrastructural) integration is not shown. Suggest clarifying motivation and interpretation of the in vivo data.

Back in 2020 our manuscript had already passed detailed review processes whereby we struggled by not providing any in vivo data concerning repopulation of our progenitor cells. Coming from the human pluripotent stem cell biology field we have never completely understood the value of this hybrid experiments to test human cells in mouse again.

For the current version, we have then taken additional efforts to transplant our progenitor cells into injured skeletal muscle cells similarly to other groups in the field (Alexander et al., 2016, Marg et al., 2019, Tanoury et al., 2020) (Figure 4I,J). A proof that 3D-derived progenitor cells have a clear repopulation advantage over progenitor cells derived in a 2D protocol would go beyond what can be done within the scope of our study. We are still mainly basing our claims on the extended bulk and single RNA seq comparison to progenitor cells obtained by others. However, to address the demand of several experts to test our cells also in vivo, we can also provide in vivo data in the current manuscript version.

Within the Discussion we are suggesting further evaluations using these transplantations: It would be of interest for future studies to investigate whether increased engraftment can be achieved in 3D protocols (Faustino Martins et al., 2020; Shahriyari et al., 2022; ours) versus 2D patterned progenitor cells.

Reviewer #2 (Recommendations For The Authors):

Minor comments:

7) Plot CD82 gene on UMAP of Figure 4

We had provided a CD82 scRNAseq analysis within the t-SNE plots of Figure 3 – figure supplement 1, which is demonstrating, that CD82-positive cells almost exclusively overlap with Pax7-positive cells, being a subcluster of them. We agree, that the reader will benefit from this further analysis and we are now providing in Author response image 3 additional CD82 and Pax7 UMAP plots on the myogenic progenitor / satellite cell clustering analysis of Figure 4F within the new Figure 4 – figure supplement 4E.

Author response image 3.

8) Immunofluorescence of CD82 in organoids

We have tried CD82 immunofluorescence analysis on our organoids but are not very satisfied with the technical outcome. The available CD82 antibody seems to be primarily suited for FACS analysis and not for immunohistochemistry on slices.

9) Change red-green color of the heatmap. Color-blind person cannot see it well

We have changed all heatmaps to yellow-purple in the main Figure 2G and the Supplemental Figures S2.1 and S3.1..

Author Response

We are pleased that the data presented in our submission was found to be informative and suitable for publication in eLife. The Reviewers made several comments that we address below. They listed three weaknesses of our work: 1) details of RPE GLUT1 immunohistochemistry (IHC), 2) the mechanism of Arrdc4, and 3) the mechanism of HSP90AB1. Additional suggestions made by the Reviewers, aimed at elucidating mechanisms, are of great interest to us, but would require experiments that are beyond the scope of the current work.

We provide the following provisional responses to the identified weaknesses:

1) Reviewer 1 asked several questions regarding the IHC of GLUT1, including the number of retinas examined, the location and quantification of the staining, and our results relative to those of another publication.

We injected more than one eye with each of the AAV-Best1-Txnip alleles.

However, only one of the fully infected eyes of each allele was processed for GLUT1 IHC. We found the GLUT1 removal from the basolateral surface of the RPE by AAV-Best1-Txnip (i.e. the wild type full length allele) was complete, obvious, and consistent from eye to eye, as shown in our original publication (Xue et al., 2021, PMID: 33847261). It was obvious as the GLUT1 on the basolateral surface of the RPE is more easily scored than that on the apical surface. The photoreceptor inner segments and Müller glia microvilli also have GLUT1, and their processes are juxtaposed and/or intertwined with the apical processes of the RPE, making the apical process GLUT1 staining of the RPE much more difficult to score. In some sections where the RPE and the retina separate, we can score the apical process GLUT1 staining of the RPE, but we do not always have this situation in our sections. We should have been more explicit about the location of the IHC signal that we were referring to in the manuscript and will do so in the Revision.

We present images in Figure 2 supplement 1 that are representative for each allele, in the one retina scored for each allele. As Dr. Xue was in the process of moving to China and setting up his own lab at the time of submission, additional retinas were not processed for IHC. However, his laboratory will examine the staining on additional retinas. Given that the results of the wild type allele were very reproducible, we do not anticipate different results from those we have presented for the new alleles. However, the quantification is difficult for the total GLUT1 protein within the RPE due to the ambiguities of staining in the photoreceptors and the Müller glia.

As a separate issue, Reviewer #1 mentioned the work of another group (Wang et al., 2019, PMID: 31365873), which claimed that, on the apical surface of the RPE, GLUT1 is down-regulated in a RP mouse strain, RhoP23H. We have not consistently observed such a down-regulation of GLUT1 in other RP mouse strains such as rd1, rd10 or Rho-/- (unpublished data; see review Xue and Cepko, 2023, PMID: 37460158). However, we would like to point out that it is difficult to score GLUT1 staining on the RPE apical surface, as noted above. It is even more difficult in the degenerating retina where RPE and photoreceptor processes degenerate. For reference, one can see images of degenerating RPE apical processes in Wu et al. 2021 (PMID: 33491671).

2) Little was known about the function of Arrdc4 until very recently. During our submission of this manuscript, a study was published concerning an Arrdc4 global knockout mouse by Richard Lee’s group. They proposed that Arrdc4 is critical for liver glucagon signaling, which could be negated by insulin (Dagdeviren et al, 2023, PMID: 37451484). The implication of this study to RP cone survival is unclear, but interestingly, the activation of insulin/mTORC1 pathway is helpful for RP cone survival, as first discovered by Claudio Punzo when a postdoc in our group (PMID: 19060896, PMID: 25798619).

3) Little is known about the function of HSP90AB1. Recently, Ramamurthy’s group reported that knocking out HSP90AA1, a paralog of HSP90AB1 which has 14% different amino acids, led to rod death and correlated with PDE6 dysregulation (Munezero et al, 2023, PMID: 37172722). However, the exact role of HSP90AA1 in rods needs to be clarified, and the implications for HSP90AB1 in WT and/or RP cones are still unclear.

The above responses will be incorporated to our next version of submission.

Author Response

Reviewer #1 (Public Review):

The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.

Unfortunately, studies conducted in South America to understand host use by Culex mosquitoes are very limited, and there are virtually no studies on the seasonal pattern of host use. In Argentina, there is some evidence (Stein et al., 2013; Beranek, 2018) regarding the seasonal change in host use by Culex species, including Culex quinquefasciatus, where the inclusion of mammals during the autumn has been observed. As part of a comprehensive study on characterizing bridge vectors for SLE and WN viruses, our research group is currently working on the molecular identification of blood meals from engorged females to gain deeper insights into the seasonal host use by Culex mosquitoes.

While the seasonal change in host use by Culex quinquefasciatus has not been reported in Argentina so far, there has been an observed increase in reported cases of SLE virus in humans between summer and autumn (Spinsanti et al., 2008). It is based on this evidence that we hypothesize there is a seasonal change in host use by Culex quinquefasciatus, similar to what occurs in the United States. This is also considering that both countries (Argentina and the United States) have regions with similar climatic conditions (temperate climates with thermal and hydrological seasonality).

I think the authors need to discuss more about the bigger question they were addressing. I think that the discussion section can be strengthened greatly by elaborating on whether there is evidence for a seasonal shift in host use pattern in Cx. quinquefasciatus in the southern latitudes. If yes, what alternate mechanisms they believe could be driving the seasonal change in host use in this species in the southern latitudes now that they show the 'deriving reproductive advantages' hypothesis to be not true for those populations.

We will restructure our discussion to align it with our results, as suggested.

Grammar and writing

The manuscript will be grammatically revised.

Reviewer #2 (Public Review):

There is no replication built into this study. Egg lay is a highly variable trait, even within treatments, so it is important to see replication of the effects of treatment across multiple discrete replicates. It is standard practice to replicate mosquito fitness experiments for this reason. Furthermore, the sample size was particularly small for some groups (e.g. 15 egg rafts for the second gonotrophic cycle of mice in the autumn, which was the only group for which a decrease in fecundity and fertility was detected between 1st and 2nd gonotrophic cycles). Replicates also allow investigators to change around other variables that might impact the results for unknown reasons; for example, the incubators used for fall/summer conditions can be swapped, ensuring that the observed effects are not artifacts of other differences between treatments. While most groups had robust sample sizes, I do not trust the replicability of the results without experimental replication within the study.

We agree egg lay is a variable trait and so we consider high numbers of mosquitoes and egg lay during experiments compared to our studies of the same topics. Evaluating variables such as fecundity, fertility, or other types of variables (collectively referred to as "life tables") is a challenging issue that depends on several intrinsic and extrinsic factors. Because of all of this, in some experiments, sample sizes might not be very large, and in several articles, lower sample sizes could be found. For instance, in Richards et al. (2012), for Culex quinquefasciatus, during the second gonotrophic cycle, some experiments had 13 or even 6 egg rafts. For species like Aedes aegypti, the sample size for life table analysis is also usually small. As an example, Muttis et al. (2018) reported between 1 and 4 engorged females (without replicates). Because of this, we do find our sample sizes quite robust for our results.

Regarding the need to repeat the experiments in order to give more robustness to the study we also agree. However, after a review of the literature (articles cited in the original manuscript), it is apparent that similar experiments are not frequently repeated as such. Examples of this are the studies of Richards et al. (2012), Demirci et al. (2014) or Telang & Skinner (2019), which even manipulate several cages at a time as “replicates”, they are not true replicates because they summarise and manipulate all data together, and do not repeat the experiment several times. We see these “replicates” as a way of getting a greater N.

As it was stated by the reviewer, repetition is a resource and time consuming activity that we are not able to do. Replicating the experiment poses a significant time challenge. The original experiment took over three months to complete, and it is anticipated that a similar timeframe would be necessary for each replication (6 months in total considering two more replicates). Given our existing commitments and obligations, dedicating such an extensive period solely to this would impede progress on other crucial projects and responsibilities. Given the limitations of resources and time and the infrequent use of experimental repetition in this type of studies, we suggest performing a simulation-based analysis. This approach involves generating synthetic data that mimics the expected characteristics of the original experiment and subsequently subjecting it to the same analysis routine. The main goal of this simulation will be to evaluate the potential spuriousness and randomness of the results that might arise due to the experimental conditions. We will introduce this simulation-based analysis in the next revised version of the manuscript.

Considering the hypothesis is driven by the host switching observed in the field, this phenomenon is discussed very little. I do not believe Cx. quinquefasciatus host switching has been observed in Argentina, only in the northern hemisphere, so it is possible that the species could have an entirely different ecology in Argentina. It would have been helpful to conduct a blood meal analysis prior to this experiment to determine whether using an Argentinian population was appropriate to assess this question. If the Argentinian populations don't experience host switching, then an Argentinian colony would not be the appropriate colony to use to assess this question. Given that this experiment has already been conducted with this population, this possibility should at least be acknowledged in the discussion. Or if a study showing host switching in Argentina has been conducted, it would be helpful to highlight this in the introduction and discussion.

We are aware that few studies regarding host shifting in South America are available, some such those conducted by Stein et al. (2013) and Beranek (2018) reported a moderate host switch for Culex quinquefasciatus in Argentina. We have already performed a study about seasonal host feeding patterns for this species. As you suggested, we could mention it in the discussion to highlight our partial findings. However, even though there are few studies regarding host shifting, our hypothesis is based mainly in the seasonality of human cases of WNV and SLEV, a pattern that has been demonstrated for our region, see for example the study of Spinsanti et al. (2008).

The impacts of certain experimental design decisions are not acknowledged in the manuscript and warrant discussion. For example, the larvae were reared under the same conditions to ensure adults of similar sizes and development timing, but this also prevents mechanisms of action that could occur as a result of seasonality experienced by mothers, eggs, and larvae.

We understand the confusion that may have arisen due to a lack of further details in the methodology. If we are not mistaken, you are referring to our oversight regarding the consideration of carry-over effects of larvae rearing that could potentially impact reproductive traits. When investigating the effects of temperature or other environmental factors on reproductive traits, it is possible to acclimate either larvae or adults. This is due to the significant phenotypic plasticity that mosquitoes exhibit throughout their entire ontogenetic cycle. In our study, we followed an approach similar to that of other authors where the adults are exposed to experimental conditions (temperature and photoperiod). For a similar approach you can refer to the studies conducted by Ferguson et al. (2018) for Cx. pipiens, Garcia Garcia & Londoño Benavides (2007) for Cx. quinquefasciatus and Christiansen-Jucht et al. (2014, 2015) for Anopheles gambiae.

Beyond the issue of lack of replication limiting trust in the conclusions in general, there is one conclusion reached at the end of the discussion that would not be supported, even if additional replicates are conducted. The results do not show that physiological changes in mosquitoes trigger the selection of new hosts. Host selection is never measured, so this claim cannot be made. The results don't even suggest that fitness might trigger selection because the results show that physiological changes are in the opposite direction as what would be hypothesized to produce observed host switches. Similarly, the last sentence of the abstract is not supported by the results.

We agree with this observation. However, we did not evaluate the impact of fitness on host selection in this study. Instead, we aimed to investigate the potential influence of seasonality on mosquito fitness as a potential trigger for a shift in host selection. We agree that we have incorrectly used the term “host selection” when we should actually be discussing “host use change”. Our results indicate a seasonal alteration in mosquito fitness in response to temperature and photoperiod changes. Building upon this observation, we will discuss into our hypotheses and theoretical model to explain this seasonal shift in host use.

Grammar and writing

The manuscript will be grammatically revised by a professional translator.

Author Response

Thank you for your thorough critique and thoughtful suggestions for improving our manuscript, "Homeostatic Synaptic Plasticity of Miniature Excitatory Postsynaptic Currents in Mouse Cortical Cultures Requires Neuronal Rab3A.” The reviewers’ detailed comments suggest that showing multiple types of graphs to demonstrate the presence of divergent scaling of mEPSC amplitudes in cultures from Rab3A wild type, and its disruption in cultures from Rab3A knockout mice, had the unintended consequence of obscuring the major results of our study. Furthermore, our proposal that the difference in characteristics of scaling of GluA2 receptor expression compared to that of mEPSC amplitudes, based on the ratio plots, indicated that a mechanism other than postsynaptic receptors likely contributes to the homeostatic increase in mEPSC amplitude was not convincing to the reviewers. Reviewers 2 and 3 point out these results might be explained by differences in the limitations and artifacts of the two very distinct techniques, electrophysiology and fluorescence imaging. In the revision we will acknowledge that a greater variability in the signal, or, more issues with signal over noise, might be present in imaging experiments compared to electrophysiology. This could explain the lack of identical effects on GluA2 receptors compared to mEPSC amplitudes in the matched experiments, but we maintain it is also possible that a greater variability in GluA2 responses is biologically meaningful. Further, an issue with the accuracy of imaging experiments to report the true receptor effects would also call into question the conclusion that receptors always increase after activity blockade. Finally, the graphs illustrating the detailed characteristics of scaling with rank order and ratio plots required pooling multiple samples per cell, which precludes application of standard statistical methods to determine whether effects or differences reach statistical significance. Therefore, we will remove the cumulative distribution functions, rank order plots, and ratio plots, and show only analyses that involve a single sample per cell. This major change will simplify and clarify the main findings, that homeostatic plasticity of both mEPSC amplitude and GluA2 receptor expression in mouse cortical cultures involves the synaptic vesicle protein Rab3A operating in neurons rather than astrocytes. We will focus our comparison between mEPSC amplitudes and receptors in the same cultures to differences between the magnitude of effects on the mean or median, and will make clear that overall, our data can be explained by two possibilities: 1) the presynaptic vesicle protein is acting via regulation of postsynaptic receptors alone, or, it is regulating both postsynaptic receptors and another contributor to mEPSC amplitude, possibly amount of transmitter released by a single vesicle. Either way, it is very surprising that this presynaptic protein is involved in postsynaptic changes, so our results represent a novel contribution to the field of homeostatic plasticity. In sum, the changes we propose should go a long way towards addressing the majority of the reviewers’ major critiques.

A related issue raised by the reviewers was that the model describing potential presynaptic mechanisms of Rab3A in homeostatic plasticity was not supported by direct evidence (Figure 10). We meant the model to introduce the possibility of a presynaptic contribution to mEPSC amplitude and to stimulate future research, but clearly did not communicate its speculative nature, neither in the Figure legend nor in our discussion of potential mechanisms. In the revision, we will restrict the model to the direct findings in this study. Additionally, we will state where appropriate, that while previous findings at the mouse NMJ are consistent with a presynaptic role for Rab3A (Wang et al., 2011), in the current study there is no direct evidence for this idea in cortical cultures other than the quantitative differences in the fold increases in mEPSC amplitudes and GluA2 receptors which were assayed in the same cultures.

We will submit a revised version addressing each of the reviewer’s concerns and suggestions as described above and below; these major modifications will greatly improve the readability of the manuscript and clarify the main results.

Reviewer #1

Koesters and colleagues investigated the role of the presynaptic small GTPase Rab3A in homeostatic scaling of miniature synaptic transmission in primary mouse cortical cultures using electrophysiology and immunohistochemistry. The major finding is that TTX incubation for 48 hours does not induce an increase in the amplitude of excitatory synaptic miniature events in neuronal cultures derived from Rab3A KO and Rab3A Earlybird mutant mice. NASPM application had comparable effects on mEPSC amplitude in control and after TTX, implying that Ca2+-permeable glutamate receptors are unlikely modulated during synaptic scaling. Immunohistochemical analysis revealed an increase in GluA2 puncta size and intensity in wild type, but not Rab3A KO cultures. Finally, they provide evidence that loss of Rab3A in neurons, but not astrocytes, blocks homeostatic scaling. Based on these data, the authors propose a model in which presynaptic Rab3A is required for homeostatic scaling of synaptic transmission through GluA2-dependent and independent mechanisms.

While the title of the manuscript is mostly supported by data of solid quality, many conclusions, as well as the final model, cannot be derived from the results presented. Importantly, the results do not indicate that Rab3A modulates quantal size on both sides of the synapse. Moreover, several analysis approaches seem inappropriate.

The following points should be addressed:

1) The model shown in Figure 10 is not supported by the data. The authors neither provide evidence for two different functional states of Rab3A being involved in mEPSC amplitude modulation, nor for a change in glutamate content of vesicles. Furthermore, the data do not fully support the conclusion of a presynaptic role for Rab3A in homeostatic scaling.

We will revise the model, removing presynaptic mechanisms for Rab3A and restricting it to the direct findings in this study.

2) The analysis of mEPSC data using quantile sampling followed by ratio calculation is not meaningful under the tested experimental conditions because of the following reasons:

(i) The analysis implicitly assumes that all events have been detected. The prominent mEPSC frequency increase after TTX suggests that this is not the case, i.e., many (small) mEPSCs are likely missed under control conditions.

We explicitly addressed the potential contribution of missed mEPSCs that are below threshold in (Hanes et al., 2020). We found that even simulating a threshold of 7 pA, applied to data artificially modified by uniformly multiplying the control data set, did not generate a ratio plot with the increasing ratio over 75% of the data that we observe in the experimental data. Overall, the findings from simulating a threshold and a uniform multiplicative factor illustrate that the threshold issue does not cause major changes to the data. Furthermore, in cultures from Rab3A+/+ mice from the Rab3AEbd/+ colony, the mEPSC amplitudes were significantly smaller than those recorded in cultures from Rab3A+/+ mice from the Rab3A+/- colony (lines 327-329, 11 pa vs 13 pA), indicating that if there were smaller mEPSCs occurring in the Rab3A+/+ data set, we would have detected them. Although for these reasons we feel it is unlikely our ratio plot analysis is invalid, to clarify the result that homeostatic plasticity of mEPSC amplitude requires functioning Rab3A, we will remove the ratio plots.

(ii) The analysis is used to conclude how events of a certain size are altered by TTX treatment. However, this analysis compares the smallest mEPSCs of the TTX condition with the smallest control mEPSCs, but this is not a pre-post experimental design. Variation between cells and between coverslips will markedly affect the results and lead to misleading interpretations.

The rank order plot is a well-established plot to examine the mathematical transformation caused by homeostatic plasticity, first used in (Turrigiano et al., 1998). We included it here to facilitate comparison of our findings with previous results. We introduced the ratio plot in (Hanes et al., 2020), finding it shows more clearly differences occurring in the range of small mEPSC values. The reviewer is correct in that we are assuming the smallest mEPSCs before treatment should be matched with the smallest mEPSCs after treatment. It is almost impossible to do a pre-post experimental design for mEPSCs. Even when applying a treatment, for example acute perfusion with a receptor antagonist, to a single cell and recording mEPSCs before and after the treatment, it is not a true pre-post design at the level of mEPSC amplitudes, which come from many different inputs. The power of the method is that different characteristic mathematical transformations for different experimental conditions (e.g., genotype or activity protocol) support the idea that those conditions either involve different mechanisms or have altered the mechanism. Such differences might be missed by only comparing means or medians. However, we found no evidence that loss of Rab3A or expression of the Rab3A Earlybird mutant altered the mathematical transformation due to homeostatic plasticity, other than to reduce its magnitude across all amplitudes. Therefore, including these complex analyses is not adding anything to the finding that Rab3A plays a role in homeostatic plasticity of mEPSC amplitudes and they will be removed in the revision.

(iii) The ratio (TTX/control) vs. control plots seem to suffer from a division by small value artifact (see Figure 6F).

The reviewer is referring to findings on the ratio plot for receptor cluster area. Because the large ratios for the smallest control areas occur in the cultures prepared from wild type mice, and to a much lower extent in cultures prepared from Rab3A knockout mice, we think there is a biologically relevant increase in the TTX/CON ratio, since an artifact due to division by small values should be present in both data sets. However, we cannot rule out that the differences in ratio plot behavior between receptors and mEPSC amplitudes result from the different limitations in detection of receptor clusters vs. the limits of detection of mEPSCs, so we will remove the ratio plots and focus on comparison of means or medians.

Correspondingly, ratio-analysis differs considerably for different control conditions (Fig. 1Giii, Fig. 2Giii, Fig. 6C, Fig. 9A).

The reviewer is correct to point out that the ratio plot shows differences across control conditions (note, these differences are not obvious with the more standard rank order plot). The magnitude of the 50th percentile ratio differs across control conditions, and behaviors of the largest mEPSCs also differ, with some ratios going down at the highest control amplitudes (1Giii, 6C), and others continuing to increase with increasing control amplitude (2Giii, 9A). They all share the divergent increasing ratio from smallest mEPSC amplitude to around the 20 pA level. We attribute the differences in magnitude to the differences in experimental conditions: 1Giii is Rab3A+/+ from the +/+ colony; 1Giii is Rab3A+/+ from the Ebd/+ colony; 6C is a set of Rab3A+/+ cultures assayed several years after the set in 1Giii; 9A is a different culture condition altogether, with neurons being plated onto an already formed bed of astrocytes. Effects on the largest mEPSCs are likely attributable to the small number and high variability of amplitudes in this range. Since the variability in the very sensitive ratio plot have taken away from the main findings of homeostatic plasticity being disrupted in the absence of functioning Rab3A in neurons, we will remove the rank-order and the ratio plots from the manuscript.

3) As noted by the authors in a previous publication (Hanes et al. 2020), statistical analysis of CDFs suffers from ninflation. In addition, the quantile sampling method chosen violates an important assumption of the K-S test. Indeed, pvalues for these comparisons are typically several orders of magnitude smaller. Given that the statistical N most likely corresponds to the number of cultures (see, e.g., https://doi.org/10.1371/journal.pbio.2005282), CDF comparisons are not informative and should thus not be used to draw conclusions from the data. The plots can be informative, though.

As the reviewer acknowledges, we were very careful in (Hanes et al., 2020) to state that the p values could not be used to determine significance in the KS test of cumulative distributions for pooled data because the KS test assumes a single sample per cell. We also suggested in that study that the p values could be used in a comparative way for looking at data sets with similar (inflated) n values to say something about bigger or smaller differences. We failed to reiterate those caveats here. In reviewing the article “What is N” by (Lazic et al., 2018) (which we very much appreciate being shown by the reviewer), we agree that in the current study where we are attempting to show how the effect of homeostatic plasticity is or is not altered by loss of Rab3A function, it is imperative that we be able to make conclusions about statistical significance. The pooling approach is essential for having some sense of the mEPSC amplitude distributions, but that is not necessary for looking at the effect of Rab3A. Therefore, we will remove all analyses that involve pooling of multiple mEPSC amplitudes per cell.

4) How does recoding noise and the mEPSC amplitude threshold affect "divergent scaling"?

We addressed this in our 2020 paper (Hanes et al., 2020) where we showed that the experimental homeostatic increase in mEPSC amplitude cannot be simulated with uniform, multiplicative synaptic scaling whether we included or excluded distortion caused by a detection threshold.

5) What is the justification for the line fits of the ratio data/how was the fit range chosen?

We are assuming the reviewer is referring to the line fits for the rank-order data. If so, the fit range is the entire range of the data. This issue will be addressed by the removal of the rank-order plots from the manuscript.

6) TTX application induces a significant increase in mEPSC amplitude in Rab3A-/- mice in two out of three data sets (Figs. 1 and 9). Hence, the major conclusion that Rab3A is required for homeostatic scaling is only partially supported by the data.

Based on the p-values for comparison of means with a Kruskal-Wallis test, we would argue that TTX application does not show a significant increase in mEPSC amplitude in Rab3A-/- neurons (Figure 1 p-value = .318; Figure 9 p-value = .125) when comparing to untreated control mEPSC amplitude means. It is only when we use the KS test and the inflated n’s that we get a barely significant results, p = 0.042. Based on the Lazic article (Lazic et al., 2018), we would now conclude that we cannot use the KS p value in that analysis. We have tried to be clear that the effect of TTX application on mEPSC amplitude in Rab3A-/- neurons is not completely abolished, but rather is dramatically reduced, which we acknowledge in the manuscript (line 279). This issue will be addressed by removal of CDFs from the manuscript.

7) Line 289: A comparison of p-values between conditions does not allow any meaningful conclusions.

Although we feel that comparison of magnitude of effects can be stated in a qualitative way for similar sized pooled data sets with larger or smaller p-values, we agree that statistical significance has no meaning. This issue will be addressed by removing the CDF plots from the manuscript.

8) There is a significant increase in baseline mEPSC amplitude in Rab3AEbd/Ebd (15 pA) vs. Rab3Aebd/+ (11 pA) cultures, but not in Rab3A-/- (13.6 pA) vs. Rab3A+/- (13.9 pA). Although the nature of scaling was different between Rab3AEbd/Ebd vs. Rab3AEbd/+, and Rab3AEbd/Ebd with vs. without TTX, the question arises whether the increase in mEPSC amplitude in Rab3AEbd/Ebd is Rab3A dependent. Could a Rab3A independent mechanism occlude scaling?

We have acknowledged in the manuscript that one explanation for a failure to exhibit homeostatic plasticity in the cultures from Rab3A Earlybird mutant mice is that the already large basal amplitude occludes any further increase (line 366). In the revision we will make sure the occlusion possibility is highlighted, but we will also discuss other proteins that have been implicated in homeostatic plasticity that have caused an increase in mEPSC amplitude and/or AMPA receptors at baseline, for example, Arc/Arg3.1 KO (Shepherd et al., 2006; Beique et al., 2011); Homer KO (Hu et al., 2010) and inhibition of mir-186-5p (Silva et al., 2019).

9) Figure 4: NASPM appears to have a stronger effect on mEPSC frequency in the TTX condition vs. control (-40% vs. 15%). A larger sample size might be necessary to draw definitive conclusions on the contribution of Ca2+-permeable AMPARs.

We will acknowledge that Ca2+-permeable AMPARs could be contributing to the frequency increase following activity blockade and will also include analyses of frequency throughout the manuscript.

10) The authors discuss previous papers showing changes in VGLUT1 intensity. Was VGLUT intensity altered in the stainings presented in the manuscript?

We will perform analyses VGLUT1 intensity and include them in the manuscript.

11) The change in GluA2 area or fluorescence intensity upon TTX treatment in controls is modest. How does the GluA2 integral change?

The changes in GluA2 integrals look exactly like the changes in cluster size and were not included to simplify the results. But with the removal of the CDFs, rank order, and ratio plots, we can easily include integral measurements. What we did not observe was an additive effect with intensity and size such that the effects on integral were of greater magnitude or statistical significance than either alone. We will include the integral plots in the revised manuscript.

12) The quantitative comparison between physiology and microscopy data is problematic. The authors report a mismatch in ratio values between the smallest mEPSC amplitudes and smallest GluA2 receptor cluster sizes (l. 464; Figure 8). Is this comparison affected by the fluorescence intensity threshold?

What was the rationale for a threshold of 400 a.u. or 450 a.u.?

We have acquired AOIs of receptor clusters at multiple threshold levels, and can examine whether the results are altered when using a low, medium or high threshold level.

How does this threshold compare to the mEPSC threshold of 3 pA?

The issue with values being below threshold in untreated cultures has been the concern in interpreting effects on mEPSC amplitudes, specifically, whether this mismatch contributes to divergent scaling. A problem of values being below a toohighly set threshold in the control and becoming detectable after the homeostatic plasticity produces a lower ratio than expected, because now there are values in the treated condition that were not present in the control condition. Instead, for GluA2 receptor cluster size, we observed higher TTX/CON ratios at the low end of the data set. So, based on this, the thresholds chosen for imaging are not having the same effect, if that is what is being asked. This issue will be addressed by removing ratio plots.

The conclusion that an increase in AMPAR levels is not fully responsible for the observed mEPSC increase is mainly based on the rank-order analysis of GluA2 intensity, yielding a slope of ~0.9. There are several points to consider here: (i) GluA2 fluorescence intensity did increase on average, as did GluA2 cluster size. (ii) The increase in GluA2 cluster size is very similar to the increase in mEPSC amplitude (each approx. 18-20%). (iii) Are there any reports that fluorescence intensity values are linearly reporting mEPSC amplitudes (in this system)?

We agree that our data show GluA2 receptors increase as based on cluster size, and did not mean to imply otherwise. Our conclusion that there is another contributor to mEPSC amplitude other than receptors is based on two main findings, 1) that the ratio plots for mEPSC amplitudes and receptor cluster size have distinctively different behaviors, and 2) that there are differences in either magnitude or direction of the TTX effect across 6 matched cultures, 3 from WT animals and 3 from TTX animals (see more explanation of this point below, in response to Reviewer 3). To our knowledge, no one has reported homeostatic plasticity effects on a culture by culture basis, and no one has compared imaging results and physiological results for the same cultures. We will remove the ratio plots and the conclusions based on the differences in behavior for mEPSC amplitudes and receptor cluster size. We will acknowledge in the revision that the differences in magnitude and direction across the 6 matched cultures could be due to the differences in limitations and artifacts of imaging fluorescent antibody staining vs. the limitations and artifacts of detecting mEPSCs electrophysiologically. However, we will continue to state that our results could also be due to the possibility that mEPSC amplitude is not changing in lockstep with receptor levels in every situation. To support this proposal, we will discuss those articles that include both measurements, and point out where mEPSC amplitude measurements and receptor levels match and where they do not.

Antibody labelling efficiency, and false negatives of mEPSC recordings may influence the results. The latter was already noted by the authors.

We will add the caveat that antibody labeling efficiency can vary between coverslips. Although we prepared single solutions that were applied to all coverslips in an experiment, this was not possible for the primary antibody to GluA2, which was added to live cultures in individual wells.(iv) It is not entirely clear if their imaging experiments will sample from all synapses. We will add to Materials and Methods that we sample from all the synapses that could be detected by the researcher on the primary dendrite of the pyramidal cell.

Other AMPAR subtypes than GluA2 could contribute, as could kainate or NMDA receptors.

This is true, other AMPARs (GluA3 and/or GluA4) could be contributing, but we only looked at the receptors well established to be contributing to homeostatic plasticity (GluA1 and GluA2). We will acknowledge the possible contribution of other AMPARs in the revised manuscript.

Furthermore, the statement "complete lack of correspondence of TTX/CON ratios" is not supported by the data presented (l. 515ff). First, under the assumption that no scaling occurs in Rab3A-/- , the TTX/CON ratios show a 20-30% change, which indicates the variation of this readout. Second, the two examples shown in Figure 8 for Rab3A+/+ are actually quite similar (culture #1 and #2), particularly when ignoring the leftmost section of the data, which is heavily affected by the raw values approaching zero.

We will remove the ratio plots from the manuscript and the arguments about differences between GluA2 receptors and mEPSC amplitudes that were based on them. However, we maintain that we have demonstrated a lack of consistent effect for GluA2 receptors and mEPSCs in the matched culture experiments. Yes, the readout of homeostatic plasticity in ratio plots for mEPSCs in the Rab3AKO reach over 1.1 in Figure 1, and as high a 1.2 in the cultures where Rab3AKO neurons were plated on Rab3AWT glia (Figure 9). Our point is that if we had measured GluA2 receptor responses to TTX in those same experiments, the ratios should have been above 1. However, in the experiments in which we measured both mEPSCs and GluA2 receptors, the ratios do not match. In culture #1, the ratio for mEPSCs was at 1 for more than 50% of the data, but for GluA2 receptors, was below 1 for more than 50% of the data. In culture #3, the ratio for mEPSCs was below 1 for more than 50% of the data, but for GluA2 receptors was close to 1.2 for 50% of the data. Only for culture #2 do the ratios appear to match. In the revised manuscript, the evidence that GluA2 receptors and mEPSCs are not changing in parallel will be based on the behavior of means or medians in untreated vs TTXtreated cultures, rather than ratio plots. It could be argued that we need a greater number of matched experiments to make conclusions, but the whole point of a matched experiment is that it should always show the same result—we are no longer dealing with the variability in the homeostatic plasticity itself. We will add a statement that the only three explanations left for the failure of mEPSC amplitudes and GluA2 receptors to change in parallel are 1) a true mismatch, 2) a sampling issue, or 3) technical artifacts that occur in one culture and not another.

13) Figure 7A: TTX CDF was shifted to smaller mEPSC amplitude values in Rab3A-/- cultures. How can this be explained?

Figure 7A depicts the pooled data that are shown separately for 3 cultures in Figure 8. We observed mEPSC amplitudes being smaller after TTX treatment in some range of the data for all three Rab3AKO cultures, suggesting that this may be a biological result rather than random variation around no change (which would be a ratio of 1). However, this effect is not significant at the level of means, nor in the KS test (which has the issue of inflated n in any case), so we did not highlight this point. This issue will be addressed by the removal of the CDF plots from the manuscript.

Reviewer #2

Technical concerns:

1) The culture condition is questionable. The authors saw no NMDAR current present during spontaneous recordings, which is worrisome since NMDARs should be active in cultures with normal network activity (Watt et al., 2000; Sutton et al., 2006).

The (Watt et al., 2000) study recorded mEPSCs in 0 Mg2+ (Figure 1). The (Sutton et al., 2006) study also shows an average mEPSC waveform (Figure 1D) that was recorded from in 0 Mg2+. Our extracellular recording solution contains Mg2+ (1.3 mM) so we likely are not observing NMDA-mediated currents because they are blocked with Mg2+ when strong depolarizations are prevented with TTX in the recording solution. We will add the idea that the NMDA currents are blocked by Mg2+ to Material and Methods.

It is important to ensure there is enough spiking activity before doing any activity manipulation.

We agree that it would be best if network spiking activity were monitored alongside mEPSC recordings, for example by culturing on multi-electrode arrays. Data from these measurements might explain culture to culture variability in homeostatic responses. To our knowledge, most other studies investigating homeostatic plasticity do not monitor network spiking activity in the same cultures that assay mEPSC amplitudes. This is something that the field should move towards. We will add the caveat that activity was not directly measured to the manuscript.

Similarly, it is also unknown whether spiking activity is normal in Rab3A KO/Ebd neurons.

Since we did not measure spiking activity, we cannot address whether the disruption in homeostatic plasticity in cultures prepared from Rab3A KO and Rab3AEbd/Ebd mutant mice is due to an alteration in network activity. If activity were already low in cultures prepared from these genetically altered mice, we would expect mEPSC amplitudes to be increased, compared to those measured in cultures from WT animals. That is not the case in cultures from Rab3A KO mice, so it is unlikely that network activity is reduced. However, mEPSC amplitudes are increased in Rab3AEbd/Ebd cultures, leaving open this possibility. It would have to be a defect unique to neurons in culture, since the Rab3AEbd/Ebd mouse appears normal in every way, suggesting action potential activity is occurring in the brains of these animals in vivo. We will add the possibility that activity is altered in the cultures from Rab3AKO and Rab3AEbd/Ebd to the manuscript.

2) Selection of mEPSC events is not conducted in an unbiased manner. Manually selecting events is insufficient for cumulative distribution analysis, where small biases could skew the entire distribution. Since the authors claim their ratio plot is a better method to detect the uniformity of scaling than the well-established rank-order plot, it is important to use an unbiased population to substantiate this claim.

MiniAnalysis (a standard program used for mEPSC event detection and analysis) selects many false positives with the automated feature (due to the very small sizes of events that are close to the noise level) so manual re-evaluation of the automated process is necessary to eliminate false positives. As soon as there is a manual step, bias is introduced. Interestingly, a manual reevaluation step was applied in a recent study that describes their process as ‘unbiased” (Wu et al., 2020). The alternative is to apply a very large threshold, reducing or eliminating false positives. However, this has the effect of biasing the data towards large events. In sum, we do not believe it is currently possible to perform a completely unbiased detection process. We feel that it is important to include as many small events as possible to reduce the problem of having events in the TTX experimental group that were not matched by events in the control experimental group, for the rank order and ratio plots, so setting the threshold low and manually detecting events accomplishes this. We will add to the Materials and Methods section that the person selecting events did not have information on whether the record was from an untreated or a TTX-treated cell at the time of selection. All of these issues, the potential for skewing the CDFs, and bias potentially interfering in the true rank order and ratio relationships, are addressed by removal of the CDFs, ratio and rank-order plots from the manuscript.

3) Immunohistochemistry data analysis is problematic. The authors only labeled dendrites without doing cell-fills to look at morphology, so it is questionable how they differentiate branches from pyramidal neurons and interneurons. Since glutamatergic synapses on these two types of neuron scale in the opposite directions, it is crucial to show that only pyramidal neurons are included for analysis.

MAP2, in addition to labeling dendrites, also labels the cell body, and we used the cell structure revealed by MAP2 staining to select pyramidal-shaped neurons. The selection of the primary dendrite of a pyramidal neuron was stated in lines 239-240 in Materials and Methods and lines 1094 in the figure legend, but we had not explicitly stated how we knew it was a pyramidal neuron. We will include a low power picture of each of the selected pyramidal neurons in the revision.

Conceptual concerns:

The only novel finding here is the implicated role for Rab3A in synaptic scaling, but insights into mechanisms behind this observation are lacking. The author claims that Rab3A likely regulates scaling from the presynaptic side, yet there is no direct evidence from data presented. In its current form, this study's contribution to the field is very limited.

We acknowledge that a presynaptic mechanism is involved in the regulation of homeostatic plasticity by Rab3A is not supported by direct evidence in cortical cultures in this study. But we disagree that the study’s contribution is very limited.

The revised manuscript will emphasize that there are only two possible mechanisms by which Rab3A is acting in homeostatic plasticity. Either this presynaptic vesicle protein is regulating postsynaptic receptors (an extremely surprising result for which we do have direct evidence), or, it is regulating quantal size from both sides of the synapse (supported by direct evidence from our previous study at the mouse neuromuscular junction in vivo, where receptors are not being upregulated during homeostatic plasticity, and, by indirect evidence in the current study, that receptors and mEPSCs are not being identically regulated in the same cultures). Furthermore, the first idea that follows from the effect of Rab3A on receptors is that it would be regulating release of factors from astrocytes, since this is a mechanism that has been shown to be involved in homeostatic plasticity, and we clearly disprove this hypothesis.

1) Their major argument for this is that homeostatic effects on mEPSC amplitudes and GluA2 cluster sizes do not match. This is inconsistent with reports from multiple labs showing that upscaling of mEPSC amplitude and GluA2 accumulation occur side by side during scaling (Ibata et al., 2008; Pozo et al., 2012; Tan et al., 2015; Silva et al., 2019).

We agree with the reviewer that many studies show an increase in receptors and mEPSC amplitudes after activity blockade. This is why we were very surprised in our initial experiments to find that there was not a consistent robust increase in receptors in our cultures. At that point we were only imaging, and we assumed that it was homeostatic plasticity that was not always robust. We decided it was essential to measure mEPSC amplitudes and image receptors in the same cultures. We expected to observe larger and smaller effects on mEPSC amplitudes from culture to culture that were paralleled by larger and smaller effects on receptors, but this is not what happened. We have gone back to the literature to look more closely at whether variability across cultures has ever been shown for mEPSC amplitudes, receptors, or both. In a survey of 14 studies, none report results culture by culture. To our knowledge, we are the first to report this variability in the receptor response, and the lack of correlation between mEPSC amplitudes and receptor responses, in the same cultures. That said, for the 4 examples provided by the reviewer, only 1 reports evidence relevant to our study that receptors and mEPSC amplitudes ‘occur side by side,’ which is the (Ibata et al., 2008) study. Here, 24 hr of TTX treatment of rat cortical cultures causes synaptically localized GluA2 receptors in confocal imaging, and mEPSC amplitudes, to both increase to around 130%. The (Pozo et al., 2012) study is not a study of activity blockade but of the effects of overexpressing beta-integrins in rat hippocampal cultures, and this causes both GluA2 receptors and mEPSC amplitudes to increase, but the GluA2 level is not restricted to synaptic sites, and, is expressed as the surface fraction (surface receptor/total receptor—total receptor being surface intensity plus internalized intensity) which increases from 0.5 to 0.55, or to 110%, while mEPSC amplitude increases to ~180%. The (Tan et al., 2015) study only provides Western blot data to show an increase of receptors to 125% in mouse cortical cultures in response to 48 hr TTX, with mEPSC amplitudes increased to ~140%, but the Western blot technique measures synaptic and nonsynaptic receptors on excitatory and inhibitory neurons, as well as receptors on astrocytes. Finally, in (Silva et al., 2019), the culture conditions for the imaging data and the mEPSC amplitude data are markedly different, with ‘low-density’ Banker cultures being used for the former, and ‘high-density’ cultures used for the latter, and the protocol to induce activity blockade is different from ours (noncompetitive AMPA and NMDA blockers); synaptic GluA2 receptors are increased to ~280% and mEPSC amplitudes to ~170%. In the revision we will carefully summarize the previous evidence for receptors and mEPSC amplitude responses to activity blockade. Since it is known that different protocols trigger different molecular mechanisms, for example, TTX + APV triggers a homeostatic plasticity that can be completely reversed by acute application of blockers of Ca-permeable receptors, whereas TTX alone triggers a plasticity that is insensitive to these blockers (Sutton et al., 2006), Figure 4E; (Soden and Chen, 2010); Figure 4A), we will keep our discussion restricted to studies using TTX alone for at least 24 hr. We will acknowledge that our finding that GluA2 receptors and mEPSC amplitudes are not varying in lockstep from culture to culture suggests there is another contributor to mEPSC amplitude, but that we cannot rule out it is due to a greater variability in signal, or more issues with signal over noise, in imaging experiments compared to electrophysiology experiments.

Studies surveyed about reporting results by culture:

(Ju et al., 2004; Stellwagen et al., 2005; Shepherd et al., 2006; Sutton et al., 2006; Cingolani and Goda, 2008; Hou et al., 2008; Ibata et al., 2008; Chang et al., 2010; Hu et al., 2010; Jakawich et al., 2010; Beique et al., 2011; Tatavarty et al., 2013; Diering et al., 2014; Sanderson et al., 2018)

Further, because the acquisition and quantification methods for mEPSC recordings and immunohistochemistry imaging are entirely different (each with its own limitations in signal detection), it is not convincing that the lack of proportional changes must signify a presynaptic component.

We agree with the reviewer that there is no way to compare absolute levels from one type of experimental technique to another, but whatever differences in technical issues there are for the two techniques, they should cause systemic errors and should not contribute to the differences between experiments. Most of the issues with imaging come down to variability in the intensity of fluorescence from experiment to experiment, since the antibody solutions are made anew each time, as is the fixation solution. In addition, the confocal microscope function can vary over time and give brighter or dimmer images. But those kinds of artifacts are addressed by using the same solutions on control and TTX-treated coverslips, and imaging control and TTX-treated coverslips in the same single 2-3 hour imaging session, so that whatever issues there are, they cannot contribute to the TTX effect itself. Therefore when we compare the TTX effect (TTX measurements compared to untreated measurements) from culture to culture and find that in one WT culture there was no increase in receptors but there was in mEPSC amplitude, it is difficult to explain how a limitation specific to the antibody imaging technique could produce such a result. Similarly, when we get the opposite result, that in one KO culture, receptors increased but mEPSC amplitudes did not, it is unclear how limitations in signal detection would produce such a result in one culture but not another. The one exception to this is that the primary GluA2 antibody has to be added individually to each coverslip before returning the dishes to the incubator in order to avoid the disruption to live cells that a complete removal of media would have had. The only remaining ‘artifact’ that could explain the results would be a greater variability in the imaging experiments due to limitations in the signal or the signal to noise ratio. In the revision we will report additional characteristics of imaging experiments, such as average intensity for each coverslip, and for each experiment, to address whether variability in fluorescence levels could explain the variability in TTX effects we observe. We will include the possibility that the mismatches in GluA2 receptors and mEPSCs could be caused by greater variability in the imaging experiments.

2) The authors also speculate in the discussion that presynaptic Rab3A could be interacting with retrograde BDNF signaling to regulate postsynaptic AMPARs. Without data showing Rab3A-dependent presynaptic changes after TTX treatment, this argument is not compelling. In this retrograde pathway, BDNF is synthesized in and released from dendrites (Jakawich et al., 2010; Thapliyal et al., 2022), and it is entirely possible for postsynaptic Rab3A to interfere with this process cell-autonomously.

In the revision, the model will focus on the direct findings of the manuscript and tone down the speculation about BDNF signaling, but in the Discussion we will add the possibility that a Rab3A-BDNF interaction could occur either presynaptically or postsynaptically. Interestingly, these articles suggest the postsynaptic BDNF is affecting presynaptic function, namely mEPSC frequency. It is conceivable it could presynaptically affect the vesicle’s release of transmitter.

3) The authors propose that a change in AMPAR subunit composition from GluA2-containing ones to GluA1 homomers may account for the distinct changes in mEPSC amplitudes and GluA2 clusters. However, their data from the Naspm wash-in experiments clearly show that GluA1 homomer contributions have not changed before and after TTX treatment.

Our apologies to the reviewer that we were not clear on this point. In lines 396 to 400 we were describing the significant effects that NASPM had on mEPSC frequency on both untreated and TTX-treated cells, despite having only modest, and not quite significant effects on mEPSC amplitude. We conclude from these results that there are synaptic sites that have only GluA1 homomers, and the mEPSCs from these sites are blocked 100% by NASPM. There may be an increase in such GluA1-only synapses after activity blockade, but nevertheless, these events do not contribute to the amplitude increase. So we did not mean to suggest that there is a shift from Glua2 containing to GluA1 containing receptors that leads to the amplitude increase and fully agree with the reviewer that the GluA1 homomer contributions to amplitude have not changed before and after TTX. We will clarify the difference between the contribution of GluA1 homomers to amplitude and frequency in the revised manuscript.

Reviewer #3

Summary: The authors clearly demonstrate the Rab3A plays a role in HSP at excitatory synapses, with substantially less plasticity occurring in the Rab3A KO neurons. There is also no apparent HSP in the Earlybird Rab3A mutation, although baseline synaptic strength seems already elevated. In this context, it is unclear if the plasticity is absent or just occluded by a ceiling effect due the synapses already being strengthened. The authors do appropriately discuss both options. There are also differences in genetic background between the Rab3A KO and Earlybird mutants that could also impact the results, which are also noted. The authors have solid data showing that Rab3A is unlikely to be active in astrocytes, Finally, they attempt to study the linkage between synaptic strength during HSP and AMPA receptor trafficking, and conclude that trafficking is largely not responsible for the changes in synaptic strength.

Strengths: This work adds another player into the mechanisms underlying an important form of synaptic plasticity. The plasticity is only reduced, suggesting Rab3A is only partially required and perhaps multiple mechanisms contribute. The authors speculate about some possible novel mechanisms.

Weaknesses: However, the rather strong conclusions on the dissociation of AMPAR trafficking and synaptic response are made from somewhat weaker data. The key issue is the GluA2 immunostaining in comparison with the mESPC recordings. Their imaging method involves only assessing puncta clearly associated with a MAP2 labeled dendrite. This is a small subset of synapses, judging from the sample micrographs (Fig 5). To my knowledge, this is a new and unvalidated approach that could represent a particular subset of synapses not representative of the synapses contributing to the mEPSC change. (they are also sampling different neurons for the two measurements; an additional unknown detail is how far from the cell body were the analyzed dendrites for immunostaining. While the authors acknowledge that a sampling issue could explain the data, they still use this data to draw strong conclusions about the lack of AMPAR trafficking contribution to the mEPSC amplitude change. This apparent difference may be a methodological issue rather than a biological one, and at this point it is impossible to differentiate these. It will unfortunately be difficult to validate their approach. Perhaps if they were to drive NMDA-dependent LTD or chemLTP, and show alignment of the imaging and ephys, that would help. More helpful would be recordings and imaging from the same neurons but this is challenging. Sampling from identified synapses would of course be ideal, perhaps from 2P uncaging combined with SEP-labeled AMPARs, but this is more challenging still. But without data to validate the method, it seems unwarranted to make such strong conclusions such as that AMPAR trafficking does not underlie the increase in mEPSC amplitude, given the previous data supporting such a model.

We chose the primary dendrite to ensure we were not assaying dendrites from inhibitory neurons or on axons, but we will add in the revision that it is a limitation of our methods that we are not sampling all the synapses for each neuron. The majority of previous studies that establish that receptors are increased side by side with mEPSCs did not measure receptors and mEPSCs in the same cells, nor even in the same cultures. There is a recent study which employs dual recordings, transfection of GluA2 and VGlut1 constructs, and infusion of dyes to highlight cell morphology (Letellier et al., 2019), so in principle an experiment could be done in which synaptic GluA2 sites are imaged in a cell in which the mEPSCs are also measured. It would be difficult to make these measurements in the same cells before and after TTX treatment, since there is a high likelihood of damaging the cell upon electrode withdrawal and with the imaging process itself. In theory, only a few such experiments would be necessary to establish whether receptors and mEPSC amplitudes are varying in lockstep, and we will consider this for a future study. As stated in response to conceptual concern #1 in Reviewer 2’s comments, we will review the literature on previous studies’ demonstrations of increases in receptors and mEPSC amplitudes following activity blockade in more detail, including how the synaptic sites to be imaged were chosen, to address whether our selection of sites touching the primary dendrite is unvalidated.

A sample from 3 articles:

(Ibata et al., 2008), only information is that ‘distal dendrites’ were examined. The authors do not use a dendritic label. (Jakawich et al., 2010), ‘neurons with pyramidal-like morphology were selected for imaging,’ and ‘principal dendrite of each neuron was linearized’—but how these were identified is not clear, since MAP2 or other cellular labels are not described.

(Silva et al., 2019), ‘dendrites with similar thickness and appearance were randomly selected using MAP2 staining,’ which suggests synaptic sites with GluA2 and VGLUT1 were selected on the basis of being close to or touching the MAP2 positive dendrite, although this is not stated explicitly.

We can perform length measurements on the dendrites imaged and report this information in the revision, but the primary dendrite is the closest dendrite to the cell body.

We have addressed the potential contribution of technical artifacts arising from the two distinct methods of measurement, imaging and electrophysiology, in our response to conceptual concern #1 of Reviewer 2.

Other questions arise from the NASPM experiments, used to justify looking at GluA2 (and not GluA1) in the immunostaining. First, there is a frequency effect that is quite unclear in origin. One would expect NASPM to merely block some fraction of the post-synaptic current, and not affect pre-synaptic release or block whole synapses. It is also unclear why the authors argue this proves that the NASPM was at an effective concentration (lines 399-400).

We observed a clear effect of NASPM reducing mEPSC frequency. We will state more clearly that we infer from the loss of mEPSCs after NASPM that such mEPSCs were from synaptic sites that had only GluA1 homomers, and acknowledge that this is an interpretation. We will also clarify that if our inference is correct, it would indicate that the dose of NASPM we used was 100% effective at blocking GluA1 homomers. The alternative explanation would be a presynaptic effect of NASPM, which has never been reported, to our knowledge.

Further, the amplitude data show a strong trend towards smaller amplitude. The p value for both control and TTX neurons was 0.08 - it is very difficult to argue that there is no effect. And the decrease is larger in the TTX neurons. Considering the strong claims for a pre-synaptic and the use of this data to justify only looking at GluA2 by immunostaining, these data do not offer much support of the conclusions. Between the sampling issues and perhaps looking at the wrong GluA subunit, it seems premature to argue that trafficking is not a contributor to the mEPSC amplitude change, especially given the substantial support for that hypothesis. Further, even if trafficking is not the major contributor, there could be shifts in conductance (perhaps due to regulation of auxiliary subunits) that does not necessitate a pre-synaptic locus. While the authors are free to hypothesize such a mechanism, it would be prudent to acknowledge other options and explanations.

We did not mean to suggest that there is no effect of NASPM on mEPSC amplitude. We will clarify that our data indicate that there is no effect of NASPM on the TTX effect on mEPSC amplitude. We agree with the reviewer that the effect of NASPM on frequency is of larger magnitude after TTX treatment, although the p value is larger than that for untreated cells, likely due to greater variability. We interpret this to mean that TTX treatment increases the proportion of synapses that have only GluA1 homomers. Nevertheless, the increase in GluA1 homomer sites does not appear to contribute to the overall increase in amplitude following TTX treatment, and we wanted to find the mechanism of the amplitude increase. That is why we focused on GluA2 receptors. We will acknowledge the limitation of basing our conclusions on only GluA2 receptors in the revision, as well as the possibility that there is a change in conductance. As stated in our response to Reviewer 2, we do not mean to state that GluA2 receptors do not go up after activity blockade, we find that this is the case. We are proposing an additional mechanism contributing to mEPSC amplitude to explain the different responses for GluA2 receptors vs. mEPSC amplitudes in some of the 6 matched experiments (3 WT and 3 KO).

The frequency data are missing from the paper, with the exception of the NASPM dataset. The mEPSC frequencies should be reported for all experiments, particularly given that Rab3A is generally viewed as a pre-synaptic protein regulating release. Also, in the NASPM experiments, the average frequency is much higher in the TTX treated cultures. Is this statistically above control values?

We will report frequency measurements for all experiments shown. Following TTX treatment, frequency variability increases enormously, with cells having as high as > 10 mEPSCs per second, and other TTX-treated cells with frequencies as low as < 1 mEPSC per second, so the TTX effect on frequency, and whether this effect is present or not in Rab3A KO and Rab3AEbd/Ebd is not completely clear, which is why we did not include those results previously.

Unaddressed issues that would greatly increase the impact of the paper:

1) Is Rab3A acting pre-synaptically, post-synaptically or both? The authors provide good evidence that Rab3A is acting within neurons and not astrocytes. But where it is acting (pre or post) would aid substantially in understanding its role (and particularly the hypothesized and somewhat novel idea that the amount of glutamate released per vesicle is altered in HSP). They could use sparse knock-down of Rab3A, or simply mix cultures from KO and WT mice (with appropriate tags/labels). The general view in the field has been that HSP is regulated post-synaptically via regulation of AMPAR trafficking, and considerable evidence supports this view. The more support for their suggestion of a pre-synaptic site of control, the better.

We agree with the reviewer that this is the most important question to answer next. The approach suggested by the reviewer would be to record from Rab3A KO neurons in a culture where the majority of its inputs are Rab3A positive. If the TTX effect is absent from these cells, it would strongly indicate that postsynaptic Rab3A is required for homeostatic plasticity. There are not currently transgenic mice expressing GFP forms of Rab3A, so we would have to create one, or, transiently transfect Rab3A-GFP into Rab3AKO neurons. Given that under our experimental conditions, we require a very high density of neurons to observe the increase in mEPSC amplitude, it would be difficult to get the ratio of Rab3A-expressing neurons high enough using transfection to be sure that a given postsynaptic cell lacking Rab3A had a normal number of Rab3A-positive inputs and almost no Rab3A-negative inputs. It may be that the opposite experiment is more doable—an isolated Rab3A-positive neuron in a sea of Rab3A-negative neurons, which could be accomplished with a very low transfection efficiency. Another approach would be to use the fast off rate antagonist gamma-DGG, which is more effective against low glutamate concentrations than high glutamate concentrations (see (Liu et al., 1999; Wu et al., 2007). If gamma-DGG were less effective at reducing mEPSC amplitude in TTX-treated cells, compared to untreated cells, it would support the hypothesis that activity blockade leads to an increase in the amount of transmitter per vesicle fusion event. Further, if the change in gamma-DGG sensitivity after activity blockade were disrupted in cultures from Rab3A KO cells, it would support a presynaptic role for Rab3A in homeostatic plasticity of mEPSC amplitude. We have begun these experiments but are finding the surprising result that within a single recording, small mEPSCs and large mEPSCs appear to be differentially sensitive to gamma-DGG. To confirm that this is a biological characteristic, rather than an issue with the detection threshold, we will be repeating our experiments with a slow off rate antagonist that has same effect regardless of transmitter concentration. The complexity of these results precludes including them in the current manuscript.

2) Rab3A is also found at inhibitory synapses. It would be very informative to know if HSP at inhibitory synapses is similarly affected. This is particularly relevant as at inhibitory synapses, one expects a removal of GABARs and/or a decrease of GABA-packaging in vesicles (ie the opposite of whatever is happening at excitatory synapses). If both processes are regulated by Rab3A, this might suggest a role for this protein more upstream in the signaling; an effect only at excitatory synapses would argue for a more specific role just at these synapses.

The next question, after it is determined where Rab3A is acting, is whether it is required for other forms of homeostatic plasticity. This includes plasticity of GABA mIPSCs on pyramidal neurons, but also mEPSCs on inhibitory neurons, and, the downscaling of mEPSCs (and upscaling of mIPSCs) when activity is increased, by bicuculline for example. We will add a statement about future experiments examining other forms of plasticity to the discussion, and include examples where a molecular mechanism has mediated multiple forms, and those that have been shown to be very specific.

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Author Response

Reviewer #1 (Public Review):

Weaknesses:

1) The authors should better review what we know of fungal Drosophila microbiota species as well as the ecology of rotting fruit. Are the microbiota species described in this article specific to their location/setting? It would have been interesting to know if similar species can be retrieved in other locations using other decaying fruits. The term 'core' in the title suggests that these species are generally found associated with Drosophila but this is not demonstrated. The paper is written in a way that implies the microbiota members they have found are universal. What is the evidence for this? Have the fungal species described in this paper been found in other studies? Even if this is not the case, the paper is interesting, but there should be a discussion of how generalizable the findings are.

The reviewer inquires as to whether the microbial species described in this article are ubiquitously associated with Drosophila or not. Indeed, most of the microbes described in this manuscript are generally recognized as species associated with Drosophila spp. For example, species such as Hanseniaspora uvarum, Pichia kluyveri, and Starmerella bacillaris have been detected in or isolated from Drosophila spp. collected in European countries as well as the United States and Oceania (Chandler et al., 2012; Solomon et al., 2019). As for the bacteria, species belonging to the genera Pantoea, Lactobacillus, Leuconostoc, and Acetobacter have also previously been detected in wild Drosophila spp. (Chandler et al., 2011). These elucidations will be incorporated into our revised manuscript.

Nevertheless, the term “core” in the manuscript title may lead to misunderstanding, as the generality does not ensure the ubiquitous presence of these microbial species in every individual fly. Considering this point, we will replace the term with an expression more appropriate to our context.

2) Can the authors clearly demonstrate that the microbiota species that develop in the banana trap are derived from flies? Are these species found in flies in the wild? Did the authors check that the flies belong to the D. melanogaster species and not to the sister group D. simulans?

Can the authors clearly demonstrate that the microbiota species that develop in the banana trap are derived from flies? Are these species found in flies in the wild?

The reviewer asked whether the microbial species identified in the fermented banana samples were derived from flies. To address this question, additional experiments under more controlled conditions, such as the inoculation of specific species of wild flies onto fresh bananas, would be needed. Nevertheless, the microbes may potentially originate from wild flies, as supported by the literature cited in our response to the Weakness 1).

Alternative sources for microbial provenance also merit consideration. For example, microbial entities may be inherently present in unfermented bananas through the infiltration of peel injuries (lines 1141-1142 of the original manuscript). In addition, they could be introduced by insects other than flies, given that both rove beetles (Staphylinidae) and sap beetles (Nitidulidae) were observed in some of the traps. These possibilities will be incorporated into the 'MATERIALS AND METHODS' and 'DISCUSSION' sections of our revised manuscript.

Did the authors check that the flies belong to the D. melanogaster species and not to the sister group D. simulans?

Our sampling strategy was designed to target not only D. melanogaster but also other domestic Drosophila species, such as D. simulans, that inhabit human residential areas. After adult flies were caught in each trap, we identified the species as shown in Table S1, thereby showing the presence of either or both D. melanogaster and D. simulans. We will provide these descriptions in MATERIALS AND METHODS and DISCUSSION.

3) Did the microarrays highlight a change in immune genes (ex. antibacterial peptide genes)? Whatever the answer, this would be worth mentioning. The authors described their microarray data in terms of fed/starved in relation to the Finke article. They should clarify if they observed significant differences between species (differences between species within bacteria or fungi, and more generally differences between bacteria versus fungi).

Did the microarrays highlight a change in immune genes (ex. antibacterial peptide genes)? Whatever the answer, this would be worth mentioning.

Regarding the antimicrobial peptide genes, statistical comparisons of our RNA-seq data across different conditions were impracticable because most of them showed low expression levels (refer to Author response table 1, which exhibits the RNA-seq data of the yeast-fed larvae; similar expression profiles were observed in the bacteria-fed larvae). While a subset of genes exhibited significantly elevated expression in the non-supportive conditions relative to the supportive ones, this can be due to intra-sample variability rather than due to distinct nutritional environments. Therefore, it would be difficult to discuss a change in immune genes in the paper. Additionally, the previous study that conducted larval microarray analysis (Zinke et al., 2002) did not explicitly focus on immune genes.

Author Response Table 1.

Antimicrobial peptide genes are not up-regulated by any of the microbes Antimicrobial peptides gene expression profiles of whole bodies of first-instar larvae fed on yeasts. TPM values of all samples and comparison results of gene expression levels in the larvae fed on supportive and non-supportive yeasts are shown. Antibacterial peptide genes mentioned in Hanson and Lemaitre, 2020 are listed. NA or na, not available.

They should clarify if they observed significant differences between species (differences between species within bacteria or fungi, and more generally differences between bacteria versus fungi).

We did not observe significant differences between species within bacteria or fungi, or between bacteria and fungi. For example, the gene expression profiles of larvae fed on the various supporting microbes showed striking similarities to each other, as evidenced by the heat map showing the expression of all genes detected in larvae fed either yeast or bacteria (Author response image 1). Similarities were also observed among larvae fed on distinct non-supporting microbes.

Author response image 1.

Gene expression profiles of larvae fed on the various supporting microbes show striking similarities to each other. Heat map showing the gene expression of the first-instar larvae that fed on yeasts or bacteria. Freshly hatched germ-free larvae were placed on banana agar inoculated with each microbe and collected after 15 h feeding to examine gene expression of the whole body. Note that data presented in Figures 3A and 4C in the original manuscript, which are obtained independently, are combined to generate this heat map. The labels under the heat map indicate the microbial species fed to the larvae, with three samples analyzed for each condition. The lactic acid bacteria (“LAB”) include Lactiplantibacillus plantarum and Leuconostoc mesenteroides, while the lactic acid bacterium (“AAB”) represents Acetobacter orientalis. “LAB + AAB” signifies mixtures of the AAB and either one of the LAB species. The asterisk in the label highlights a sample in a “LAB” condition (Leuconostoc mesenteroides), which clustered separately from the other “LAB” samples. Brown abbreviations of scientific names are for the yeast-fed conditions. H. uva, Hanseniaspora uvarum; K. hum, Kazachstania humilis; M. asi, Martiniozyma asiatica; S. cra, Saccharomycopsis crataegensis; P. klu, Pichia kluyveri; S. bac, Starmerella bacillaris; S. cer, S. cerevisiae BY4741 strain.

Only a handful of genes showed different expression patterns between larvae fed on yeast and those fed on bacteria, without any enrichment for specialized gene functions. Thus, it is challenging to discuss the potential differential impacts, if any, of yeast and bacteria on larval growth.

4) The whole paper - and this is one of its merits - points to a role of the Drosophila larval microbiota in processing the fly food. Are these bacterial and fungal species found in the gut of larvae/adults? Are these species capable of establishing a niche in the cardia of adults as shown recently in the Ludington lab (Dodge et al.,)? Previous studies have suggested that microbiota members stimulate the Imd pathway leading to an increase in digestive proteases (Erkosar/Leulier). Are the microbiota species studied here affecting gut signaling pathways beyond providing branched amino acids?

The whole paper - and this is one of its merits - points to a role of the Drosophila larval microbiota in processing the fly food. Are these bacterial and fungal species found in the gut of larvae/adults? Are these species capable of establishing a niche in the cardia of adults as shown recently in the Ludington lab (Dodge et al.,)?

Although we did not investigate the microbiota in the gut of either larvae or adults, we did compare the microbiota within surface-sterilized larvae or adults with those in food samples. We found that adult flies and early-stage food sources, as well as larvae and late-stage food sources, harbor similar microbial species (Figure 1F). Additionally, previous examinations of the gut microbiota in wild adult flies have identified microbial species or taxa congruent with those we isolated from our foods (Chandler et al., 2011; Chandler et al., 2012). We have elaborated on this in our response to Weakness 1).

While we did not investigate whether these species are capable of establishing a niche in the cardia of adults, we will cite the study by Dodge et al., 2023 in our revised manuscript and discuss the possibility that predominant microbes in adult flies may show a propensity for colonization.

Previous studies have suggested that microbiota members stimulate the Imd pathway leading to an increase in digestive proteases (Erkosar/Leulier). Are the microbiota species studied here affecting gut signaling pathways beyond providing branched amino acids?

The reviewer inquires whether the supportive microbes in our study stimulate gut Imd signaling pathways and induce the expression of digestive protease genes, as demonstrated in a previous study (Erkosar et al., 2015). According to our RNA-seq data, it seems unlikely that the supportive microbes stimulate the signaling pathway. Figures contained in Author response image 2 provide the statistical comparisons of expression levels for seven protease genes between the supportive and the non-supportive conditions. These genes did not exhibit a consistent upregulation in the presence of the supportive microbes (H. uva or K. hum in Author response image 2A; Le mes + A. ori in Author response image 2B). Rather, they exhibited a tendency to be upregulated under the non-supportive microbes (St. bac or Pi. klu in Author response image 2A; La. pla in Author response image 2B).

Author response image 2.

Most of the peptidase genes reported by Erkosar et al., 2015 are more highly expressed under the non-supportive conditions than the supportive conditions. Comparison of the expression levels of seven peptidase genes derived from the RNA-seq analysis of yeast-fed (A) or bacteria-fed (B) first-instar larvae. A previous report demonstrated that the expression of these genes is upregulated upon association with a strain of Lactiplantibacillus plantarum, and that the PGRP-LE/Imd/Relish signaling pathway, at least partially, mediates the induction (Erkosar et al., 2015). H. uva, Hanseniaspora uvarum; K. hum, Kazachstania humilis; P. klu, Pichia kluyveri; S. bac, Starmerella bacillaris; La. pla, Lactiplantibacillus plantarum; Le. mes, Leuconostoc mesenteroides; A. ori, Acetobacter orientalis; ns, not significant.

Reviewer #2 (Public Review):

Weaknesses:

The experimental setting that, the authors think, reflects host-microbe interactions in nature is one of the key points. However, it is not explicitly mentioned whether isolated microbes are indeed colonized in wild larvae of Drosophila melanogaster who eat bananas. Another matter is that this work is rather descriptive and a few mechanical insights are presented. The evidence that the nutritional role of BCAAs is incomplete, and molecular level explanation is missing in "interspecies interactions" between lactic acid bacteria (or yeast) and acetic acid bacteria that assure their inhabitation. Apart from these matters, the future directions or significance of this work could be discussed more in the manuscript.

The experimental setting that, the authors think, reflects host-microbe interactions in nature is one of the key points. However, it is not explicitly mentioned whether isolated microbes are indeed colonized in wild larvae of Drosophila melanogaster who eat bananas.

The reviewer asks whether the isolated microbes were colonized in the larval gut. Previous studies on microbial colonization associated with Drosophila have predominantly focused on adults (Pais et al. PLOS Biology, 2018), rather than larval stages. Developing larvae continually consume substrates which are already subjected to microbial fermentation and abundant in live microbes until the end of the feeding larval stage. Therefore, we consider it difficult to discuss microbial colonization in the larval gut. We will add this point in the DISCUSSION of the revised manuscript.

Another matter is that this work is rather descriptive and a few mechanical insights are presented. The evidence that the nutritional role of BCAAs is incomplete, and molecular level explanation is missing in "interspecies interactions" between lactic acid bacteria (or yeast) and acetic acid bacteria that assure their inhabitation.

While recognizing the importance of comprehensive mechanistic analysis, this study includes all experimentally feasible data. Elucidation of more detailed molecular mechanisms lies beyond the scope of this study and will be the subject of future research.

Regarding the nutritional role of BCAAs, the incorporation of BCAAs enabled larvae fed with the non-supportive yeast to grow to the second instar. This observation suggests that consumption of BCAAs upregulates diverse genes involved in cellular growth processes in larvae. We have discussed the hypothetical interaction between lactic acid bacteria (LAB) and acetic acid bacteria (AAB) in the manuscript (lines 402-405): LAB may facilitate lactate provision to AAB, consequently enhancing the biosynthesis of essential nutrients such as amino acids. To test this hypothesis, future experiments will include the supplementation of lactic acid to AAB culture plates and the co-inoculating LAB mutant strains defective in lactate production with AABs, to assess both larval growth and continuous larval association with AABs. With respect to AAB-yeast interactions, metabolites released from yeast cells might benefit AAB growth, and this possibility will be investigated through the supplementation of AAB culture plates with candidate metabolites identified in the cell suspension supernatants of the late-stage yeasts.

Apart from these matters, the future directions or significance of this work could be discussed more in the manuscript.

We appreciate the reviewer's recommendations and will include additional descriptions regarding these aspects in the DISCUSSION section.

Reviewer #3 (Public Review):

Weaknesses:

Despite describing important findings, I believe that a more thorough explanation of the experimental setup and the steps expected to occur in the exposed diet over time, starting with natural "inoculation" could help the reader, in particular the non-specialist, grasp the rationale and main findings of the manuscript. When exactly was the decision to collect early-stage samples made? Was it when embryos were detected in some of the samples? What are the implications of bacterial presence in the no-fly traps? These samples also harbored complex microbial communities, as revealed by sequencing. Were these samples colonized by microbes deposited with air currents? Were they the result of flies that touched the material but did not lay eggs? Could the traps have been visited by other insects? Another interesting observation that could be better discussed is the fact that adult flies showed a microbiome that more closely resembles that of the early-stage diet, whereas larvae have a more late-stage-like microbiome. It is easy to understand why the microbiome of the larvae would resemble that of the late-stage foods, but what about the adult microbiome? Authors should discuss or at least acknowledge the fact that there must be a microbiome shift once adults leave their food source. Lastly, the authors should provide more details about the metabolomics experiments. For instance, how were peaks assigned to leucine/isoleucine (as well as other compounds)? Were both retention times and MS2 spectra always used? Were standard curves produced? Were internal, deuterated controls used?

When exactly was the decision to collect early-stage samples made? Was it when embryos were detected in some of the samples?

We collected traps and early-stage samples 2.5 days after setting up the traps. This time frame was determined by pilot experiments. A shorter collection time resulted in a greater likelihood of obtaining no-fly traps, whereas a longer collection time caused larval overcrowding, as well as adults’ deaths from drowning in the liquid seeping out of fruits. These procedural details will be delineated in the MATERIALS AND METHODS section of the revised manuscript.

What are the implications of bacterial presence in the no-fly traps? These samples also harbored complex microbial communities, as revealed by sequencing. Were these samples colonized by microbes deposited with air currents? Were they the result of flies that touched the material but did not lay eggs? Could the traps have been visited by other insects?

We assume that the origins of the microbes detected in the no-fly trap foods vary depending on the species. For instance, Colletotrichum musae, the fungus that causes banana anthracnose, may have been present in fresh bananas before trap placement. The filamentous fungi could have originated from airborne spores, but they could also have been introduced by insects that feed on these fungi. We will include these possibilities in the DISCUSSION section of the revised manuscript.

Another interesting observation that could be better discussed is the fact that adult flies showed a microbiome that more closely resembles that of the early-stage diet, whereas larvae have a more late-stage-like microbiome. It is easy to understand why the microbiome of the larvae would resemble that of the late-stage foods, but what about the adult microbiome? Authors should discuss or at least acknowledge the fact that there must be a microbiome shift once adults leave their food source.

We are grateful for the reviewer's insightful suggestions regarding shifts in the adult microbiome. We plan to include in the DISCUSSION section of the revised manuscript the possibility that the microbial composition may change substantially during pupal stages and that microbes obtained after eclosion could potentially form the adult gut microbiota.

Lastly, the authors should provide more details about the metabolomics experiments. For instance, how were peaks assigned to leucine/isoleucine (as well as other compounds)? Were both retention times and MS2 spectra always used? Were standard curves produced? Were internal, deuterated controls used?

We appreciate the reviewer's advice. Detailed methods of the metabolomic experiments will be included in our revised manuscript.

Author Response

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

Reviewer #1:

People can perform a wide variety of different tasks, and a long-standing question in cognitive neuroscience is how the properties of different tasks are represented in the brain. The authors develop an interesting task that mixes two different sources of difficulty, and find that the brain appears to represent this mixture on a continuum, in the prefrontal areas involved in resolving task difficulty. While these results are interesting and in several ways compelling, they overlap with previous findings and rely on novel statistical analyses that may require further validation.

Strengths

1) The authors present an interesting and novel task for combining the contributions of stimulus-stimulus and stimulus-response conflict. While this mixture has been measured in the multi-source interference task (MSIT), this task provides a more graded mixture between these two sources of difficulty

2) The authors do a good job triangulating regions that encoding conflict similarity, looking for the conjunction across several different measures of conflict encoding

3) The authors quantify several salient alternative hypothesis and systematically distinguish their core results from these alternatives

4) The question that the authors tackle is of central theoretical importance to cognitive control, and they make an interesting an interesting contribution to this question

We would like to thank the reviewer for the positive evaluation of our manuscript and the constructive comments and suggestions. Your feedback has been invaluable in our efforts to enhance the accessibility of our manuscript and strengthen our findings. In response to your suggestion, we reanalyzed our data using the approach proposed by Chen et al.’s (2017, NeuroImage) and applied stricter multiple comparison correction thresholds in our reporting. This reanalysis largely replicated our previous results, thereby reinforcing the robustness of our findings. We also have examined several alternative models and results supported the integration of the spatial Stroop and Simon conflicts within the cognitive space. In addition, we enriched the theoretical framework of our manuscript by connecting the cognitive space with other important theories such as the “Expected Value of Control” theory. We have incorporated your feedback, revisions and additional analyses into the manuscript. As a result, we firmly believe that these changes have significantly improved the quality of our work. We have provided detailed responses to your comments below.

1) It's not entirely clear what the current task can measure that is not known from the MSIT, such as the additive influence of conflict sources in Fu et al. (2022), Science. More could be done to distinguish the benefits of this task from MSIT.

We agree that the MSIT task incorporates Simon and Eriksen Flanker conflict tasks and can efficiently detect the additivity of conflict effects across orthogonal tasks. Like the MSIT, our task incorporates Simon with spatial Stroop conflicts and can test the same idea. For example, a previous study from our lab (Li et al., 2014) used the combined spatial Stroop-Simon condition with the arrows displayed on diagonal corners and found evidence for the additive hypothesis. However, the MSIT cannot be used to test whether/how different conflicts are parametrically represented in a low-dimensional space, a question that is important to address the debate of domain-general and domain-specific cognitive control.

To this end, our current study adopted the spatial Stroop-Simon task for the unique purpose of parametrically modulating conflict similarity. As far as we know, there is no way to define the similarity between the combined Simon_Flanker conflict condition and the Simon/Flanker conditions in the MSIT. In contrast, with the spatial Stroop-Simon paradigm, we can define the similarity with the cosine of the angle difference across the two conditions in question.

We have added the following texts in the discussion part to emphasize the 51 difference between our paradigm and other studies.

"The use of an experimental paradigm that permits parametric manipulation of conflict similarity provides a way to systematically investigate the organization of cognitive control, as well as its influence on adaptive behaviors. This approach extends traditional paradigms, such as the multi-source interference task (Fu et al., 2022), color Stroop-Simon task (Liu et al., 2010) and similar paradigms that do not afford a quantifiable metric of conflict source similarity."

References:

Li, Q., Nan, W., Wang, K., & Liu, X. (2014). Independent processing of stimulus-stimulus and stimulus-response conflicts. PloS One, 9(2), e89249.

2) The evidence from this previous work for mixtures between different conflict sources make the framing of 'infinite possible types of conflict' feel like a strawman. The authors cite classic work (e.g., Kornblum et al., 1990) that develops a typology for conflict which is far from infinite, and I think few people would argue that every possible source of difficulty will have to be learned separately. Such an issue is addressed in theories like 'Expected Value of Control', where optimization of control policies can address unique combinations of task demands.

The notion that there might be infinite conflicts arises when we consider the quantitative feature of cognitive control. If each combination of the Stroop-Simon combination is regarded as a conflict condition, there would be infinite combinations, and it is our major goal to investigate how these infinite conflict conditions are represented effectively in a space with finite dimensions. We agree that it is unnecessary to dissociate each of these conflict conditions into a unique conflict type, since they may not differ substantially. However, we argue that understanding variant conflicts within a purely categorical framework (e.g., Simon and Flanker conflict in MSIT) is insufficient, especially because it leads to dichotomic conclusions that do not capture how combinations of conflicts are organized in the brain, as our study addresses.

There could be different perspectives on how our cognitive control system flexibly encodes and resolves multiple conflicts. The cognitive space assumption we held provides a principle by which we can represent multiple conflicts in a lower dimensional space efficiently. While the “Expected Value of Control” theory addresses when and how much cognitive control to apply based on control demand, the “cognitive space” view seeks to explain how the conflict, which defines cognitive control demand, is encoded in the brain. Thus, we argue that these two lines of work are different yet complementary. The geometry of cognitive space of conflict can benefit the adjustment of cognitive control for upcoming conflicts. For example, our brain may evaluate the similarity/distance (and thus cost) between the consecutive conflict conditions, and selects the path with best cost-benefit tradeoff to switch from one state to another. This idea is conceptually similar to a recent study by Grahek et al. (2022) demonstrating that more frequently switching states were encoded as closer together than less frequently switching states in a “drift-threshold” space.

Nevertheless, Grahek et al (2022) investigated how cognitive control changes based on the expected value of control theory within the same conflict, whereas our study aims to examine organization of different conflict.

We have added the implications of cognitive space view in the discussion to indicate the potential values of our finding to understand the EVC account and the difference between the two theories.

“Previous researchers have proposed an “expected value of control (EVC)” theory, which posits that the brain can evaluate the cost and benefit associated with executing control for a demanding task, such as the conflict task, and specify the optimal control strength (Shenhav et al., 2013). For instance, Grahek et al. (2022) found that more frequently switching goals when doing a Stroop task were achieved by adjusting smaller control intensity. Our work complements the EVC theory by further investigating the neural representation of different conflict conditions and how these representations can be evaluated to facilitate conflict resolution. We found that different conflict conditions can be efficiently represented in a cognitive space encoded by the right dlPFC, and participants with stronger cognitive space representation have also adjusted their conflict control to a greater extent based on the conflict similarity (Fig 4C). The finding suggests that the cognitive space organization of conflicts guides cognitive control to adjust behavior. Previous studies have shown that participants may adopt different strategies to represent a task, with the model-based strategies benefitting goal-related behaviors more than the model-free strategies (Rmus et al., 2022). Similarly, we propose that cognitive space could serve as a mental model to assist fast learning and efficient organization of cognitive control settings. Specifically, the cognitive space representation may provide a principle for how our brain evaluates the expected cost of switching and the benefit of generalization between states and selects the path with the best cost-benefit tradeoff (Abrahamse et al., 2016; Shenhav et al., 2013). The proximity between two states in cognitive space could reflect both the expected cognitive demand required to transition and the useful mechanisms to adapt from. The closer the two conditions are in cognitive space, the lower the expected switching cost and the higher the generalizability when transitioning between them. With the organization of a cognitive space, a new conflict can be quickly assigned a location in the cognitive space, which will facilitate the development of cognitive control settings for this conflict by interpolating nearby conflicts and/or projecting the location to axes representing different cognitive control processes, thus leading to a stronger CSE when following a more similar conflict condition. On the other hand, without a cognitive space, there would be no measure of similarity between conflicts on different trials, hence limiting the ability of fast learning of cognitive control setting from similar trials.”

Reference:

Grahek, I., Leng, X., Fahey, M. P., Yee, D., & Shenhav, A. Empirical and Computational Evidence for Reconfiguration Costs During Within-Task Adjustments in Cognitive Control. CogSci.

3) Wouldn't a region that represented each conflict source separately still show the same pattern of results? The degree of Stroop vs Simon conflict is perfectly negatively correlated across conditions, so wouldn't a region that just tracks Stoop conflict show these RSA patterns? The authors show that overall congruency is not represented in DLPFC (which is surprising), but they don't break it down by whether this is due to Stroop or Simon congruency (I'm not sure their task allows for this).

To estimate the unique contributions of the spatial Stroop and Simon conflicts, we performed a model-comparison analysis. We constructed a Stroop-Only model and a Simon-Only model, with each conflict type projected onto the Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, P., 1901), that is, their intersection divided by their union. By replacing the cognitive spacebased conflict similarity regressor with the Stroop-Only and Simon-Only regressors, we calculated their BICs. Results showed that the BIC was larger for Stroop-Only (5377122) and Simon-Only (5377096) than for the Cognitive-Space model (5377094). An additional Stroop+Simon model, including both Stroop-Only and Simon-Only regressors, also showed a poorer model fitting (BIC = 5377118) than the Cognitive-Space model. Considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials), we also conducted the model comparison using the incongruent trials only. Results showed that Stroop-Only (1344128), Simon-Only (1344120), and Stroop+Simon (1344157) models all showed higher BIC values than the CognitiveSpace model (1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. Therefore, we believe the cognitive space has incorporated both dimensions. We added these additional analyses and results to the revised manuscript.

“To examine if the right 8C specifically encodes the cognitive space rather than the domain-general or domain-specific organizations, we tested several additional models (see Methods). Model comparison showed a lower BIC in the Cognitive-Space model (BIC = 5377094) than the Domain-General (BIC = 537127) or Domain-Specific (BIC = 537127) models. Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D. We also tested if the observed conflict similarity effect was driven solely by spatial Stroop or Simon conflicts, and found larger BICs for the models only including the Stroop similarity (i.e., the Stroop-Only model, BIC = 5377122) or Simon similarity (i.e., the Simon-Only model, BIC = 5377096). An additional Stroop+Simon model, including both StroopOnly and Simon-Only regressors, also showed a worse model fitting (BIC = 5377118). Moreover, we replicated the results with only incongruent trials, considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. The more detailed model comparison results are listed in Table 2.”

We reason that we did not observe an overall congruency effect in the RSA results is because our definition of congruency here differed from traditional definitions (i.e., contrast between incongruent and congruent conditions). In the congruency regressor of our RSA model, we defined representational similarity as 1 if calculated between two incongruent, or two congruent trials, and 0 if between incongruent and congruent trials. Thus, our definition of the congruency regressor reflects whether multivariate patterns differ between incongruent and congruent trials, rather than whether activity strengths differ. Indeed, we did observe the latter form of congruency effects, with stronger univariate activities in pre-SMA for incongruent versus congruent conditions. We have added this in the Note S6 (“The multivariate representations of conflict type and orientation are different from the congruency effect”):

“Neither did we observe a multivariate congruency effect (i.e., the pattern difference between incongruent and congruent conditions compared to that within each condition) in the right 8C or any other regions. Note the definition of congruency here differed from traditional definitions (i.e., contrast between activity strength of incongruent and congruent conditions), with which we found stronger univariate activities in pre-SMA for incongruent versus congruent conditions.”

We could not determine whether the null effect of the congruency regressor was due to Stroop or Simon congruency alone, because congruency levels of the two types always covary. On all trials of the compound conditions (Conf 2-4), whenever the Stroop dimension was incongruent, the Simon dimension was also incongruent, and vice versa for the congruent condition. Thus, the contribution of spatial Stroop or Simon alone to the congruency effect could not be tested using compound conditions. Although we have pure spatial Stroop or Simon conditions, within-Stroop and withinSimon trial pairs constituted only 8% of cells in the representational similarity matrix. This was insufficient to determine whether the null congruency effect was due to solely Stroop or Simon.

Overall, with the added analysis we found that the data in the right 8C area supports conflict representations that are organized based on both Simon and spatial Stroop conflict. Although the current experimental design does not allow us to identify whether the null effect of the congruency regressor was driven by either conflict or both, we clarified that the congruency regressor did not test the 205 conventional congruency effect and the null finding does not contradict previous 206 research.

Reference:

Jaccard, P. (1901). Étude comparative de la distribution florale dans une portion des Alpes et des Jura. Bull Soc Vaudoise Sci Nat(37), 547-579.

4) The authors use a novel form of RSA that concatenates patterns across conditions, runs and subjects into a giant RSA matrix, which is then used for linear mixed effects analysis. This appears to be necessary because conflict type and visual orientation are perfectly confounded within the subject (although, if I understand, the conflict type x congruence interaction wouldn't have the same concern about visual confounds, which shouldn't depend on congruence). This is an interesting approach but should be better justified, preferably with simulations validating the sensitivity and specificity of this method and comparing it to more standard methods.

The confound exists for both the conflict type and the conflict type × congruence interaction in our design, since both incongruent and congruent conditions include stimuli from the full orientation space. For example, for the spatial Stroop type, the congruent condition could be either an up arrow at the top or a down arrow at the bottom. Similarly, the incongruent condition could be either an up arrow at the bottom or a down arrow at the top. Therefore, both the congruent and incongruent conditions are perfectly confounded with the orientation.

We reanalyzed the data using the well-documented approach by Chen et al. (2017, Neuroimage), as suggested by the reviewer. The new analysis replicated our previously reported results (Fig. 4-5, S4-S7). As Chen et al (2017) has provided abundant simulations to validate this approach, we did not run any further simulations.

5) A chief concern is that the same pattern contributes to many entries in the DV, which has been addressed in previous work using row-wise and column-wise random effects (Chen et al., 2017, Neuroimage). It would also be informative to know whether the results hold up to removing within-run similarity, which can bias similarity measures (Walther et al., 2016, Neuroimage).

Thank you for the comment. In our revised manuscript, we followed your suggestion and adopted the approach proposed by Chen et al. (2017). Specifically, we included both the upper and lower triangle of the representational similarity matrix (excluding the diagonal). Moreover, we also removed all the within-subject similarity (thus also excluding the within-run similarity as suggested by Walther et al. (2016)) to minimize the bias of the potentially strong within-subject similarity. In addition, we added both the row-wise and column-wise random effects to capture the dependence of cells within each column and each row, respectively (Chen et al., 2017).

Results from this approach largely replicated our previous results. The right 8C again showed significant conflict similarity representation, with greater representational strength in incongruent than congruent condition, and positively correlated to behavioral performance. The orientation effect was also identified in the visual (e.g., right V1) and oculomotor (e.g., left FEF) regions.

We have revised the methodology and the results in the revised manuscript:

"Representational similarity analysis (RSA).

For each cortical region, we calculated the Pearson’s correlations between fMRI activity patterns for each run and each subject, yielding a 1400 (20 conditions × 2 runs × 35 participants) × 1400 RSM. The correlations were calculated in a cross297 voxel manner using the fMRI activation maps obtained from GLM3 described in the previous section. We excluded within-subject cells from the RSM (thus also excluding the within-run similarity as suggested by Walther et al., (2016)), and the remaining cells were converted into a vector, which was then z-transformed and submitted to a linear mixed effect model as the dependent variable. The linear mixed effect model also included regressors of conflict similarity and orientation similarity. Importantly, conflict similarity was based on how Simon and spatial Stroop conflict are combined and hence was calculated by first rotating all subject’s stimulus location to the top right and bottom-left quadrants, whereas orientation was calculated using original stimulus locations. As a result, the regressors representing conflict similarity and orientation similarity were de-correlated. Similarity between two conditions was measured as the cosine value of the angular difference. Other regressors included a target similarity regressor (i.e., whether the arrow directions were identical), a response similarity regressor (i.e., whether the correct responses were identical); a spatial Stroop distractor regressor (i.e., vertical distance between two stimulus locations); a Simon distractor regressor (i.e., horizontal distance between two stimulus locations). Additionally, we also included a regressor denoting the similarity of Group (i.e., whether two conditions are within the same subject group, according to the stimulus-response mapping). We also added two regressors including ROI316 mean fMRI activations for each condition of the pair to remove the possible uni-voxel influence on the RSM. A last term was the intercept. To control the artefact due to dependence of the correlation pairs sharing the same subject, we included crossed random effects (i.e., row-wise and column-wise random effects) for the intercept, conflict similarity, orientation and the group factors (G. Chen et al., 2017)."

Reference:

Walther, A., Nili, H., Ejaz, N., Alink, A., Kriegeskorte, N., & Diedrichsen, J. (2016). Reliability of dissimilarity measures for multi-voxel pattern analysis. Neuroimage, 137, 188-200. doi:10.1016/j.neuroimage.2015.12.012

6) Another concern is the extent to which across-subject similarity will only capture consistent patterns across people, making this analysis very similar to a traditional univariate analysis (and unlike the traditional use of RSA to capture subject-specific patterns).

With proper normalization, we assume voxels across different subjects should show some consistent localizations, although individual differences can be high. J. Chen et al. (2017) has demonstrated that consistent multi-voxel activation patterns exist across individuals. Previous studies have also successfully applied cross-subject RSA (see review by Freund et al, 2021) and cross-subject decoding approaches (e.g., Jiang et al., 2016; Tusche et al., 2016), so we believe cross-subject RSA should be feasible to capture distributed activation patterns shared at the group level. We added this argument in the revised manuscript:

"Previous studies (e.g., J. Chen et al., 2017) have demonstrated that consistent multivoxel activation patterns exist across individuals, and successful applications of cross-subject RSA (see review by Freund, Etzel, et al., 2021) and cross-subject decoding approaches (Jiang et al., 2016; Tusche et al., 2016) have also been reported."

In the revised manuscript, we also tested whether the representation in right 8C held for within-subject data. We reasoned that the conflict similarity effects identified by cross-subject RSA should be replicable in within-subject data, although the latter is not able to dissociate the conflict similarity effect from the orientation effect. We performed similar RSA for within-subject RSMs, excluding the within-run cells. We replaced the perfectly confounded factors of conflict similarity and orientation with a common factor called similarity_orientation. Other confounding factor pairs were addressed similarly. Results showed a significant effect of similarity_orientation, t(13993) = 3.270, p = .0005, 1-tailed. Given the specific representation of conflict similarity identified by the cross-subject RSA, we believe that the within-subject data of right 8C probably showed similar conflict similarity modulation effects as the cross-subject data, although future research that orthogonalizes conflict type and orientation is needed to fully answer this question. We added this result in the revised section Note S7.

"Note S7. The cross-subject RSA captures similar effects with the within-subject RSA Considering the variability in voxel-level functional localizations among individuals, one may question whether the cross-subject RSA results were biased by the consistent multi-voxel patterns across subjects, distinct from the more commonly utilized withinsubject RSA. We reasoned that the cross-subject RSA should have captured similar effects as the within-subject RSA if we observe the conflict similarity effect in right 8C with the latter analysis. Therefore, we tested whether the representation in right 8C held for within-subject data. Specifically, we performed similar RSA for withinsubject RSMs, excluding the within-run cells. We replaced the perfectly confounded factors of conflict similarity and orientation with a common factor called similarity_orientation. Other confounding factor pairs (i.e., target versus response, and Stroop distractor versus Simon distractor) were addressed similarly. Results showed a significant effect of similarity_orientation, t(13993) = 3.270, p = .0005, 1tailed. Given the specific representation of conflict similarity identified by the crosssubject RSA, the within-subject data of right 8C may show similar conflict similarity modulation effects as the cross-subject data. Further research is needed to fully dissociate the representation of conflict and the representation of visual features such as orientation."

Reference:

Chen, J., Leong, Y. C., Honey, C. J., Yong, C. H., Norman, K. A., & Hasson, U. (2017). Shared memories reveal shared structure in neural activity across individuals. Nature Neuroscience, 20(1), 115-125.

Freund, M. C., Etzel, J. A., & Braver, T. S. (2021). Neural Coding of Cognitive Control: The Representational Similarity Analysis Approach. Trends in Cognitive Sciences, 25(7), 622-638.

Jiang, J., Summerfield, C., & Egner, T. (2016). Visual Prediction Error Spreads Across Object Features in Human Visual Cortex. J Neurosci, 36(50), 12746-12763.

Tusche, A., Bockler, A., Kanske, P., Trautwein, F. M., & Singer, T. (2016). Decoding the Charitable Brain: Empathy, Perspective Taking, and Attention Shifts Differentially Predict Altruistic Giving. Journal of Neuroscience, 36(17), 4719-4732.

7) Finally, the authors should confirm all their results are robust to less liberal methods of multiplicity correction. For univariate analysis, they should report the effects from the standard p < .001 cluster forming threshold for univariate analysis (or TFCE). For multivariate analyses, FDR can be quite liberal. The authors should consider whether their mixed-effects analyses allow for group-level randomization, and consider (relatively powerful) Max-Stat randomization tests (Nichols & Holmes, 2002, Hum Brain Mapp).

In our revised manuscript, we have corrected the univariate results using the probabilistic TFCE (pTFCE) approach by Spisak et al. (2019). This approach estimates the conditional probability of cluster extent based on Bayes’ rule. Specifically, we applied pTFCE on our univariate results (i.e., the z-maps of our contrasts). This returned enhanced Z-score maps, which were then thresholded based on simulated cluster size thresholds using 3dClustSim. A cluster-forming threshold of p < .001 was employed. Results showed only the pre-SMA was activated in the incongruent > congruent contrast, and right IPS and right dmPFC were activated in the linear Simon modulation effect. Further tests also showed these regions were not correlated with the behavioral performance, uncorrected ps >.28. These results largely replicated our previous results. We have revised the method and results accordingly.

Methods:

"Results were corrected with the probabilistic threshold-free cluster enhancement(pTFCE) and then thresholded by 3dClustSim function in AFNI (Cox & Hyde, 1997) with voxel-wise p < .001 and cluster-wize p < .05, both 1-tailed."

Results:

"In the fMRI analysis, we first replicated the classic congruency effect by searching for brain regions showing higher univariate activation in incongruent than congruent conditions (GLM1, see Methods). Consistent with the literature (Botvinick et al., 2004; Fu et al., 2022), this effect was observed in the pre-supplementary motor area (preSMA) (Fig. 3, Table S1). We then tested the encoding of conflict type as a cognitive space by identifying brain regions with activation levels parametrically covarying with the coordinates (i.e., axial angle relative to the horizontal axis) in the hypothesized cognitive space. As shown in Fig. 1B, change in the angle corresponds to change in spatial Stroop and Simon conflicts in opposite directions. Accordingly, we found the right inferior parietal sulcus (IPS) and the right dorsomedial prefrontal cortex (dmPFC) displayed positive correlation between fMRI activation and the Simon conflict (Fig. 3, Fig. S3, Table S1)."

We appreciate the reviewer’s suggestion to apply the Max-Stat randomization tests (Nichols & Holmes, 2002) for the multivariate analyses. However, the representational similarity matrix was too large (1400×1400) to be tested with a balanced randomization approach (i.e., the Max-Stat), due to (1) running even 1000 times for all ROIs cost very long time; (2) the distribution generated from normal times of randomization (e.g., 5000 iterations) would probably be unbalanced, since the full range of possible samples that could be generated by a complete randomization is not adequately represented. Instead, we adopted a very strict Bonferroni correction p < 0.0001/360 when reporting the regression results from RSA. Notebally, Chen et al (2017) has shown that their approach could control the FDR at an acceptable level.

Reference:

Spisák, T., Spisák, Z., Zunhammer, M., Bingel, U., Smith, S., Nichols, T., & Kincses,T. (2019). Probabilistic TFCE: A generalized combination of cluster size and voxel intensity to increase statistical power. NeuroImage, 185, 12-26.

Chen, G., Taylor, P. A., Shin, Y.-W., Reynolds, R. C., & Cox, R. W. J. N. (2017). Untangling the relatedness among correlations, Part II: Inter-subject correlation group analysis through linear mixed-effects modeling. 147, 825-840.

Minor concerns:

8) I appreciate the authors wanting to present the conditions in a theory-agnostic way, but the framing of 5 conflict types was confusing. I think framing the conditions as a mixture of 2 conflict types (Stroop and Simon) makes more sense, especially given the previous work on MSIT.

We have renamed the Type1-5 as spatial Stroop, StHSmL, StMSmM, StLSmH, and Simon conditions, respectively. H, L, and M indicate high, low andmedium similarity with the corresponding conflict, respectively. This is alsoconsistent with the naming of our previous work (Yang et al., 2021).

Reference:

Yang, G., Xu, H., Li, Z., Nan, W., Wu, H., Li, Q., & Liu, X. (2021). The congruency sequence effect is modulated by the similarity of conflicts. Journal of Experimental Psychology: Learning, Memory, and Cognition, 47(10), 1705-1719.

9) It would be helpful to have more scaffolding for the key conflict & orientation analyses. A schematic in the main text that outlines these contrasts would be very helpful (e.g. similar to S4).

We have inserted Figure 7 in the revised manuscript. In this figure, we plotted the schematic of the difference between the conflict similarity 467 and orientation regressors according to their cross-group representational similarity 468 matrices.

10) Figure 4D could be clearer, both in labeling and figure caption. 'Modeled similarity' could be relabelled to something more informative, like 'conflict type (or mixture) similarity'. Alternatively, it would be helpful to show a summary RDM for region r-8C. For example, breaking it down by just conflict type and congruence.

We have relabeled the x-axis to “Conflict type similarity” and y-axis to “Neural similarity” for Figure 4D in the revised manuscript.

We have also added a summary RSM figure in Fig. S5 to show the different similarity patterns between incongruent and congruent conditions.

11) It may be helpful to connect your work to how people have discussed multiple forms of conflict monitoring and control with respect to target and distractor features e.g., Lindsay & Jacoby, 1994, JEP:HPP; Mante, Sussillo et al., 2013, Nature; Soutschek et al., 2015, JoCN; Jackson et al., 2021, Comm Bio; Ritz & Shenhav, 2022, bioRxiv

We have added an analysis to examine how cognitive control modulates target and distractor representation. To this end, we selected the left V4, a visual region showing joint representation of target, Stroop distractor and Simon distractor, as the region of interest. We tested whether these representation strengths differed between incongruent and congruent conditions, finding the representation of target was stronger and representations of both distractors were weaker in the incongruent condition. This suggests that cognitive control modulates the stimuli in both directions. We added the results in Note S10 and Fig. S8, and also added discussion of it in “Methodological implications”.

“Note S10. Cognitive control enhances target representation and suppresses distractor representation Using the separability of confounding factors afforded by the cross-subject RSA, we examined how representations of targets and distractors are modulated by cognitive control. The key assumption is that exerting cognitive control may enhance target representation and suppress distractor representation. We hypothesized that stimuli are represented in visual areas, so we chose a visual ROI from the main RSA results showing joint representation of target, spatial Stroop distractor and Simon distractor (p < .005, 1-tail, uncorrected). Only the left V4 met this criterion. We then tested representations with models similar to the main text for incongruent only trials, congruent only trials, and the incongruent – congruent contrast. The contrast model additionally used interaction between the congruency and target, Stroop distractor and Simon distractor terms. Results showed that in the incongruent condition, when we employ more cognitive control, the target representation was enhanced (t(237990) = 2.59, p = .029, Bonferroni corrected) and both spatial Stroop (t(237990) = –4.18, p < .001, Bonferroni corrected) and Simon (t(237990) = –3.14, p = .005, Bonferroni corrected) distractor representations were suppressed (Fig. S8). These are consistent with the idea that the top-down control modulates the stimuli in both directions (Polk et al., 2008; Ritz & Shenhav, 2022).”

Discussion:

“Moreover, the cross-subject RSA provides high sensitivity to the variables of interest and the ability to separate confounding factors. For instance, in addition to dissociating conflict type from orientation, we dissociated target from response, and spatial Stroop distractor from Simon distractor. We further showed cognitive control can both enhance the target representation and suppress the distractor representation (Note S10, Fig. S8), which is in line with previous studies (Polk et al., 2008; Ritz & Shenhav, 2022)."

12) For future work, I would recommend placing stimuli along the whole circumference, to orthogonalize Stroop and Simon conflict within-subject.

We thank the reviewer for this highly helpful suggestion. Expanding the 547 conflict conditions to a full conflict space and replicating our current results could 548 provide stronger evidence for the cognitive space view.

In the revised manuscript, we added this as a possible future design:

“A possible improvement to our current design would be to include left, right, up, and down arrows presented in a grid formation across four spatially separate quadrants, with each arrow mapped to its own response button. However, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity."

Reviewer #2:

Summary, general appraisal

This study examines the construct of "cognitive spaces" as they relate to neural coding schemes present in response conflict tasks. The authors utilize a novel paradigm, in which subjects must map the direction of a vertically oriented arrow to either a left or right response. Different types of conflict (spatial Stroop, Simon) are parametrically manipulated by varying the spatial location of the arrow (a taskirrelevant feature). The vertical eccentricity of the arrow either agrees or conflicts with the arrow's direction (spatial Stroop), while the horizontal eccentricity of the arrow agrees or conflicts with the side of the response (Simon). A neural coding model is postulated in which the stimuli are embedded in a cognitive space, organized by distances that depend only on the similarity of congruency types (i.e., where conditions with similar relative proportions of spatial-Stroop versus Simon congruency are represented with similar activity patterns). The authors conduct a behavioral and fMRI study to provide evidence for such a representational coding scheme. The behavioral findings replicate the authors' prior work in demonstrating that conflict-related cognitive control adjustments (the congruency sequence effect) shows strong modulation as a function of the similarity between conflict types. With the fMRI neural activity data, the authors report univariate analyses that identified activation in left prefrontal and dorsomedial frontal cortex modulated by the amount of Stroop or Simon conflict present, and multivariate representational similarity analyses (RSA) that identified right lateral prefrontal activity encoding conflict similarity and correlated with the behavioral effects of conflict similarity.

This study tackles an important question regarding how distinct types of conflict, which have been previously shown to elicit independent forms of cognitive control adjustments, might be encoded in the brain within a computationally efficient representational format. The ideas postulated by the authors are interesting ones and the utilized methods are rigorous.

We would like to express our sincere appreciation for the reviewer’s positive evaluation of our manuscript and the constructive comments and suggestions. Through careful consideration of your feedback, we have endeavored to make our manuscript more accessible to readers and further strengthened our findings. In response to your suggestion, we reanalyzed our data with the approach proposed by Chen et al.’s (2017, NeuroImage). This reanalysis largely replicated our previous results, reinforcing the validity of our findings. Additionally, we conducted tests with several alternative models and found that the cognitive space hypothesis best aligns with our observed data. We have incorporated these revisions and additional analyses into the manuscript based on your valuable feedback. As a result, we believe that these changes and additional analyses have significantly enhanced the quality of our manuscript. We have provided detailed responses to your comments below.

However, the study has critical limitations that are due to a lack of clarity regarding theoretical hypotheses, serious confounds in the experimental design, and a highly non-standard (and problematic) approach to RSA. Without addressing these issues it is hard to evaluate the contribution of the authors findings to the computational cognitive neuroscience literature.

1) The primary theoretical question and its implications are unclear. The paper would greatly benefit from more clearly specifying potential alternative hypotheses and discussing their implications. Consider, for example, the case of parallel conflict monitors. Say that these conflict monitors are separately tuned for Stroop and Simon conflict, and are located within adjacent patches of cortex that are both contained within a single cortical parcel (e.g., as defined by the Glasser atlas used by the authors for analyses). If RSA was conducted on the responses of such a parcel to this task, it seems highly likely that an activation similarity matrix would be observed that is quite similar (if not identical) to the hypothesized one displayed in Figure 1. Yet it would seem like the authors are arguing that the "cognitive space" representation is qualitatively and conceptually distinct from the "parallel monitor" coding scheme. Thus, it seems that the task and analytic approach is not sufficient to disambiguate these different types of coding schemes or neural architectures.

The authors also discuss a fully domain-general conflict monitor, in which different forms of conflict are encoded within a single dimension. Yet this alternative hypothesis is also not explicitly tested nor discussed in detail. It seems that the experiment was designed to orthogonalize the "domain-general" model from the "cognitive space" model, by attempting to keep the overall conflict uniform across the different stimuli (i.e., in the design, the level of Stroop congruency parametrically trades off with the level of Simon congruency). But in the behavioral results (Fig. S1), the interference effects were found to peak when both Stroop and Simon congruency are present (i.e., Conf 3 and 4), suggesting that the "domain-general" model may not be orthogonal to the "cognitive space" model. One of the key advantages of RSA is that it provides the ability to explicitly formulate, test and compare different coding models to determine which best accounts for the pattern of data. Thus, it would seem critical for the authors to set up the design and analyses so that an explicit model comparison analysis could be conducted, contrasting the domain-general, domain-specific, and cognitive space accounts.

We appreciate the reviewer pointing out the need to formally test alternative models. In the revised manuscript, we have added and compared a few alternative models, finding the Cognitive-Space model (the one with graded conflict similarity levels as we reported) provided the best fit to our data. Specifically, we tested the following five models against the Cognitive-Space model:

(1) Domain-General model. This model treats each conflict type as equivalent, so each two conflict types only differ in the magnitude of their conflict. Therefore, we defined the domain-general matrix as the difference in their effects indexed by the group-averaged RT in Experiment 2. Then the z-scored model vector was sign-flipped to reflect similarity instead of distance. This model showed non-significant conflict type effects (t(951989) = 0.92, p = .179) and poorer fit (BIC = 5377126) than the Cognitive-Space model (BIC = 5377094).

(2) Domain-Specific model. This model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all crossconflict type similarities being 0. This model also showed non-significant effects (t(951989) = 0.84, p = .201) and poorer fit (BIC = 5377127) than the Cognitive-Space model.

(3) Stroop-Only model. This model assumes that the right 8C only encodes the spatial Stroop conflict. We projected each conflict type to the Stroop (vertical) axis and calculated the similarity between any two conflict types as the Jaccard similarity index (Jaccard, 1901), that is, their intersection divided by their union. This model also showed non-significant effects (t(951989) = 0.20, p = .423) and poorer fit (BIC = 5377122) than the Cognitive-Space model.

(4) Simon-Only model. This model assumes that the right 8C only encodes the Simon conflict. We projected each conflict type to the Simon (horizontal) axis and calculated the similarity like the Stroop-Only model. This model showed significant effects (t(951989) = 4.19, p < .001) but still quantitatively poorer fit (BIC = 5377096) than the Cognitive-Space model.

(5) Stroop+Simon model. This model assumes the spatial Stroop and Simon conflicts are parallelly encoded in the brain, similar to the "parallel monitor" hypothesis suggested by the reviewer. It includes both Stroop-Only and Simon-Only regressors. This model showed nonsignificant effect for the Stroop regressor (t(951988) = 0.06, p = .478) and significant effect for the Simon regressor (t(951988) = 3.30, p < .001), but poorer fit (BIC = 5377118) than the Cognitive-Space model.

“Moreover, we replicated these results with only incongruent trials (i.e., when conflict is present), considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104).”

In summary, these results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. We added the above results to the revised manuscript.

The above analysis approach was added to the method “Model comparison and representational dimensionality”, and the results were added to the “Multivariate patterns of the right dlPFC encodes the conflict similarity” in the revised manuscript.

Methods:

“Model comparison and representational dimensionality To estimate if the right 8C specifically encodes the cognitive space, rather than the domain-general or domain-specific structures, we conducted two more RSAs. We replaced the cognitive space-based conflict similarity matrix in the RSA we reported above (hereafter referred to as the Cognitive-Space model) with one of the alternative model matrices, with all other regressors equal. The domain-general model treats each conflict type as equivalent, so each two conflict types only differ in the magnitude of their conflict. Therefore, we defined the domain-general matrix as the difference in their congruency effects indexed by the group-averaged RT in Experiment 2. Then the zscored model vector was sign-flipped to reflect similarity instead of distance. The domain-specific model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all cross-conflict type similarities being 0.

Moreover, to examine if the cognitive space is driven solely by the Stroop or Simon conflicts, we tested a spatial Stroop-Only (hereafter referred to as “Stroop-Only”) and a Simon-Only model, with each conflict type projected onto the spatial Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, 1901), that is, their intersection divided by their union. We also included a model assuming the Stroop and Simon dimensions are independently represented in the brain, adding up the StroopOnly and Simon-Only regressors (hereafter referred to as the Stroop+Simon model). We conducted similar RSAs as reported above, replacing the original conflict similarity regressor with the Strrop-Only, Simon-Only, or both regressors (for the Stroop+Simon model), and then calculated their Bayesian information criterions (BICs).”

Results:

“To examine if the right 8C specifically encodes the cognitive space rather than the domain-general or domain-specific organizations, we tested several additional models (see Methods). Model comparison showed a lower BIC in the Cognitive-Space model (BIC = 5377094) than the Domain-General (BIC = 537127) or Domain-Specific (BIC = 537127) models. Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D. We also tested if the observed conflict similarity effect was driven solely by spatial Stroop or Simon conflicts, and found larger BICs for the models only including the Stroop similarity (i.e., the Stroop-Only model, BIC = 5377122) or Simon similarity (i.e., the Simon-Only model, BIC = 5377096). An additional Stroop+Simon model, including both StroopOnly and Simon-Only regressors, also showed a worse model fitting (BIC = 5377118). Moreover, we replicated the results with only incongruent trials, considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. The more detailed model comparison results are listed in Table 2.”

Reference:

Jaccard, P. (1901). Étude comparative de la distribution florale dans une portion des Alpes et des Jura. Bull Soc Vaudoise Sci Nat(37), 547-579.

2a) Relatedly, the reasoning for the use of the term "cognitive space" is unclear. The mere presence of graded coding for two types of conflict seems to be a low bar for referring to neural activity patterns as encoding a "cognitive space". It is discussed that cognitive spaces/maps allow for flexibility through inference and generalization. But no links were made between these cognitive abilities and the observed representational structure.

In the revised manuscript, we have clarified that we tested a specific prediction of the cognitive space hypothesis: the geometry of the cognitive space predicts that more similar conflict types will have more similar neural representations,leading to the CSE and RSA patterns tested in this study. These results add to the literature by providing empirical evidence on how different conflict types are encoded in the brain. We agree that this study is not a comprehensive test of the cognitive space hypothesis. Thus, in the revised manuscript we explicitly clarified that this study is a test of the geometry of the cognitive space hypothesis.

Critically, the cognitive space view holds that the representations of different abstract information are organized continuously and the representational geometry in the cognitive space are determined by the similarity among the represented information (Bellmund et al., 2018).

"The present study aimed to test the geometry of cognitive space in conflict representation. Specifically, we hypothesize that different types of conflict are represented as points in a cognitive space. Importantly, the distance between the points, which reflects the geometry of the cognitive space, scales with the difference in the sources of the conflicts being represented by the points."

We have also discussed the limitation of the results and stressed the need for more research to fully test the cognitive space hypothesis.

“Additionally, our study is not a comprehensive test of the cognitive space hypothesis but aimed primarily to provide original evidence for the geometry of cognitive space in representing conflict information in cognitive control. Future research should examine other aspects of the cognitive space such as its dimensionality, its applicability to other conflict tasks such as Eriksen Flanker task, and its relevance to other cognitive abilities, such as cognitive flexibility and learning.

2b) Additionally, no explicit tests of generality (e.g., via cross-condition generalization) were provided.

To examine the generality of cognitive space across conditions, we conducted a leave-one-out prediction analysis. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model as reported in the main text (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001. We have added this analysis and result to the “Conflict type 706 similarity modulated behavioral congruency sequence effect (CSE)” section.

“Moreover, to test the continuity and generalizability of the similarity modulation, we conducted a leave-one-out prediction analysis. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001."

2c) Finally, although the design elicits strong CSE effects, it seems somewhat awkward to consider CSE behavioral patterns as a reflection of the kind of abilities supported by a cognitive map (if this is indeed the implication that was intended). In fact, CSE effects are well-modeled by simpler "model-free" associative learning processes, that do not require elaborate representations of abstract structures.

We argue the conflict similarity modulation of CSEs we observed cannot be explained by the “model-free” stimulus-driven associative learning process. This mainly refers to the feature integration account proposed by Hommel et al. (2004), which explains poorer performance in CI and IC trials (compared with CC and II trials) with the partial repetition cost caused by the breaking of stimulus-response binding. Although we cannot remove its influence on the within-type trials (similarity level 5, θ = 0), it should not affect the cross-type trials (similarity level 1-4, θ = 90°, 67.5°, 45° and 22.5°, respectively), because the CC, CI, IC, II trials had equal probabilities of partially repeated and fully switched trials (see the Author response image 1 for an example of trials across Conf 1 and Conf 3 conditions). Thus, feature integration cannot explain the gradual CSE decrease from similarity level 1 to 4, which sufficiently reproduce the full effect, as suggested by the leave-one-out prediction analysis mentioned above. We thus conclude that the similarity modulation of CSE cannot be explained by the stimulus-driven associative learning.

Author response image 1.

Notably, however, our findings are aligned with an associative learning account of cognitive control (Abrahamse et al., 2016), which extends association learning from stimulus/response level to cognitive control. In other words, abstract cognitive control state can be learned and generalized like other sensorimotor features. This view explicitly proposes that “transfer occurs to the extent that two tasks overlap”, a hypothesis directly supported by our CSE results (see also Yang et al., 2021). Extending this, our fMRI results provide the neural basis of how cognitive control can generalize through a representation of cognitive space. The cognitive space view complements associative learning account by providing a fundamental principle for the learning and generalization of control states. Given the widespread application of CSE as indicator of cognitive control generalization (Braem et al., 2014), we believe that it can be recognized as a kind of ability supported by the cognitive space. This was further supported by the brain-behavioral correlation: stronger encoding of cognitive space was associated with greater bias of trial-wise behavioral adjustment by the consecutive conflict similarity.

We have incorporated these ideas into the discussion:

“Similarly, we propose that cognitive space could serve as a mental model to assist fast learning and efficient organization of cognitive control settings. Specifically, the cognitive space representation may provide a principle for how our brain evaluates the expected cost of switching and the benefit of generalization between states and selects the path with the best cost-benefit tradeoff (Abrahamse et al., 2016; Shenhav et al., 2013). The proximity between two states in cognitive space could reflect both the expected cognitive demand required to transition and the useful mechanisms to adapt from. The closer the two conditions are in cognitive space, the lower the expected switching cost and the higher the generalizability when transitioning between them. With the organization of a cognitive space, a new conflict can be quickly assigned a location in the cognitive space, which will facilitate the development of cognitive control settings for this conflict by interpolating nearby conflicts and/or projecting the location to axes representing different cognitive control processes, thus leading to a stronger CSE when following a more similar conflict condition.”

References:

Hommel, B., Proctor, R. W., & Vu, K. P. (2004). A feature-integration account of sequential effects in the Simon task. Psychological Research, 68(1), 1-17. Abrahamse, E., Braem, S., Notebaert, W., & Verguts, T. (2016). Grounding cognitive control in associative learning. Psychological Bulletin, 142(7), 693-728.

Yang, G., Xu, H., Li, Z., Nan, W., Wu, H., Li, Q., & Liu, X. (2021). The congruency sequence effect is modulated by the similarity of conflicts. Journal of 770 Experimental Psychology: Learning, Memory, and Cognition, 47(10), 1705-1719.

Braem, S., Abrahamse, E. L., Duthoo, W., & Notebaert, W. (2014). What determines the specificity of conflict adaptation? A review, critical analysis, and proposed synthesis. Frontiers in Psychology, 5, 1134.

3) More generally, it seems problematic that Stroop and Simon conflict in the paradigm parametrically trade-off against each other. A more powerful design would have de-confounded Stroop and Simon conflict so that each could be separately estimation via (potentially orthogonal) conflict axes. Additionally, incorporating more varied stimulus sets, locations, or responses might have enabled various tests of generality, as implied by a cognitive space account.

We thank the reviewer for these valuable suggestions. We argue that the current design is adequate to test the prediction that more similar conflict types have more similar neural representations. That said, we agree that further examination using more powerful experimental designs are needed to fully test the cognitive space account of cognitive control. We also agree that employing more varied stimulus sets,locations and responses would further extend our findings. We have included this as a future research direction in the revised manuscript.

We have revised our discussion about the limitation as:

“A few limitations of this study need to be noted. To parametrically manipulate the conflict similarity levels, we adopted the spatial Stroop-Simon paradigm that enables parametrical combinations of spatial Stroop and Simon conflicts. However, since this paradigm is a two-alternative forced choice design, the behavioral CSE is not a pure measure of adjusted control but could be partly confounded by bottom-up factors such as feature integration (Hommel et al., 2004). Future studies may replicate our findings with a multiple-choice design (including more varied stimulus sets, locations and responses) with confound-free trial sequences (Braem et al., 2019). Another limitation is that in our design, the spatial Stroop and Simon effects are highly anticorrelated. This constraint may make the five conflict types represented in a unidimensional space (e.g., a circle) embedded in a 2D space. Future studies may test the 2D cognitive space with fully independent conditions. A possible improvement to our current design would be to include left, right, up, and down arrows presented in a grid formation across four spatially separate quadrants, with each arrow mapped to its own response button. However, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity.”

4) Serious confounds in the design render the results difficult to interpret. As much prior neuroimaging and behavioral work has established, "conflict" per se is perniciously correlated with many conceptually different variables. Consequently, it is very difficult to distinguish these confounding variables within aggregate measures of neural activity like fMRI. For example, conflict is confounded with increased time-on-task with longer RT, as well as conflict-driven increases in coding of other task variables (e.g., task-set related coding; e.g., Ebitz et al. 2020 bioRxiv). Even when using much higher resolution invasive measures than fMRI (i.e., eCoG), researchers have rightly been wary of making strong conclusions about explicit encoding of conflict (Tang et al, 2019; eLife). As such, the researchers would do well to be quite cautious and conservative in their analytic approach and interpretation of results.

We acknowledge the findings showing that encoding of conflicts may not be easily detected in the brain. However, recent studies have shown that the representational similarity analysis can effectively detect representations of conflict tasks (e.g., the color Stroop) using factorial designs (Freund et al., 2021a; 2021b).

In our analysis, we are aware of the potential impact of time-on-task (e.g., RT) on univariate activation levels and subsequent RSA patterns. To address this issue, we added univariate fMRI activation levels as nuisance regressors to the RSA. To de confound conflict from other factors such as orientation of stimuli related to the center of the screen, we also applied the cross-subject RSA approach. Furthermore, we were cautious about determining regions that encoded conflict control. We set three strict criteria: (1) Regions must show a conflict similarity modulation effect; (2) regions must show higher representational strength in the incongruent condition compared with the congruent condition; and (3) regions must correlate with behavioral performance. With these criteria, we believe that the results we reported are already conservative. We would be happy to implement any additional criteria the reviewer recommends.

Reference:

Freund, M. C., Etzel, J. A., & Braver, T. S. (2021a). Neural Coding of Cognitive Control: The Representational Similarity Analysis Approach. Trends in Cognitive Sciences, 25(7), 622-638.

Freund, M. C., Bugg, J. M., & Braver, T. S. (2021b). A Representational Similarity 823 Analysis of Cognitive Control during Color-Word Stroop. Journal of 824 Neuroscience, 41(35), 7388-7402.

5) This issue is most critical in the interpretation of the fMRI results as reflecting encoding of conflict types. A key limitation of the design, that is acknowledged by the authors is that conflict is fully confounded within-subject by spatial orientation. Indeed, the limited set of stimulus-response mappings also cast doubt on the underlying factors that give rise to the CSE modulations observed by the authors in their behavioral results. The CSE modulations are so strong - going from a complete absence of current x previous trial-type interaction in the cos(90) case all the way to a complete elimination of any current trial conflict when the prior trial was incongruent in the cos(0) case - that they cause suspicion that they are actually driven by conflict-related control adjustments rather than sequential dependencies in the stimulus-response mappings that can be associatively learned.

Unlike the fMRI data, we cannot tease apart the effects of conflict similarity and orientation in a similar manner as the cross-subject RSA for behavioral CSEs. However, we have a few reasons that the orientation and other bottom-up factors should not be the factors driving the similarity modulation effect.

First, we did not find any correlation between the regions showing orientation effects and behavioral CSEs. This suggests that orientation does not directly contribute to the CSE modulation.

Second, if the CSE modulation is purely driven by the association learning of the stimulus-response mapping, we should observe a stronger modulation effect after more extensive training. However, our results do not support this prediction. Using data from Experiment 1, we found that the modulation effect remained constant across the three sessions (see Note S3).

“Note S3. Modulation of conflict similarity on behavioral CSEs does not change across time We tested if the conflict similarity modulation on the CSE is susceptible to training. We collected the data of Experiment 1 across three sessions, thus it is possible to examine if the conflict similarity modulation effect changes across time. To this end, we added conflict similarity, session and their interaction into a mixed-effect linear model, in which the session was set as a categorical variable. With a post-hoc analysis of variance (ANOVA), we calculated the statistical significance of the interaction term. This approach was applied to both the RT and ER. Results showed no interaction effect in either RT, F(2,1479) = 1.025, p = .359, or ER, F(2,1479) = 0.789, p = .455. This result suggests that the modulation effect does not change across time. “

Third, the observed similarity modulation on the CSE, particularly for similarity levels 1-4, should not be attributed to the stimulus-response associations, such as feature integration, as have been addressed in response to comment 2.c.

Finally, other bottom-up factors, such as the spatial location proximity did not drive the CSE modulation results, which we have addressed in the original manuscript in Note S2.

"Note S2. Modulation of conflict similarity on behavioral CSEs cannot be explained by the physical proximity

In our design, the conflict similarity might be confounded by the physical proximity between stimulus (i.e., the arrow) of two consecutive trials. That is, when arrows of the two trials appear at the same quadrant, a higher conflict similarity also indicates a higher physical proximity (Fig. 1A). Although the opposite is true if arrows of the two trials appear at different quadrants, it is possible the behavioral effects can be biased by the within quadrant trials. To examine if the physical distance has confounded the conflict similarity modulation effect, we conducted an additional analysis.

We defined the physical angular difference across two trials as the difference of their polar angles relative to the origin. Therefore, the physical angular difference could vary from 0 to 180°. For each CSE conditions (i.e., CC, CI, IC and II), we grouped the trials based on their physical angular distances, and then averaged trials with the same previous by current conflict type transition but different orders (e.g., StHSmL−StLSmH and StLSmH−StHSmL) within each subject. The data were submitted to a mixed-effect model with the conflict similarity, physical proximity (i.e., the opposite of the physical angular difference) as fixed-effect predictors, and subject and CSE condition as random effects. Results showed significant conflict similarity modulation effects in both Experiment 1 (RT: β = 0.09 ± 0.01, t(7812) = 13.74, p < .001, ηp2 = .025; 875 ER: β = 0.09 ± 0.01, t(7812) = 7.66, p < .001, ηp2 = .018) and Experiment 2 (RT: β = 876 0.21 ± 0.02, t(3956) = 9.88, p < .001, ηp2 = .043; ER: β = 0.20 ± 0.03, t(4201) = 6.11, 877 p < .001, ηp2 = .038). Thus, the observed modulation of conflict similarity on behavioral 878 CSEs cannot be explained by physical proximity."

6) To their credit, the authors recognize this confound, and attempt to address it analytically through the use of a between-subject RSA approach. Yet the solution is itself problematic, because it doesn't actually deconfound conflict from orientation. In particular, the RSA model assumes that whatever components of neural activity encode orientation produce this encoding within the same voxellevel patterns of activity in each subject. If they are not (which is of course likely), then orthogonalization of these variables will be incomplete. Similar issues underlie the interpretation target/response and distractor coding. Given these issues, perhaps zooming out to a larger spatial scale for the between-subject RSA might be warranted. Perhaps whole-brain at the voxel level with a high degree of smoothing, or even whole-brain at the parcel level (averaging per parcel). For this purpose, Schaefer atlas parcels might be more useful than Glasser, as they more strongly reflect functional divisions (e.g., motor strip is split into mouth/hand divisions; visual cortex is split into central/peripheral visual field divisions). Similarly, given the lateralization of stimuli, if a within-parcel RSA is going to be used, it seems quite sensible to pool voxels across hemispheres (so effectively using 180 parcels instead of 360).

Doing RSA at the whole-brain level is an interesting idea. However, it does not allow the identification of specific brain regions representing the cognitive space. Additionally, increasing the spatial scale would include more voxels that are not involved in representing the information of interest and may increase the noise level of data. Given these concerns, we did not conduct the whole-brain level RSA.

We agree that smoothing data can decrease cross-subject variance in voxel distribution and may increase the signal-noise ratio. We reanalyzed the results for the right 8C region using RSA on smoothed beta maps (6-mm FWHM Gaussian kernel). This yielded a significant conflict similarity effect, t(951989) = 5.55, p < .0001, replicating the results on unsmoothed data (t(951989) = 5.60, p < .0001). Therefore, we retained the results from unsmoothed data in the main text, and added the results based on smoothed data to the supplementary material (Note S9).

“Note S9. The cross-subject pattern similarity is robust against individual differences Due to individual differences, the multivoxel patterns extracted from the same brain mask may not reflect exactly the same brain region for each subject. To reduce the influence of individual difference, we conducted the same cross-subject RSA using data smoothed with a 6-mm FWHM Gaussian kernel. Results showed a significant conflict similarity effect, t(951989) = 5.55, p < .0001, replicating the results on unsmoothed data (t(951989) = 5.60, p < .0001). “

We also used the bilateral 8C area as a single mask and conducted the same RSA. We found a significant conflict type similarity effect, t(951989) = 4.36, p < .0001. However, the left 8C alone showed no such representation, t(951989) = 0.38, p = .351, consistent with the right lateralized representation of cognitive space we reported in Note S8. Therefore, we used ROIs from each hemisphere separately.

“Note S8. The lateralization of conflict type representation

We observed the right 8C but not the left 8C represented the conflict type similarity. A further test is to show if there is a lateralization. We tested several regions of the left dlPFC, including the i6-8, 8Av, 8C, p9-46v, 46, 9-46d, a9-46v (Freund, Bugg, et al., 2021). We found that none of these regions show the representation of conflict type, all uncorrected ps > .35. These results indicate that the conflict type is specifically represented in the right dlPFC. “

We have also discussed the lateralization in the manuscript:

“In addition, we found no such representation in the left dlPFC (Note S8), indicating a possible lateralization. Previous studies showed that the left dlPFC was related to the expectancy-related attentional set up-regulation, while the right dlPFC was related to the online adjustment of control (Friehs et al., 2020; Vanderhasselt et al., 2009), which is consistent with our findings. Moreover, the right PFC also represents a composition of single rules (Reverberi et al., 2012), which may explain how the spatial Stroop and Simon types can be jointly encoded in a single space.”

7) The strength of the results is difficult to interpret due to the non-standard analysis method. The use of a mixed-level modeling approach to summarize the empirical similarity matrix is an interesting idea, but nevertheless is highly non-standard within RSA neuroimaging methods. More importantly, the way in which it was implemented makes it potentially vulnerable to a high degree of inaccuracy or bias. In this case, this bias is likely to be overly optimistic (high false positive rate). No numerical or formal defense was provided for this mixed-level model approach. As a result, the use of this method seems quite problematic, as it renders the strength of the observed results difficult to interpret. Instead, the authors are encouraged using a previously published method of conducting inference with between-subject RSA, such as the bootstrapping methods illustrated in Kragel et al. (2018; Nat Neurosci), or in potentially adopting one of the Chen et al. methods mentioned above, that have been extensively explored in terms of statistical properties.

No numerical or formal defense was provided for this mixed-level model approach. As a result, the use of this method seems quite problematic, as it renders the strength of the observed results difficult to interpret. Instead, the authors are encouraged using a previously published method of conducting inference with between-subject RSA, such as the bootstrapping methods illustrated in Kragel et al. (2018; Nat Neurosci), or in potentially adopting one of the Chen et al. methods mentioned above, that have been extensively explored in terms of statistical properties.

In our revised manuscript, we have adopted the approach proposed by Chen et al. (2017). Specifically, we included both the upper and lower triangle of the representational similarity matrix (excluding the diagonal). Moreover, we also removed all the within-subject similarity (thus also excluding the within-run similarity) to minimize the bias of the potentially strong within-subject similarity (note we also analyzed the within-subject data and found significant effects for the similarity modulation, though this effect cannot be attributed to the conflict similarity or orientation alone. We added this part in Note S7, see below). In addition, we added both the row-wise and column-wise random effects to capture the dependence of cells within each column/row (Chen et al., 2017). We have revised the method part as:

“We excluded within-subject cells from the RSM (thus also excluding the withinrun similarity as suggested by Walther et al., (2016)), and the remaining cells were converted into a vector, which was then z-transformed and submitted to a linear mixed effect model as the dependent variable. The linear mixed effect model also included regressors of conflict similarity and orientation similarity. Importantly, conflict similarity was based on how Simon and spatial Stroop conflicts are combined and hence was calculated by first rotating all subject’s stimulus location to the topright and bottom-left quadrants, whereas orientation was calculated using original stimulus locations. As a result, the regressors representing conflict similarity and orientation similarity were de-correlated. Similarity between two conditions was measured as the cosine value of the angular difference. Other regressors included a target similarity regressor (i.e., whether the arrow directions were identical), a response similarity regressor (i.e., whether the correct responses were identical); a spatial Stroop distractor regressor (i.e., vertical distance between two stimulus locations); a Simon distractor regressor (i.e., horizontal distance between two stimulus locations). Additionally, we also included a regressor denoting the similarity of Group (i.e., whether two conditions are within the same subject group, according to the stimulus-response mapping). We also added two regressors including ROImean fMRI activations for each condition of the pair to remove the possible uni-voxel influence on the RSM. A last term was the intercept. To control the artefact due to dependence of the correlation pairs sharing the same subject, we included crossed random effects (i.e., row-wise and column-wise random effects) for the intercept, conflict similarity, orientation and the group factors (G. Chen et al., 2017).”

Results from this approach highly replicated our original results. Specifically, we found the right 8C again showed a strong conflict similarity effect, a higher representational strength in the incongruent condition compared to the congruent condition, and a significant correlation with the behavioral CSE. The orientation effect was also identified in the visual (e.g., right V1) and oculomotor (e.g., left FEF) regions.

We revised the results accordingly:

For the conflict type effect:

“The first criterion revealed several cortical regions encoding the conflict similarity, including the Brodmann 8C area (a subregion of dlPFC(Glasser et al., 2016)) and a47r in the right hemisphere, and the superior frontal language (SFL) area, 6r, 7Am, 24dd, and ventromedial visual area 1 (VMV1) areas in the left hemisphere (Bonferroni corrected ps < 0.0001, one-tailed, Fig. 4A). We next tested whether these regions were related to cognitive control by comparing the strength of conflict similarity effect between incongruent and congruent conditions (criterion 2). Results revealed that the left SFL, left VMV1, and right 8C met this criterion, Bonferroni corrected ps < .05, one-tailed, suggesting that the representation of conflict type was strengthened when conflict was present (e.g., Fig. 4D). The intersubject brain-behavioral correlation analysis (criterion 3) showed that the strength of conflict similarity effect on RSM scaled with the modulation of conflict similarity on the CSE (slope in Fig. S2C) in right 8C (r = .52, Bonferroni corrected p = .002, onetailed, Fig. 4C, Table 1) but not in the left SFL and VMV1 (all Bonferroni corrected ps > .05, one-tailed). “

For the orientation effect:

“We observed increasing fMRI representational similarity between trials with more similar orientations of stimulus location in the occipital cortex, such as right V1, right V2, right V4, and right lateral occipital 2 (LO2) areas (Bonferroni corrected ps < 0.0001). We also found the same effect in the oculomotor related region, i.e., the left 997 frontal eye field (FEF), and other regions including the right 5m, left 31pv and right parietal area F (PF) (Fig. 5A). Then we tested if any of these brain regions were related to the conflict representation by comparing their encoding strength between incongruent and congruent conditions. Results showed that the right V1, right V2, left FEF, and right PF encoded stronger orientation effect in the incongruent than the congruent condition, Bonferroni corrected ps < .05, one-tailed (Table1, Fig. 5B). We then tested if any of these regions was related to the behavioral performance, and results showed that none of them positively correlated with the behavioral conflict similarity modulation effect, all uncorrected ps > .45, one-tailed. Thus all regions are consistent with the criterion 3.”

“Note S7. The cross-subject RSA captures similar effects with the within-subject RSA Considering the variability in voxel-level functional localizations among individuals, one may question whether the cross-subject RSA results were biased by the consistent multi-voxel patterns across subjects, distinct from the more commonly utilized withinsubject RSA. We reasoned that the cross-subject RSA should have captured similar effects as the within-subject RSA if we observe the conflict similarity effect in right 8C with the latter analysis. Therefore, we tested whether the representation in right 8C held for within-subject data. Specifically, we performed similar RSA for withinsubject RSMs, excluding the within-run cells. We replaced the perfectly confounded factors of conflict similarity and orientation with a common factor called similarity_orientation. Other confounding factor pairs (i.e., target versus response, and Stroop distractor versus Simon distractor) were addressed similarly. Results showed a significant effect of similarity_orientation, t(13993) = 3.270, p = .0005, 1tailed. Given the specific representation of conflict similarity identified by the crosssubject RSA, the within-subject data of right 8C may show similar conflict similarity modulation effects as the cross-subject data. Further research is needed to fully dissociate the representation of conflict and the representation of visual features such as orientation.”

8) Another potential source of bias is in treating the subject-level random effect coefficients (as predicted by the mixed-level model) as independent samples from a random variable (in the t-tests). The more standard method for inference would be to use test statistics derived from the mixed-model fixed effects, as those have degrees of freedom calculations that are calibrated based on statistical theory.

In our revised manuscript, we reported the statistical p values calculated from the mixed-effect models. Note that because we used the Chen et al. (2017) method, which includes data from the symmetric matrix, we corrected the degrees of freedom and estimated the true p values based on the t statistics of model results. For the I versus C comparison results, we calculated the p values by combining I and C RSMs into a larger model and then adding the condition type, as well as the interaction between the regressors of interest (conflict similarity and orientation) and the condition type. We made the statistical inference based on the interaction effect.

We have revised the corresponding methods as:

“The statistical significance of these beta estimates was based on the outputs of the mixed-effect model estimated with the “fitlme” function in Matlab 2022a. Since symmetric cells from the RSM matrix were included in the mixed-effect model, we adjusted the t and p values with the true degree of freedom, which is half of the cells included minus the number of fixed regressors. Multiple comparison correction was applied with the Bonferroni approach across all cortical regions at the p < 0.0001 level. To test if the representation strengths are different between congruent and incongruent conditions, we also conducted the RSA using only congruent (RDM_C) and incongruent (RDM_I) trials separately. The contrast analysis was achieved by an additional model with both RDM_C and RDM_I included, adding the congruency and the interaction between conflict type (and orientation) and congruency as both fixed and random factors. The difference between incongruent and congruent representations was indicated by a significant interaction effect.”

Reviewer #3:

Yang and colleagues investigated whether information on two task-irrelevant features that induce response conflict is represented in a common cognitive space. To test this, the authors used a task that combines the spatial Stroop conflict and the Simon effect. This task reliably produces a beautiful graded congruency sequence effect (CSE), where the cost of congruency is reduced after incongruent trials. The authors measured fMRI to identify brain regions that represent the graded similarity of conflict types, the congruency of responses, and the visual features that induce conflicts.

Using several theory-driven exclusion criteria, the authors identified the right dlPFC (right 8C), which shows 1) stronger encoding of graded similarity of conflicts in incongruent trials and 2) a positive correlation between the strength of conflict similarity type and the CSE on behavior. The dlPFC has been shown to be important for cognitive control tasks. As the dlPFC did not show a univariate parametric modulation based on the higher or lower component of one type of conflict (e.g., having more spatial Stroop conflict or less Simon conflict), it implies that dissimilarity of conflicts is represented by a linear increase or decrease of neural responses. Therefore, the similarity of conflict is represented in multivariate neural responses that combine two sources of conflict.

The strength of the current approach lies in the clear effect of parametric modulation of conflict similarity across different conflict types. The authors employed a clever cross-subject RSA that counterbalanced and isolated the targeted effect of conflict similarity, decorrelating orientation similarity of stimulus positions that would otherwise be correlated with conflict similarity. A pattern of neural response seems to exist that maps different types of conflict, where each type is defined by the parametric gradation of the yoked spatial Stroop conflict and the Simon conflict on a similarity scale. The similarity of patterns increases in incongruent trials and is correlated with CSE modulation of behavior.

We would like to thank the reviewer for the positive evaluation of our manuscript and for providing constructive comments. By addressing these comments, we believe that we have made our manuscript more accessible for the readers while also strengthening our findings. In particular, we have tested a few alternative models and confirmed that the cognitive space hypothesis best fits the data. We have also demonstrated the geometric properties of the cognitive space by examining the continuity and dimensionality of the space, further supporting our main arguments. We have incorporated revisions and additional analyses to the manuscript based on your feedback. Overall, we believe that these changes and additional analyses have significantly improved the manuscript. Please find our detailed responses below.

However, several potential caveats need to be considered.

1) One caveat to consider is that the main claim of recruitment of an organized "cognitive space" for conflict representation is solely supported by the exclusion criteria mentioned earlier. To further support the involvement of organized space in conflict representation, other pieces of evidence need to be considered. One approach could be to test the accuracy of out-of-sample predictions to examine the continuity of the space, as commonly done in studies on representational spaces of sensory information. Another possible approach could involve rigorously testing the geometric properties of space, rather than fitting RSM to all conflict types. For instance, in Fig 6, both the organized and domain-specific cognitive maps would similarly represent the similarity of conflict types expressed in Fig1c (as evident from the preserved order of conflict types). The RSM suggests a low-dimensional embedding of conflict similarity, but the underlying dimension remains unclear.

Following the reviewer’s first suggestion, we conducted a leave-one-out prediction approach to examine the continuity of the cognitive space. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model as reported in the main text (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level at subject level. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001. We have added this analysis and result to the “Conflict type similarity modulated behavioral congruency sequence effect (CSE)” 1079 section:

“Moreover, to test the continuity and generalizability of the similarity modulation, we conducted a leave-one-out prediction analysis. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001.”

To estimate if the domain-specific model could explain the results we observed in right 8C, we conducted a model-comparison analysis. The domain-specific model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all cross-conflict type similarities being 0. This model showed non-significant effects (t(951989) = 0.84, p = .201) and poorer fit (BIC = 5377127) than the cognitive space model (t(951989) = 5.60, p = 1.1×10−8, BIC = 5377094). We also compared other alternative models and found the cognitive space model best fitted the data. We have included these results in the revised manuscript:

“To examine if the right 8C specifically encodes the cognitive space rather than the domain-general or domain-specific organizations, we tested several additional models (see Methods). Model comparison showed a lower BIC in the Cognitive-Space model (BIC = 5377094) than the Domain-General (BIC = 537127) or Domain-Specific (BIC = 537127) models. Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D. We also tested if the observed conflict similarity effect was driven solely by spatial Stroop or Simon conflicts, and found larger BICs for the models only including the Stroop similarity (i.e., the Stroop-Only model, BIC = 5377122) or Simon similarity (i.e., the Simon-Only model, BIC = 5377096). An additional Stroop+Simon model, including both StroopOnly and Simon-Only regressors, also showed a worse model fitting (BIC = 5377118). Moreover, we replicated the results with only incongruent trials, considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. The more detailed model comparison results are listed in Table 2.”

We also estimated the dimensionality of the right 8C with the averaged RSM and found the dimensionality of the cognitive space was ~ 1.19, very close to a 1D space. This result is consistent with our experimental design, as the only manipulated variable is the angular distance between conflict types. We have added these results and the methods to the revised manuscript.

Results:

“Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D.”

Methods:

“To better capture the dimensionality of the representational space, we estimated its dimensionality using the participation ratio (Ito & Murray, 2023). Since we excluded the within-subject cells from the whole RSM, the whole RSM is an incomplete matrix and could not be used. To resolve this issue, we averaged the cells corresponding to each pair of conflict types to obtain an averaged 5×5 RSM matrix, similar to the matrix shown in Fig. 1C. We then estimated the participation ratio using the formula:

where λi is the eigenvalue of the RSM and m is the number of eigenvalues.

2) Another important factor to consider is how learning within the confined task space, which always negatively correlates the two types of conflicts within each subject, may have influenced the current results. Is statistical dependence of conflict information necessary to use the organized cognitive space to represent conflicts from multiple sources? Answering this question would require a paradigm that can adjust multiple sources of conflicts parametrically and independently. Investigating such dependencies is crucial in order to better understand the adaptive utility of the observed cognitive space of conflict similarity.

As the central goal of our design was to test the geometry of neural representations of conflict, we manipulated the conflict similarity. The anticorrelated Simon and spatial Stroop conflict aimed to make the overall magnitude of conflict similar among different conflict types. We agree that with the current design the likely cognitive space is not a full 2D space with Simon and spatial Stroop being two dimensions. Instead, the likely cognitive space is a subspace (e.g., a circle) embedded in the 2D space, due to the constraint of anticorrelated Simon and spatial Stroop conflict across conflict types. Nevertheless, the subspace can also be used to test the geometry that similar conflict types share similar neural representations.

To test the full 2D cognitive space, a possible revision of our current design is to have multiple hybrid conditions (like Type 2-4) that cover the whole space. For instance, imagine arrow locations in the first quadrant space. We could have a 3×3 design with 9 conflict conditions, where their horizontal/vertical coordinates could be one of the combinations of 0, 0.5 and 1. This way, the spatial Stroop and Simon conditions would be independent of each other. Notably, however, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity.<br /> We have added the above limitations and future designs to the revised 1156 manuscript.

“Another limitation is that in our design, the spatial Stroop and Simon effects are highly anticorrelated. This constraint may make the five conflict types represented in a unidimensional space (e.g., a circle) embedded in a 2D space. Future studies may test the 2D cognitive space with fully independent conditions. A possible improvement to our current design would be to include left, right, up, and down arrows presented in a grid formation across four spatially separate quadrants, with each arrow mapped to its own response button. However, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity.”

Major comments:

3) The RSM result (and the absence of univariate effect) seem to be a good first step to claim the use of cognitive space of conflict. Yet, the presence of an organized (unidimensional; Fig. 6) and continuous cognitive space should be further tested and backed up.

We thank the reviewer for recognizing the methods and results of our current work. Indeed, the utilization of a parametric design and RSA to examine organization of neural representations is a widely embraced methodology in the field of cognitive neuroscience (e.g., Freund et al., 2021; Ritz et al., 2022). Our current study aimed primarily to provide original evidence for whether similar conflicts are represented similarly in the brain, which reflects the geometry of conflict representations (i.e., the structure of differences between conflict representations). We have used multiple criteria to back up the findings by showing the representation is sensitive to the presence of conflict and has behavioral relevance.

We agree that the cognitive space account of cognitive control requires further validation. Therefore, in the revised manuscript, we have added several additional tests to strengthen the evidence supporting the organized cognitive space representation. Firstly, we tested five alternative models (Domain-General, Domain Specific, Stroop-Only, Simon-Only and Stroop+Simon models), and found that the Cognitive-Space model best fitted our data. Secondly, we explicitly calculated the dimensionality of the representation and observed a low dimensionality (1.19D). We have added these results to the “Multivariate patterns of the right dlPFC encodes the conflict similarity” section in the revised manuscript (see also the response to Comment 1).

Furthermore, we utilized data from Experiment 1 to demonstrate the continuity of the cognitive space by showing its ability to predict out-of-sample data. We have included this result to the “Conflict type similarity modulated behavioral congruency sequence effect (CSE)” section in the revised manuscript:

“Moreover, to test the continuity and generalizability of the similarity modulation, we conducted a leave-one-out prediction analysis. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001.”

References:

Freund, M. C., Bugg, J. M., & Braver, T. S. (2021). A Representational Similarity Analysis of Cognitive Control during Color-Word Stroop. Journal of Neuroscience, 41(35), 7388-7402.

Ritz, H., & Shenhav, A. (2022). Humans reconfigure target and distractor processing to address distinct task demands. bioRxiv. doi:10.1101/2021.09.08.459546

4) Is the conflict similarity effect not driven by either coding of the weak to strong gradient of the spatial Stroop conflict or the Simon conflict? For example, would simply identifying brain regions that selectively tuned to the Simon conflict continuously enough to create a graded similarity in Fig. C.

We recognize that our current design and analyzing approach cannot fully exclude the possibility that the current results are driven solely by either Stroop or Simon conflicts, since their gradients are correlated to the conflict similarity gradient we defined. To estimate their unique contributions, we performed a model-comparison analysis. We constructed a Stroop-Only model and a Simon-Only model, with each conflict type projected onto the Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, P., 1901), that is, their intersection divided by their union. By replacing the cognitive space-based conflict similarity regressor with the Stroop-Only and Simon-Only regressors, we calculated their BICs. Results showed that the BIC was larger for Stroop-Only (5377122) and Simon-Only (5377096) than for the cognitive space model (5377094). An additional Stroop+Simon model, including both Stroop-Only and Simon-Only regressors, also 1220 showed a poorer model fitting (BIC = 5377118) than the cognitive space model.

Moreover, we replicated the results with only incongruent trials. We found a poorer fitting in Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. Therefore, we believe the cognitive space has incorporated both dimensions. We added these additional analyses and results to the revised manuscript (see also the response to the above Comment 1).

5) Is encoding of conflict similarity in the unidimensional organized space driven by specific requirements of the task or is this a general control strategy? Specifically, is the recruitment of organized space something specific to the task that people are trained to work with stimuli that negatively correlate the spatial Stroop conflict and the Simon conflict?

We argue that this encoding is a general control strategy. In our task design, we asked the participants to respond to the target arrow and ignore the location that appeared randomly for them. So, they were not trained to deal with the stimuli in any certain way. We also found the conflict similarity modulation on CSE did not change with more training (We added this result in Note S3), indicating that the cognitive space did not depend on strategies that could be learned through training.

“Note S3. Modulation of conflict similarity on behavioral CSEs does not change across time We tested if the conflict similarity modulation on the CSE is susceptible to training. We collected the data of Experiment 1 across three sessions, thus it is possible to examine if the conflict similarity modulation effect changes across time. To this end, we added conflict similarity, session and their interaction into a mixed-effect linear model, in which the session was set as a categorical variable. With a post-hoc analysis of variance (ANOVA), we calculated the statistical significance of the interaction term.

This approach was applied to both the RT and ER. Results showed no interaction effect in either RT, F(2,1479) = 1.025, p = .359, or ER, F(2,1479) = 0.789, p = .455. This result suggests that the modulation effect does not change across time."

Instead, the cognitive space should be determined by the intrinsic similarity structure of the task design. A previous study (Freitas et al., 2015) has found that the CSE across different versions of spatial Stroop and flanker tasks was stronger than that across either of the two conflicts and Simon. In their designs, the stimulus similarity was controlled at the same level, so the difference in CSE was only attributable to the similar dimensional overlap between Stroop and flanker tasks, in contrast to the Simon task. Furthermore, recent studies showed that the cognitive space generally exists to represent structured latent states (e.g., Vaidya et al., 2022), mental strategy cost (Grahek et al., 2022), and social hierarchies (Park et al., 2020). Therefore, we argue that cognitive space is likely a universal strategy that can be applied to different scenarios.

We added this argument in the discussion:

“Although the spatial orientation information in our design could be helpful to the construction of cognitive space, the cognitive space itself was independent of the stimulus-level representation of the task. We found the conflict similarity modulation on CSE did not change with more training (see Note S3), indicating that the cognitive space did not depend on strategies that could be learned through training. Instead, the cognitive space should be determined by the intrinsic similarity structure of the task design. For example, a previous study (Freitas et al, 2015) has found that the CSE across different versions of spatial Stroop and flanker tasks was stronger than that across either of the two conflicts and Simon. In their designs, the stimulus similarity was controlled at the same level, so the difference in CSE was only attributable to the similar dimensional overlap between Stroop and flanker tasks, in contrast to the Simon task. Furthermore, recent studies showed that the cognitive space generally exists to represent structured latent states (e.g., Vaidya et al., 2022), mental strategy cost (Grahek et al., 2022), and social hierarchies (Park et al., 2020). Therefore, cognitive space is likely a universal strategy that can be applied to different scenarios."

Reference:

Freitas, A. L., & Clark, S. L. (2015). Generality and specificity in cognitive control: conflict adaptation within and across selective-attention tasks but not across selective-attention and Simon tasks. Psychological Research, 79(1), 143-162.

Vaidya, A. R., Jones, H. M., Castillo, J., & Badre, D. (2021). Neural representation of 1280 abstract task structure during generalization. Elife, 10, 1-26.

Grahek, I., Leng, X., Fahey, M. P., Yee, D., & Shenhav, A. Empirical and 1282 Computational Evidence for Reconfiguration Costs During Within-Task 1283 Adjustments in Cognitive Control. CogSci.

Park, S. A., Miller, D. S., Nili, H., Ranganath, C., & Boorman, E. D. (2020). Map 1285 Making: Constructing, Combining, and Inferring on Abstract Cognitive Maps. 1286 Neuron, 107(6), 1226-1238 e1228. doi:10.1016/j.neuron.2020.06.030

6) The observed pattern seems to suggest that there is conflict similarity space that is defined by the combination of the conflict similarity (i.e., the strength of conflicts) and the sources of conflict (i.e., the Simon vs the spatial Stroop). What are the rational reasons to separate conflicts of different sources (beyond detecting incongruence)? And how are they used for better conflict resolutions?

The necessity of separating conflicts of different sources lies in that the spatial Stroop and the Simon effects are resolved with different mechanisms. The behavioral congruency effects of a combined conflict from two different sources were shown to be the summation of the two conflict sources (Liu et al., 2010), suggesting that the conflicts are resolved independently. Moreover, previous studies have shown that different sources of conflict are resolved with different brain regions (Egner, 2008; Li et al., 2017), and at different processing stages (Wang et al., 2013). Therefore, when multiple sources of conflict occur simultaneously or sequentially, it should be more efficient to resolve the conflict by identifying the sources.

We have added this argument to the revised manuscript:

“The rationale behind defining conflict similarity based on combinations of different conflict sources, such as spatial-Stroop and Simon, stems from the evidence that these sources undergo independent processing (Egner, 2008; Li et al., 2014; Liu et al., 2010; Wang et al., 2014). Identifying these distinct sources is critical in efficiently resolving potentially infinite conflicts."

Reference:

Egner, T. (2008). Multiple conflict-driven control mechanisms in the human brain. Trends in Cognitive Sciences, 12(10), 374-380.

Li, Q., Yang, G., Li, Z., Qi, Y., Cole, M. W., & Liu, X. (2017). Conflict detection and 1307 resolution rely on a combination of common and distinct cognitive control networks. Neuroscience and Biobehavioral Reviews, 83, 123-131.

Wang, K., Li, Q., Zheng, Y., Wang, H., & Liu, X. (2014). Temporal and spectral 1310 profiles of stimulus-stimulus and stimulus-response conflict processing. NeuroImage, 89, 280-288.

Liu, X., Park, Y., Gu, X., & Fan, J. (2010). Dimensional overlap accounts for independence and integration of stimulus-response compatibility effects. Attention, Perception, & Psychophysics, 72(6), 1710-1720.

7) The congruency effect is larger in conflict type 2, 3, 4 consistently compared to conflict 1 and 5. Are these expected under the hypothesis of unified cognitive space of conflict similarity? Is the pattern of similarity modeled in RSA?

Yes, this is expected. The spatial Stroop and Simon effects have been shown to be additive and independent (Li et al., 2014). Therefore, the congruency effects of conflict type 2, 3 and 4 would be the weighted sum of the spatial Stroop and Simon effects. The weights can be defined by the sine and cosine of the polar angle.

For instance, in Type 2, wy = sin(67.5°) and wx = cos(67.5°). The sum of the two 1321 weight values (i.e., 1.31) is larger than 1, leading to a larger congruency effect than 1322 the pure spatial Stroop (Conf 1) and Simon (Conf 5) conditions.

Note that this hypothesis underlies the Stroop+Simon model, which assumes the Stroop and Simon dimensions are independently represented in the brain and drive the behavior in an additive fashion. Moreover, the observed difference of behavioral congruency effects may have reflected the variance in the Domain-General model, which treats all conflict types as equivalent, with the only difference between each two conflict types in the magnitude of their conflict. Therefore, we did not model the behavioral congruency effects as a covariance regressor in the major RSA. Instead, we conducted a model comparison analysis by comparing these models and the Cognitive-Space model. Results showed worse model fitting of both the Domain-general and Stroop+Simon models. Specially, the regressor of congruency effect difference in the Domain-General model was not significant (p = .575), which also suggests that the higher congruency effect in conflict type 2, 3 and 4 should not influence the Cognitive-Space model results. We have added these methods and results to the revised manuscript (see also our response to Comment 1):

Methods:

“Model comparison and representational dimensionality

To estimate if the right 8C specifically encodes the cognitive space, rather than the domain-general or domain-specific structures, we conducted two more RSAs. We replaced the cognitive space-based conflict similarity matrix in the RSA we reported above (hereafter referred to as the Cognitive-Space model) with one of the alternative model matrices, with all other regressors equal. The domain-general model treats each conflict type as equivalent, so each two conflict types only differ in the magnitude of their conflict. Therefore, we defined the domain-general matrix as the difference in their congruency effects indexed by the group-averaged RT in Experiment 2. Then the z scored model vector was sign-flipped to reflect similarity instead of distance. The domain-specific model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all cross-conflict type similarities being 0.

Moreover, to examine if the cognitive space is driven solely by the Stroop or Simon conflicts, we tested a spatial Stroop-Only (hereafter referred to as “Stroop-Only”) and a Simon-Only model, with each conflict type projected onto the spatial Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, 1901), that is, their intersection divided by their union. We also included a model assuming the Stroop and Simon dimensions are independently represented in the brain, adding up the Stroop Only and Simon-Only regressors. We conducted similar RSAs as reported above, replacing the original conflict similarity regressor with the Strrop-Only, Simon-Only, or both regressors, and then calculated their Bayesian information criterions (BICs)."

Reference:

Li, Q., Nan, W., Wang, K., & Liu, X. (2014). Independent processing of stimulus stimulus and stimulus-response conflicts. PloS One, 9(2), e89249.

8) Please clarify the observed patterns of CSE effects in relation to the hypothesis of common cognitive space of conflict. In particular, right 8C shows that the patterns become dissimilar in incongruent trials compared to congruent trials. How does this direction of the effect fit to the common unidimensional cognitive space account? And how does such a representation contribute to the CES effects?

The behavioral CSE patterns provide initial evidence for the cognitive space hypothesis. Previous studies have debated whether cognitive control relies on domain-general or domain-specific representations, with much evidence gathered from behavioral CSE patterns. A significant CSE across two conflict conditions typically suggests domain-general representations of cognitive control, while an absence of CSE suggests domain-specific representations. The cognitive space view proposes that conflict representations are neither purely domain-general nor purely domain-specific, but rather exist on a continuum. This view predicts that the CSE across two conflict conditions should depend on the representational distance between them within this cognitive space. Our finding that CSE values systematically vary with conflict similarity level support this hypothesis. We have added this point in the discussion of the revised manuscript:

“Previous research on this topic often adopts a binary manipulation of conflict(Braem et al., 2014) (i.e., each domain only has one conflict type) and gathered evidence for the domain-general/specific view with presence/absence of CSE, respectively. Here, we parametrically manipulated the similarity of conflict types and found the CSE systematically vary with conflict similarity level, demonstrating that cognitive control is neither purely domain-general nor purely domain-specific, but can be reconciled as a cognitive space(Bellmund et al., 2018) (Fig. 6, middle).

Fig. 4D was plotted to show the steeper slope of the conflict similarity effect for incongruent versus congruent conditions. Note the y-aixs displays z-scored Pearson correlation values, so the grand mean of each condition was 0. The values for the first two similarity levels (level 1 and 2) were lower for incongruent than congruent conditions, seemingly indicating lower average similarity. However, this was not the case. The five similarity levels contained different numbers of data points (see Fig. 1C), so levels 4 and 5 should be weighted more heavily than levels 1 and 2. When comparing the grand mean of raw Pearson correlation values, the incongruent condition (0.0053) showed a tendency toward higher similarity than the congruent condition (0.0040), t(475998) = 1.41, p = .079. We have also plotted another version of Fig. 4D in Fig. S5, in which the raw Pearson correlation values were used.

The greater representation of conflict type in incongruent condition compared to congruent condition (as evidenced by a steeper slope) suggests that the conflict representation was driven by the incongruent condition. This is probably due to the stronger involvement of cognitive control in incongruent condition (than congruent condition), which in turn leads to more distinct patterns across different conflict types. This is consistent with the fact that the congruent condition is typically a baseline, where any conflict related effects should be weaker.

The representation of cognitive space may contribute to the CSE as a mental model. This model allows our brain to evaluate the cost and benefit associated with transitioning between different conflict conditions. When two consecutive trials are characterized by more similar conflict types, their representations in the cognitive space will be closer, resulting in a less costly transition. As a consequence, stronger CSEs are observed. We revised the corresponding discussion part as:

“Similarly, we propose that cognitive space could serve as a mental model to assist fast learning and efficient organization of cognitive control settings. Specifically, the cognitive space representation may provide a principle for how our brain evaluates the expected cost of switching and the benefit of generalization between states and selects the path with the best cost-benefit tradeoff (Abrahamse et al., 2016; Shenhav et al., 2013). The proximity between two states in cognitive space could reflect both the expected cognitive demand required to transition and the useful mechanisms to adapt from. The closer the two conditions are in cognitive space, the lower the expected switching cost and the higher the generalizability when transitioning between them. With the organization of a cognitive space, a new conflict can be quickly assigned a location in the cognitive space, which will facilitate the development of cognitive control settings for this conflict by interpolating nearby conflicts and/or projecting the location to axes representing different cognitive control processes, thus leading to a stronger CSE when following a more similar conflict condition.”

Minor comments:

9) Some of the labels of figure axes are unclear (e.g., Fig4C) about what they represent.

In Fig. 4C, the x-axis label is “neural representational strength”, which refers to the beta coefficient of the conflict type effect computed from the main RSA, denoting the strength of the conflict type representation in neural patterns. The y-axis label is “behavioral representational strength”, which refers to the beta coefficient obtained from the behavioral linear model using conflict similarity to predict the CSE in Experiment 2; it reflects how strong the conflict similarity modulates the behavioral 1440 CSE. We apologize for any confusion from the brief axis labels. We have added expanded descriptions to the figure caption of Fig. 4C.

Author Response

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

eLife assessment

This manuscript analyzes large-scale Neuropixels recordings from visual areas and hippocampus of mice passively viewing repeated clips of a movie and reports that neurons respond with elevated firing activities to specific, continuous sequences of movie frames. The important results support a role of rodent hippocampal neurons in general episode encoding and advance understanding of visual information processing across different brain regions. The strength of evidence for the primary conclusion is solid, but some technical limitations of the study were identified that merit further analyses.

We thank the editors and reviews for the assessment and reviews. We have provided clarifications and updated the manuscripts to address the seeming technical limitations that are perhaps due to some misunderstanding, please see below. We provide additional results that isolate the contribution of pupil diameter, sharpwave ripple and theta power to show that movie tuning cannot be explained by these nonspecific effects. Nor are these mere time cells or some other internally generated patterns due to many differences highlighted below.

Reviewer #1 (Public Review):

Taking advantage of a publicly available dataset, neuronal responses in both the visual and hippocampal areas to passive presentation of a movie are analyzed in this manuscript. Since the visual responses have been described in a number of previous studies (e.g., see Refs. 11-13), the value of this manuscript lies mostly on the hippocampal responses, especially in the context of how hippocampal neurons encode episodic memories. Previous human studies show that hippocampal neurons display selective responses to short (5 s) video clips (e.g. see Gelbard-Sagiv et al, Science 322: 96-101, 2008). The hippocampal responses in head-fixed mice to a longer (30 s) movie as studied in this manuscript could potentially offer important evidence that the rodent hippocampus encodes visual episodes.

We have now included citations to Gelbard-Sagiv et al. Science 2008 paper and many other references too, thank you for pointing that out. There are major differences between that study and ours.

a. The movies used in previous study contained very familiar, famous people and famous events, and the experiment was about the patient’s ability to recall those famous movie episodes. In our case the mice had seen this movie clip only in two habituation sessions before.

b. They did not look at the fine structure of neural responses below half a second whereas we looked at the mega-scale representations from 30ms to 30s.

c. The movie clips in that study were in full color with audio, we used an isoluminant, black-and-white, silent movie clip.

d. Their movie clips contained humans and was observed by humans, whereas our study mice observed a movie clip with humans and no mice or other animals.

The analysis strategy is mostly well designed and executed. A number of factors and controls, including baseline firing, locomotion, frame-to-frame visual content variation, are carefully considered. The inclusion of neuronal responses to scrambled movie frames in the analysis is a powerful method to reveal the modulation of a key element in episodic events, temporal continuity, on the hippocampal activity. The properties of movie fields are comprehensively characterized in the manuscript.

Thank you.

Although the hippocampal movie fields appear to be weaker than the visual ones (Fig. 2g, Ext. Fig. 6b), the existence of consistent hippocampal responses to movie frames is supported by the data shown. Interestingly, in my opinion, a strong piece of evidence for this is a "negative" result presented in Ext. Fig. 13c, which shows higher than chance-level correlations in hippocampal responses to same scrambled frames between even and odd trials (and higher than correlations with neighboring scrambled frames). The conclusion that hippocampal movie fields depend on continuous movie frames, rather than a pure visual response to visual contents in individual frames, is supported to some degree by their changed properties after the frame scrambling (Fig. 4).

Yes, hippocampal selectivity is not entirely abolished with scrambled movie, as we show in several figures (Figure 4d,g and Figure 4- figure supplement 6), but it is greatly reduced, far more than that in the afferent visual cortices. The fraction of tuned cells for scrambled movies dropped to 4.5% in hippocampus, which is close to the chance level of 3%. In contrast, in visual areas selectivity was still above 80%.

Significant overlap between even and odd trials is to be expected for the tuned cells. Without a significant overlap, i.e. a stable representation, they will not be tuned. Despite this, the correlation between even and odd trials for the (only 4.5% of) tuned cells in the hippocampus was more than 2-fold smaller than (more than 80% of) cells in visual cortices. This strongly supports our hypothesis that unlike visual cortices, hippocampal subfields depended very strongly on the continuity of visual information. We have now clarified this in the main text.

However, there are two potential issues that could complicate this main conclusion.

One issue is related to the effect of behavioral variation or brain state. First, although the authors show that the movie fields are still present during low-speed stationary periods, there is a large drop in the movie tuning score (Z), especially in the hippocampal areas, as shown in Ext. Fig. 3b (compared to Ext. Fig. 2d). This result suggests a potentially significant enhancement by active behavior.

There seems to be some misunderstanding here. There was no major reduction in movie tuning during immobility or active running. As we wrote in the manuscript, the drop in selectivity during purely immobile epochs is because of reduction in the amount of data, not reduction in selectivity per se. Specifically, as the amount data reduces, the statistical strength of tuning (z-scored sparsity) reduces. For example, if we split the total of 60 trials worth of data into two parts, the amount of data reduces to about half in each part, leading to a seeming reduction in selectivity in both halves. Figure 1-figure supplement 4c shows nearly identical tuning in all brain regions during immobility (red bars) and equivalent subsamples (yellow-orange) chosen randomly from the entire data, including mobility and immobility. We also show that the movie tuning persists in sessions with and without prolonged running behavior (Figure 1-figure supplement 7), as well as by splitting the data based on pupil dilation or theta power. Please see below for more details.

Second, a general, hard-to-tackle concern is that neuronal responses could be greatly affected by changes in arousal or brain state (including drowsy or occasional brief slow-wave sleep state) in head-fixed animals without a task. Without the analysis of pupil size or local field potentials (LFPs), the arousal states during the experiment are difficult to know.

In the revised manuscript we show that the behavioral state effects cannot explain movie tuning. Specifically:

a. We compared sessions in which the mouse was mostly immobile versus sessions in which the mouse was mostly running. Movie tuned cells were found in both these cases (Figure 1-figure supplement 7).

b. We detected and removed all data around sharp-wave ripples (SWR). Movie tuning was unchanged in the remaining data. (Figure 1-figure supplement 6).

c. As a further control, we quantified arousal by two standard metrics. First within a session, we split the data into two groups, segments with high theta power and segments with low theta power. Significant movie tuning persisted in both.

d. Finally, pupil dilation is another common method to estimate arousal, so data within a session were split into two parts: those with pupil dilation versus constriction. Movie tuning remained significant in both parts. See the new Figure 1-figure supplement 7.

Many example movie fields in the presented raw data (e.g., Fig. 1c, Ext. Fig. 4) are broad with low-quality tuning, which could be due to broad changes in brain states. This concern is especially important for hippocampal responses, since the hippocampus can enter an offline mode indicated by the occurrence of LFP sharp-wave ripples (SWRs) while animals simply stay immobile. It is believed that the ripple-associated hippocampal activity is driven mainly by internal processing, not a direct response to external input (e.g., Foster and Wilson, Nature 440: 680, 2006). The "actual" hippocampal movie fields during a true active hippocampal network state, after the removal of SWR time periods, could have different quantifications that impact the main conclusion in the manuscript.

We included the broadly tuned hippocampal neurons to demonstrate the movie-field broadening compared to those in visual areas. We now include more examples with sharp movie fields in the hippocampal regions (Figure 1a-d right column, 2d and h, Figure 1-figure supplement 5 and Figure 2-figure supplement 1). Further, as stated above, we detected sharp-wave ripples and removed one second of data around SWR. Movie tuning was unchanged in the remaining data. Thus, movie tuning is not generated internally via SWR (Figure 1-figure supplement 6). See also Figure 1-figure supplement 7 and Figure 2-figure supplement 8 and the response above.

Another issue is related to the relative contribution of direct visual response versus the response to temporal continuity in movie fields. First, the data in Ext. Fig. 8 show that rapid frame-to-frame changes in visual contents contribute largely to hippocampal movie fields (similarly to visual movie fields).

There seems to be some misunderstanding here. That figure showed that the frame-to-frame changes in the visual content had the highest effect on visual areas MSUA and much weaker in hippocampus (Extended Data Fig. 8, as per previous version, now Figure3-figure supplement 2). For example, the depth of modulation (max – min) / (max + min) for MSUA was 21% and 24% for V1 but below 6% for hippocampal regions. Similarly, the MSUA was more strongly (negatively) correlated with F2F correlation for visual areas (r=0.48 to 0.56) than hippocampal (0.07 to 0.3). Similarly, comparing the number of peaks or their median widths, visual regions showed stronger correlation with F2F, and largest depth of modulation than hippocampal regions, barring handful exceptions (like CA3 correlation between F2F and median peak duration). This strongly supports our claim that visual regions generated far greater response of the frame-to-frame changes in the movie than hippocampal regions.

Interestingly, the data show that movie-field responses are correlated across all brain areas including the hippocampal ones.

In Figure 3c we compared the MSUA responses with normalization between brain regions. Amongst the 21 possible brain region pairs, 5 were uncorrelated, 7 were significantly negatively correlated and 9 were significantly positively correlated.

The changes in population overlap, number and widths of peaks are strongly correlated only between visual areas and some of the hippocampal region pairs. The correlation is much weaker for hippocampal-visual area pairs, but often significantly different from chance. This is quantified explicitly in the revised text Figure 3-figure supplement 2 with an additional correlation matrix at the right.

This could be due to heightened behavioral arousal caused by the changing frames as mentioned above, or due to enhanced neuronal responses to visual transients, which supports a component of direct visual response in hippocampal movie fields.

As shown in Figure 1-figure supplements 4,5,6 and 7 and described above, the effect of arousal as quantified by theta power of pupil diameter (or by accounting for running behavior or SWR occurrences) cannot explain the results in hippocampal areas and the correlations in multiunit responses are unrelated across many brain areas.

Second, the data in Ext. Fig. 13c show a significant correlation in hippocampal responses to same scrambled frames between even and odd trials, which also suggests a significant component of direct visual response.

This is plausible. The fraction of hippocampal cells which were significantly tuned for the scrambled presentation (4.5%) was close to chance level (3%), and this small subset of cells was used to compute the population overlap between even and odd trials in Figure 4-figure supplement 6 (Ext Fig. 13 with old numbering). As described above, this significant but small amount of tuning could generate significant population overlap, which is to be expected by construction.

Is there a significant component purely due to the temporal continuity of movie frames in hippocampal movie fields? To support that this is indeed the case, the authors have presented data that hippocampal movie fields largely disappear after movie frames are scrambled. However, this could be caused by the movie-field detection method (it is unclear whether single-frame field could be detected).

As described in the methods section, the movie-field detection algorithm had a resolution of 3.3ms resolution, which ensured that we could detect single frame fields. As reported, we did find such short movie fields in several cells in the visual areas. The sparsity metric used is agnostic to the ordering of the responses, and hence single frame field, and the resultant significant movie-tuning, if present, can be detected by our methods.

Another concern in the analysis is that movie-fields are not analyzed on re-arranged neural responses to scrambled movie frames. The raw data in Fig. 4e seem quite convincing. Unfortunately, the quantifications of movie fields in this case are not compared to those with the original movie.

We saw very few (3.6-4.9%) cells with significant movie tuning for scrambled presentation in the hippocampus. Hence, we did not quantify this earlier. This is now provided in new Figure 4-figure supplement 5. The amount of movie tuning for the scrambled presentation taken as-is, or after rearranging the frames is below 5% for all hippocampal brain regions and not significantly different between the two.

Reviewer #2 (Public Review):

Purandare and Mehta investigated the neural activities modulated by continuous and sequential visual stimuli composed of natural images, termed "movie-tuning," measured along the visuo-hippocampal network when the animals passively viewed a movie without any task demand. Neurons selectively responded to some specific parts of the movie, and their activity timescales ranged from tens of milliseconds to seconds and tiled the entire movie with their movie-fields. The movie-tuning was lost in the hippocampus but not in the visual cortices when the image frames were temporally scrambled, implying that the rodent hippocampus encoded the specific sequence of images.

The authors have concluded that the neurons in the thalamo-cortical visual areas and the hippocampus commonly encode continuous visual stimuli with their firing fields spanning the mega-scale, but they respond to different aspects of the visual stimuli (i.e., visual contents of the image versus a sequence of the images). The conclusion of the study is fairly supported by the data, but some remaining concerns should be addressed.

1) Care should be taken in interpreting the results since the animal's behavior was not controlled during the physiological recording.

This was done intentionally since plenty of research shows that task demand (e.g., Aronov and Tank, Nature 2017) can not only modulate hippocampal responses but also dramatically alter them. We have now provided additional figures (Figure 1-figure supplement 6 and 7) where we quantified the effects of the behavioral states (sharp wave ripples, theta power and pupil diameter), as well as the effect of locomotion (Figure 1-figure supplement 4). Movie tuning remained unaffected with these manipulations. Thus, movie tuning cannot be attributed to behavioral effects.

It has been reported that some hippocampal neuronal activities are modulated by locomotion, which may still contribute to some of the results in the current study. Although the authors claimed that the animal's locomotion did not influence the movie-tuning by showing the unaltered proportion of movie-tuned cells with stationary epochs only, the effects of locomotion should be tested in a more specific way (e.g., comparing changes in the strength of movie-tuning under certain locomotion conditions at the single-cell level).

Single cell analysis of the effect of locomotion and visual stimulation is underway, and beyond the scope of the current work. As detailed in Figure 1-figure supplement 4, we have ensured that in spite of the removal of running or stationary epochs, as well as removal of sharp wave ripple events (Figure 1-figure supplement 6) movie tuning persists. Further, we now provide examples of strongly tuned cells from sessions with predominantly running or predominantly stationary behavior (Figure 1-figure supplement 7).

2) The mega-scale spanning of movie-fields needs to be further examined with a more controlled stimulus for reasonable comparison with the traditional place fields. This is because the movie used in the current study consists of a fast-changing first half and a slow-changing second half, and such varying and ununified composition of the movie might have largely affected the formation of movie-fields. According to Fig. 3, the mega-scale spanning appears to be driven by the changes in frame-to-frame correlation within the movie. That is, visual stimuli changing quickly induced several short fields while persisting stimuli with fewer changes elongated the fields.

Please note that a strong correlation between the speed at which the movie scene changed across frames was correlated with movie-field width in the visual areas, but that correlation was much weaker in the hippocampal areas (correlation values - (LGN +0.61, V1 +0.51, AM-PM +0.55 vs. DG +0.39, CA3 +0.58, CA1 +0.42, SUB +0.24). Please see Figure 3-figure supplement 2 and the quantification of correlation between frame-to-frame changes in the movie and the properties of movie fields.

The presentation of persisting visual input for a long time is thought to be similar to staying in one place for a long time, and the hippocampal activities have been reported to manifest in different ways between running and standing still (i.e., theta-modulated vs. sharp wave ripple-based). Therefore, it should be further examined whether the broad movie-fields are broadly tuned to the continuous visual inputs or caused by other brain states.

As shown in Figure 1-figure supplement 6, movie field properties are largely unchanged when SWR are removed from the data, or when the effect of pupil diameter or theta power were factored for (Figure 1-figure supplement 7).

3) The population activities of the hippocampal movie-tuned cells in Fig. 3a-b look like those of time cells, tiling the movie playback period. It needs to be clarified whether the hippocampal cells are actively coding the visual inputs or just filling the duration.

Tiling patterns would be observed when the maxima are sorted in any data, even for random numbers. This alone does not make them time cells. The following observations suggest that movie fields cannot be explained as being time cells.

a. Time cells mostly cluster at the beginning of a running epoch (Pastalkova et al. Science 2008, MacDonald et al. Neuron 2011) and they taper off towards the end. Such large clustering is not visible in these tiling plots for movie tuned cells.

b. Time fields become wider as the temporal duration progresses (Pastalkova et al. Science 2008, MacDonald et al. Neuron 2011) as the encoded temporal duration increases. This is not evident in any movie fields.

c. Widths of movie fields in visual areas, and to a smaller extent in the hippocampal areas, were clearly modulated by the visual content, like the change from one frame to the next (F2F correlation, Figure 3-figure supplement 2).

d. Tiling pattern of movie fields was found in visual areas too, with qualitatively similar pattern as hippocampus. Clearly, visual area responses are not time cells, as shown by the scrambled stimulus experiment. Here, neural selectivity could be recovered by rearranging them based on the visual content of the continuous movie, and not the passage of time.

The scrambled condition in which the sequence of the images was randomly permutated made the hippocampal neurons totally lose their selective responses, failing to reconstruct the neural responses to the original sequence by rearrangement of the scrambled sequence. This result indirectly addressed that the substantial portion of the hippocampal cells did not just fill the duration but represented the contents and temporal order of the images. However, it should be directly confirmed whether the tiling pattern disappeared with the population activities in the scrambled condition (as shown in Extended Data Fig. 11, but data were not shown for the hippocampus).

As stated above for the continuous movie, tiling pattern alone does not mean those are time cells. Further, tuning, and tiling pattern remained intact with scrambled movie in the visual cortices but not in hippocampus. We now added a new supplement figure – Figure 4-figure supplement 5 where we compared the movie tuning for scrambled presentation with and without rearranging the frames. Hippocampal tuning remains at chance levels.

Reviewer #3 (Public Review):

In their study, Purandare & Mehta analyze large-scale single unit recordings from the visual system (LGN, V1, extrastriate regions AM and PM) and hippocampal system (DG, CA3, CA1 and subiculum) while mice monocularly viewed repeats of a 30s movie clip. The data were part of a larger release of publicly available recordings from the Allen Brian Observatory. The authors found that cells in all regions exhibited tuning to specific segments of the movie (i.e. "movie fields") ranging in duration from 20ms to 20s. The largest fractions of movie-responsive cells were in visual regions, though analyses of scrambled movie frames indicated that visual neurons were driven more strongly by visual features of the movie images themselves. Cells in the hippocampal system, on the other hand, tended to exhibit fewer "movie fields", which on average were a few seconds in duration, but could range from >50ms to as long as 20s. Unlike the visual system "movie fields" in the hippocampal system disappeared when the frames of the movie were scrambled, indicating that the cells encoded more complex (episodic) content, rather than merely passively reading out visual input.

The paper is conceptually novel since it specifically aims to remove any behavioral or task engagement whatsoever in the head-fixed mice, a setup typically used as an open-loop control condition in virtual reality-based navigational or decision making tasks (e.g. Harvey et al., 2012). Because the study specifically addresses this aspect of encoding (i.e. exploring effects of pure visual content rather than something task-related), and because of the widespread use of video-based virtual reality paradigms in different sub-fields, the paper should be of interest to those studying visual processing as well as those studying visual and spatial coding in the hippocampal system. However, the task-free approach of the experiments (including closely controlling for movement-related effects) presents a Catch-22, since there is no way that the animal subjects can report actually recognizing or remembering any of the visual content we are to believe they do.

Our claim is that these are movie scene evoked responses. We make no claims about the animal’s ability to recognize or remember the movie content. That would require entirely different set of experiments. Meanwhile, we have shown that these results are not an artifact of brain states such as sharp wave ripples, theta power or pupil diameter (Figure1-figure supplement 6 and 7) or running behavior (Figure 1-figure supplement 4). Please see above for a detailed response.

We must rely on above-chance-level decoding of movie segments, and the requirement that the movie is played in order rather than scrambled, to indicate that the hippocampal system encodes episodic content of the movie. So the study represents an interesting conceptual advance, and the analyses appear solid and support the conclusion, but there are methodological limitations.

It is important to emphasize that these responses could constitute episodic responses but does not prove episodic memory, just as place cell responses constitute spatial responses but that does not prove spatial memory. The link between place cells and place memory is not entirely clear. For example, mice lacking NMDA receptors have intact place cells, but are impaired in spatial memory task (McHugh et al. Cell 1996), whereas spatial tuning was virtually destroyed in mice lacking GluR1 receptors, but they could still do various spatial memory tasks (Resnik et al. J. Neuro 2012).

The experiments about episodic memory would require an entirely different set of experiments that involve task demand and behavioral response, which in turn would modify hippocampal responses substantially, as shown by many studies. Our hypothesis here, is that just like place cells, these episodic responses without task demand would play a role, to be determined, in episodic memory. We have emphasized this point in the main text (Ln 391-393 in the revised manuscript).

Major concerns:

1) A lot hinges on hinges on the cells having a z-scored sparsity >2, the cutoff for a cell to be counted as significantly modulated by the movie. What is the justification of this criterion?

The z-scored sparsity (z>2) corresponds to p<0.03. This would mean that 3% of the results could appear by chance. Hence, z>2 is a standard method used in many publications. Another advantage of z-scored sparsity is that it is relatively insensitive to the number of spikes generated by a neuron (i.e. the mean firing rate of the neuron and the duration of the experiment). In contrast, sparsity is strongly dependent on the number of spikes which makes it difficult to compare across neurons, brain regions and conditions (See Supplement S5 Acharya et al. Cell 2016).

To further address this point, we compared our z-scored sparsity measure with 2 other commonly used metrics to quantify neural selectivity, depth of modulation and mutual information (Figure 1-figure supplement 3). Comparable movie tuning was obtained from all 3 metrics, upon z-scoring in an identical fashion.

It should be stated in the Results. Relatedly, it appears the formula used for calculating sparseness in the present study is not the same as that used to calculate lifetime sparseness in de Vries et al. 2020 quoted in the results (see the formula in the Methods of the de Vries 2020 paper immediately under the sentence: "Lifetime sparseness was computed using the definition in Vinje and Gallant").

The definition of sparsity we used is used commonly by most hippocampal scientists (Treves and Rolls 1991, Skaggs et al. 1996, Ravassard et al. 2013). Lifetime sparseness equation used by de Vries et al. 2020, differs from us by just one constant factor (1-1/N) where N=900 is the number of frames in the movie. This constant factor equals (1-1/900)=0.999. Hence, there is no difference between the sparsity obtained by these two methods. Further, z-scored sparsity is entirely unaffected by such constant factors. We have clarified this in the methods of the revised manuscript.

To rule out systematic differences between studies beyond differences in neural sampling (single units vs. calcium imaging), it would be nice to see whether calculating lifetime sparseness per de Vries et al. changed the fraction "movie" cells in the visual and hippocampal systems.

As stated above, the two definitions of sparsity are virtually identical and we obtained similar results using two other commonly used metrics, which are detailed in Figure 1-figure supplement 3.

2) In Figures 1, 2 and the supplementary figures-the sparseness scores should be reported along with the raw data for each cell, so the readers can be apprised of what types of firing selectivity are associated with which sparseness scores-as would be shown for metrics like gridness or Raleigh vector lengths for head direction cells. It would be helpful to include this wherever there are plots showing spike rasters arranged by frame number & the trial-averaged mean rate.

As shown in several papers (Aghajan et al Nature Neuroscience 2015, Acharya et al., Cell 2016) raw sparsity (or information content) are strongly dependent on the number of spikes of a neuron. This makes the raw values of these numbers impossible to compare across cells, brain regions and conditions. (Please see Supplement S5 from Acharya et al., Cell 2016 for details). Including the data of sparsity would thus cause undue confusion. Hence, we provide z-scored sparsity. This metric is comparable across cells and brain regions, and now provided above each example cell in Figure 1 and Figure 1-figure supplement 2.

3) The examples shown on the right in Figures 1b and c are not especially compelling examples of movie-specific tuning; it would be helpful in making the case for "movie" cells if cleaner / more robust cells are shown (like the examples on the left in 1b and c).

We did not put the most strongly tuned hippocampal neurons in the main figures so that these cells are representative of the ensemble and not the best possible ones, so as to include examples with broad tuning responses. We have clarified in the legend that these cells are some of the best tuned cells. Although not the cleanest looking, the z-scored sparsity mentioned above the panels now indicates how strongly they are modulated compared to chance levels. Additional examples, including those with sharply tuned responses are shown in Figure 1-figure supplement 5 and Figure 2-figure supplement 1.

4) The scrambled movie condition is an essential control which, along with the stability checks in Supplementary Figure 7, provide the most persuasive evidence that the movie fields reflect more than a passive readout of visual images on a screen. However, in reference to Figure 4c, can the authors offer an explanation as to why V1 is substantially less affected by the movie scrambling than it's main input (LGN) and the cortical areas immediately downstream of it? This seems to defy the interpretation that "movie coding" follows the visual processing hierarchy.

This is an important point, one that we find very surprising as well. Perhaps this is related to other surprising observations in our manuscript, such as more neurons appeared to be tuned to the movie than the classic stimuli. A direct comparison between movie responses versus fixed images is not possible at this point due to several additional differences such as the duration of image presentations and their temporal history.

The latency required to rearrange the scrambled responses (60ms for LGN, 74ms for V1, 91ms for AM/PM) supports the anatomical hierarchy. The pattern of movie tuning properties was also broadly consistent between V1 and AM/PM (Figure 2).

However, all metrics of movie selectivity (Figure 2) to the continuous movie showed a consistent pattern that was the exact opposite pattern of the simple anatomical hierarchy: V1 had stronger movie tuning, higher number of movie fields per cell, narrower movie-field widths, larger mega-scale structure, and better decoding than LGN. V1 was also more robust to the scrambled sequence than LGN. One possible explanation is that there are other sources of inputs to V1, beyond LGN, that contribute significantly to movie tuning. This is an important insight and we have modified the discussion (Ln 315-325) to highlight this.

Relatedly, the hippocampal data do not quite fit with visual hierarchical ordering either, with CA3 being less sensitive to scrambling than DG. Since the data (especially in V1) seem to defy hierarchical visual processing, why not drop that interpretation? It is not particularly convincing as is.

The anatomical organization is well established and an important factor. Even when observations do not fit the anatomical hierarchy, it provides important insights about the mechanisms. All properties of movie tuning (Figure 2) –the strength of tuning, number of movie peaks, their width and decoding accuracy firmly put visual areas upstream of hippocampal regions. But, just like visual cortex there are consistent patterns that do not support a simple feed-forward anatomical hierarchy. We have pointed out these patterns so that future work can build upon it.

5) In the Discussion, the authors argue that the mice encode episodic content from the movie clip as a human or monkey would. This is supported by the (crucial) data from the scrambled movie condition, but is nevertheless difficult to prove empirically since the animals cannot give a behavioral report of recognition and, without some kind of reinforcement, why should a segment from a movie mean anything to a head-fixed, passively viewing mouse?

We emphasize once again that our claim is about the nature of encoding of the movie across these neurons. We make no claims about whether this forms a memory or whether the mouse is able to recognize the content or remember it. Despite decades of research, similar claims are difficult to prove for place cells, with plenty of counter examples (See the points above). The important point here is that despite any cognitive component, we see remarkably tuned responses in these brain areas. Their role in cognition would take a lot more effort and is beyond the scope of the current work.

Would the authors also argue that hippocampal cells would exhibit "song" fields if segments of a radio song-equally arbitrary for a mouse-were presented repeatedly? (reminiscent of the study by Aronov et al. 2017, but if sound were presented outside the context of a task). How can one distinguish between mere sequence coding vs. encoding of episodically meaningful content? One or a few sentences on this should be added in the Discussion.

Aronov et al 2017, found the encoding of an audio sweep in hippocampus when the animals were doing a task (release the lever at a specific frequency to obtain a reward). However, without a task demand they found that hippocampal neurons did not encode the audio sequence beyond chance levels. This is at odds with our findings with the movie where we see strong tuning despite any task demand or reward. These results are consistent with but go far beyond our recent findings that hippocampal (CA1) neurons can encode the position and direction of motion of a revolving bar of light (Purandare et al. Nature 2022). Please see Ln 373-382 for related discussion.

These responses are unlikely to be mere sequence responses since the scrambled sequence was also fixed sequence that was presented many times and it elicited reliable responses in visual areas, but not in hippocampus. Hence, we hypothesize that hippocampal areas encode temporally related information, i.e. episodic content. We have modified the discussion to address these points.

Reviewer #1 (Recommendations For The Authors):

1) Are LFP data available in the data set? If so, can SWRs identified and removed to refine the quantification of movie fields?

Done, see Figure 1-figure supplement 6.

2) Can movie fields be analyzed in re-arranged neural responses (Fig. 4e) and compared to those in other cases already shown (Fig. 4b, c)?

Done, even after rearrangement the strength of movie tuning for the scrambled presentation was low, and below 5% in all hippocampal regions. See Figure 4-figure supplement 5 for details.

3) It seems the authors are not fully committed to a main conclusion in the present manuscript. The title and abstract seem to emphasize the similar movie responses across visual and hippocampal areas, but the introduction and discussion emphasize the episode encoding of hippocampal neurons. The writing could be more consistent and the main message could be clearer.

Selective responses to the continuous movie showed similar patterns (prevalence of tuning, multi-peaked nature, relation with frame to frame changes in visual images) between visual and hippocampal regions. But the visual responses to scrambled presentation could be rearranged, and the latency for rearrangement increased from LGN to V1 to AM-PM. On the other hand, selectivity to the scrambled presentation was virtually abolished in hippocampus, and responses could not be rearranged to resemble the continuous movie sequences. To reconcile these differences, we have hypothesized here that the hippocampal responses are episodic in nature, and rely on temporal continuity, whereas the visual regions rely directly on the visual content in the images.

4) Line #158: "Net movie-field discharges was also comparable across brain areas...". This statement is not supported by Fig. 2g, which shows a wide range of median values across brain areas.

Thank you for pointing this out. The normalized firing in movie-fields used in that figure are within 3x between V1 and subiculum. We have modified the text to contrast this with the 10x difference between movie-field durations.

5) Line #253: What the two numbers (87.8%, 10.6%) mean is unclear (mean or median values). These numbers also appear inconsistent with the mean+-se values in Fig. 4 legend.

The numbers mentioned on Ln253, in the main text reflect the median visual continuity index, combining across cells from hippocampal or visual regions. On the other hand, values reported in the Fig 4 legend are for V1 and subiculum, which are the regions with smallest and largest visual continuity index, respectively. We have re-written the main text, and legends for better clarity.

6) The Gelbard-Sagiv et al paper (Science 322: 96-101, 2008) could be cited and its relevance to the present study could be discussed.

Done

7) Are there neurons recorded from a non-visual sensory or motor cortical area in the same experiment? This may provide a key negative control for the non-specific modulation caused by behavioral states or visual transients.

Owing to the nature of the experiments where the Allen Institute intended to study visual processing, we could not find any of the recorded brain regions without movie selectivity.

8) The differences in hippocampal and visual move fields between active and stationary time periods could be explicitly quantified.

We have shown several raster plots where the responses are quite similar during immobile and moving epochs. Our goal is to show that there is indeed comparable movie tuning when the animals is immobile versus any random state. Doing specific analysis of behavioral dependency is difficult because in many sessions the amount of time the mice ran in many sessions was very little. A thorough analysis overcoming these, and other challenges is beyond the scope of this paper.

Reviewer #2 (Recommendations For The Authors):

1) The methods to determine the boundaries of the movie-fields should be clarified, and the detected peaks and boundaries should be indicated in the relevant figures (e.g., Fig. 2c, 2d, and 2h) to help readers clearly understand how the movie-fields were defined and how the shapes of the movie-fields look like.

Done.

2) When testing the influence of locomotion on movie-tuning in Extended Data Fig. 3, a single cell-based analysis is further needed. For example, you need to check whether the z-scored sparsity within one cell varies or not depending on locomotion conditions (as in Extended Data Fig. 10a-c). In addition, it is recommended to exclude the cells significantly modulated by locomotion (e.g., running velocity) before defining the movie-tuned cells.

We now show example cells from sessions with or without prolonged running bouts in Figure 1-figure supplement 7 that have strong movie selectivity. We have also assessed the effects of theta power and pupil dilation on movie tuning in that figure. A more thorough analysis of the combined effects of locomotion and movie tuning is underway, but beyond the scope of the current work.

3) Regarding the time-cell-related issue raised in the public review, it would be nice if the authors confirm whether the tiling patterns of hippocampal subregions have been weakened by presenting the population activities for the scrambled condition as in the visual cortices in Extended Data Fig. 11a.

We have clarified in the earlier responses, please see above.

4) In Fig. 4 and Extended Data Fig. 3, the proportion of movie-tuned cells in the hippocampus seems to drop significantly after only a portion of trials under specific conditions were extracted. Although the authors addressed the stability issue by comparing the neural responses between even and odd trials, the concern about whether the movie-tuning is driven by a certain portion of trials still remains. To avoid such misunderstanding, as mentioned in comment no.2, tracking the changes in the z-scored sparsity of one cell between continuous and scrambled conditions should be provided. In addition, according to the methods, the scrambled condition was divided into two blocks of 10 trials each, possibly causing premature movie-tuned activities. Thus, it should be more appropriate to compare with the first 10 trials of each block in the continuous condition.

Done.

5) Explanations related to statistical analysis should be added to the methods sections. In Fig. 2a (and related figures with similar analysis), when comparing three or more groups, the Kruskal-Wallis test should be performed first to check whether there is a difference between the groups, and then pairwise comparisons should follow with adjusted p-values for multiple comparisons. Also, in Fig. 4b (and related figures), it seems that the K-S test was performed to test the changes in cell proportion by combining all brain regions, as far as I understand. However, it would be more appropriate to test the proportional changes by a Chi-square test within each region since the total numbers of cells should differ across the regions.

Yes, we have used the KS test throughout the analyses, unless otherwise mentioned or appropriate.

6) The labeling for firing rate is 'FR (sp/sec)' in Fig. 1, 2, and 4, but it is 'Firing rate (Hz)' in Fig. 3.

This has been fixed now, and only Firing rate (Hz), is used throughout. Thank you for pointing this out.

7) There is a typo in Extended Data Fig. 11b. "... across all tuned responses from (b)." It should be (a) instead of (b).

Done

Reviewer #3 (Recommendations For The Authors):

While the study presents an interesting dataset and conceptual approach, there are ways in which the manuscript should be strengthened.

Minor concerns:

1) Related to point (5) above, what content did the hippocampal "movie fields" encode? It would add a substantive dimension to the paper if the authors included examples of what segments of the movie the cells responded to. Are there "pan left" cells, or "man gets in the car" cells? Or was it more arbitrary than that? What is an example of a movie feature lasting 50ms that is stably encoded by a mouse hippocampal neuron?

We show example cells with very sharply tuned neural responses (Figure 2h). A thorough analysis of the visual content is in progress but beyond the scope of this paper.

2) Line 24-seems like it should read "Consistent presentation of the movie..." , with "ly" dropped from "consistent".

Done

3) Line 43-seems to be missing the article "a", and should read "...despite strong evidence for A hippocampal role in...".

We rewrote this sentence for better clarity

4) Line 54-to clarify, the higher visual areas recorded were the anteromedial (AM) and posterior-medial (PM) areas? The text additionally indicates a "medio-lateral" extrastriate area, but there is no such area. Can the text be revised to clear this up?

Sorry about this confusion, indeed we meant posterior-medial (PM). Thank you for pointing this out.

5) Line 84, "rate" should be pluralized to "rates".

Done

6) Line 108- the extra "But" at the start of the sentence should be removed.

Done

7) Figure 2h-was there any particular arrangement for the cells in this sub-panel? If not, could they be grouped by sub-region (or proximity between sub-regions) so it appears less arbitrary?

Done

8) Extended data 2 figure legend for (b) is missing a "that": "Fraction of selective neurons that was significantly above chance.... Ranging from 7.1% in CA

Done

9) Line 144-145, there is an extra "and" in the sentence: ".... were typically neither as narrow AND nor as prominent...."

Done

10) Line 203-the first word in the line should be "frames" (plural).

Done, thank you for pointing this out

11) Line 281-in "...scrambled sequence"-"sequence" should be plural. It looks like the same is true in line 882, in the legend title for Extended Data Fig. 11.

Since we only showed one scrambled sequence (which was repeated 20 times), we rewrote the relevant lines to be “the scrambled sequence”

12) Line 923-the first sentence of the legend for Extended Data Fig. 14-to what data or study are the authors referring to in saying that "More than 50% of hippocampal place cells shut down during maze exploration."? This was confusing, please clarify.

This reference has now been added.

Author Response

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

Reviewer #1

1.1 Fig. 1: A good control for these studies would be a TDP-43 variant with an RRM1 mutation that impairs RNA binding, but not an acetylation mimic (i.e. mutations affecting W113, R151, F147, or F149)

In our original paper (Cohen et al, Nat Commun. 2015 Jan 5; 6:5845), we already characterized TDP-43 acetylation and employed a complete RNA-deficient mutant (F147/149L), as the reviewer suggested. In that original study, this mutant showed maximal RNA binding-deficiency, and therefore we proposed that acetylation mimic mutations represent a comparable RNA-binding deficient variant.

1.2 Fig. 1: time and expression level can influence nuclear TDP-43 puncta formation. It is important that the authors take these into account when measuring puncta number/frequency.

All expression levels and transfection/transduction times were identical across samples. We chose the optimal times to express TDP-43 constructs yet minimize toxicity and found that neuronal transduction at DIV10 and arsenite exposure on DIV14 in mature neurons was optimal.

1.3 Fig. 2: to accurately refer to the nuclear foci as anisosomes, the authors will need to conduct higher-resolution imaging.

We agree with the reviewer and since anisosomes are not well characterized in terms of their relationship to TDP-43 nuclear foci (and may represent only a subset of foci), we have now omitted any mention of anisosomes but instead refer to them in the discussion, where we suggest that TDP-43 K145Q foci may partially represent anisosomes.

1.4 Fig. 2D: it seems as though the splicing reporter should have a fluorescence-based readout (red/green ratio, for instance). Is this the case, and is the ratio informative?

We have now removed the splicing reporter data and replaced this with much more robust data showing RT-qPCR of downstream TDP-43 targets including Sortilin-1 (see the new revised Figure 2E and 3B-I).

1.5 Line 145: "Overall, these results indicate that a single endogenously expressed acetylation-mimic TDP-43(K145Q) mutation is sufficient to alter TDP-43 localization, induce TDP-43 phase separation, and impair splicing in a murine primary neuron culture model." The authors did not assess phase separation in this study. Moreover, it would be more convincing to assess native splice targets of TDP-43 in K145Q primary neurons, rather than an exogenous splicing reporter.

See comment 1.1 above. We have now avoided mentioning phase separation in the main text but mention this as a potential mechanism in the discussion. In addition, we have now evaluated native TDP-43 splice targeted in primary neurons.

1.6 Fig. 4A: is the loss of neurons selective for a specific layer or region of the cortex?

Since we did not observe any gliosis, we have gone back and completely re-evaluated neuronal loss since the concept of neurodegeneration is a critical question in the TDP-43KQ/KQ mice. We do not find any significant neuronal loss in the homozygous TDP-43KQ/KQ mice (see Figure 5).

1.7 Fig. 6: The authors suggest that the large majority of splicing changes are direct results of the TDP43(K145Q) mutation and impaired RNA binding by TDP-43. However, without a direct assessment of TDP43(K145Q) target RNAs in comparison to those of TDP-43(WT), this is only an assumption. Moreover, given the fact that RNA-seq was performed in aged animals, the potential for indirect gene expression changes is very high.

In our original study (Cohen et al, Nat Commun. 2015 Jan 5;6:5845), we showed that the K145Q is severely deficient in RNA binding. In this study, we now show strong evidence that many known targets of direct TDP-43 binding are dysregulated, supporting the expected loss of function if TDP-43 K145Q mutation abrogated RNA binding. Although we have not performed direct RNA binding studies to the Sort1 transcript, for example, other studies have clearly indicated that wild-type TDP-43 binds these targets. We infer that loss of function mutations (i.e., K145Q) impact direct targets of TDP-43. Future studies employing RNA-immunoprecipitation followed by RNA sequencing (RIP-seq) could be useful in this regard and will be required to mechanistically address this point.

1.8 Sup Fig. 8 is very interesting and suggests that any TDP-43 variant that is unable to bind RNA may lead to upregulation of TDP43 RNA and phenotypes similar to those observed n K145Q animals. This is alluded to in the discussion but never specifically tested.

Yes, we agree with this reviewer’s comment. Loss of RNA binding, whether due to acetylation (e.g., K145Q) or otherwise is expected to cause autoregulatory up-regulation of the TARDBP transcript and impact other targets, potentially yielding phenotypes similar to the TDP-43KQ/KQ mice. However, new in vivo models would be needed to prove this point. For example, in the future, we will consider this possibility by characterizing recently identified RNA-binding deficient familial TARDBP mutants (e.g., P112H or K181E).

1.9 The authors should also provide some comment or potential explanation for why TDP43(K145Q) animals show no signs of motor neuron disease.

We now show a moderate level of TDP-43 aggregation and hyper-phosphorylation in spinal cord of mutant mice in Figure 6 – Figure Supplement 3. We also speculate in the discussion why we observe aspects of TDP-43 dysfunction in spinal cord without overt motor phenotypes up until 18 months old.

1.10 Line 79: "However, TARDBP mutations that disrupt RNA binding, and thereby may act in a similar manner to TDP-43 acetylation, have been identified in FTLD-TDP patients." Evidence suggests that the D169G mutation does not interfere with RNA binding. See Furukawa et al., 2016.

We thank the reviewer for pointing this out. We have now removed the D169G mutation from the discussion.

1.11 It is unclear why the authors focused solely on homozygous K145Q animals, rather than heterozygous mice.

We focused initially on homozygous mutant mice to provide better statistical power to detect small effect sizes. However, we have now included a thorough analysis of heterozygous mice including molecular analysis of brain tissue and mouse behavior, as shown in Figure 4 – Figure Supplements 1-2 and Figure 6 – Figure Supplements 1-3.

Reviewer #2

2.1 A strength of this paper is the generation of a new mouse model to study the effects of K145 acetylation in TDP-43 proteinopathy. While the authors note an absence of a behavioral phenotype on neuromuscular testing in aged animals, it would be appropriate to include some analysis of spinal cord and skeletal muscle in this initial description of their model. At a minimum, I wonder if there is pathology in the cord (neuron loss, gliosis) or muscle (fiber atrophy) if insoluble p-TDP-43 is detectable in these tissues, and whether dysregulated splicing of TDP-43 target genes (such as shown in Fig 7) occurs at these sites.

See comment 1.9 above. We analyzed TDP-43 aggregation, localization, and splicing in the spinal cord of TDP-43KQ/KQ mice and found mild loss of TDP-43 function that was comparable, though not to same extent, as that seen in hippocampus and cortex. We discussed these findings in the discussion and provide several possibilities for why there are no overt motor phenotypes in these mice. We note that TDP-43 Q331K knock-in mice also have cognitive but no motor deficits, suggesting TDP-43 dysfunction may preferentially (or at least initially) impact cognitive function (White et al, Nat Neurosci. 2018 Apr;21(4):552-563).

2.2 Fig 2: Differences in the splicing reporter are hard to appreciate from the images shown in panel E. Is the quantification shown in panel F corroborated by an analysis of green vs yellow fluorescence or by another method? Quantification of results shown in panel 2G (from 3 biological replicates) should be included.

We have now removed the splicing reporter data in lieu of the more robust RT-qPCR data shown in Figure 2E and 3B-I. We have also now included more biological replicates from our iPSC neuron imaging, as shown in Figure 3A. Due to time and resource constraints, we were not able to quantify the images shown in figure 3A, and reinforce in the text that our statements are qualitative. However, we were able to add quantitative analysis of TDP-43 dysfunction, by detecting genotype-dependent splicing changes in hiPSC neurons, as mentioned above, which strengthens our claim that TDP-43 dysfunction is prominent in this culture modee.

2.3 Fig 4: Differences in NeuN quantification without changes in cresyl violet staining or gliosis are surprising and a bit difficult to understand. Is there confirmation of neuron loss through another metric? Is it possible that NeuN expression is lower in mutants without frank neuron loss? Also, although no significant differences were seen by IF for TDP-43 staining, did IF for phospho TDP-43 show differences? One might expect this to be the case given the biochemical findings in Fig 5.

See comment 1.6 above. After a much more in-depth and rigorous assessment, we find little evidence for neurodegeneration. Given the transcriptome data showing that TDP-43 regulates a subset of synaptic genes, we suggest that synaptic deficits underlie the behavioral phenotype rather than neuronal loss.

Regarding phospho-TDP-43 pathology by immunofluorescence (IF) staining, after much effort, we have not been able to detect phospho-TDP-43 pathology by IF in TDP-43KQ/KQ mice. Currently available phospho-TDP-43 antibodies (including those acquired from collaborators) do not work well to detect endogenous mouse TDP-43 by histology or IF staining, and therefore we are somewhat limited technically. Nonetheless, given the increase in phospho-TDP-43 in the insoluble fractions by western blotting combined with the increase in cytoplasmic TDP-43 via biochemical fractionation, our data suggest that phospho-TDP-43 is the relevant species accumulating in the cytoplasm of TDP-43KQ/KQ mice.

2.4 Fig 5: Probing the NC fractions for phospho TDP-43 would be an interesting addition to support the conclusion that increased cytoplasmic localization of the KQ mutant occurs prior to its phosphorylation.

We agree that this would be an excellent addition to our data. Unfortunately, after rigorous antibody validation experiments, we were not able to find a phospho-TDP-43 antibody that specifically detected phosphorylated TDP-43 and did not cross-react with unphosphorylated TDP-43 in the buffers used for N-C fractionations. We tested phospho-TDP antibodies in RIPA (soluble), Urea (detergent-insoluble), and the N-C fractionation buffers, using samples treated or untreated with lambda phosphatase (to de-phosphorylate TDP-43). Only one antibody reliably detected the phosphorylated TDP-43 and not the lambda phosphatase-treated TDP-43 samples, and only did so in the Urea buffer, which is shown by straight westerns in our manuscript. Because of these technical difficulties with the phospho-TDP-43 antibodies, this was a challenging point to address at the moment. As better phospho-TDP antibodies become available, we hope to be able to address this. We therefore cannot definitively conclude that cytoplasmic phospho-TDP-43 pathology is present in these mice, but nonetheless the total phospho-TDP-43 levels are significantly elevated in urea (insoluble) fractions.

2.5 Fig 1: What quantitative criteria were used to distinguish between puncta and foci, as highlighted in panel A? What is the biological significance of this distinction? From the images in panel A, it is difficult to see the TDP-43 foci in wt and K145R expressing cells.

Although the size of nuclear TDP-43 foci can be quite variable, and we are certainly interested in the biological significance of this parameter, we did not focus this study on size profiles of K145Q-induced foci, only their accelerated formation and abundance. Therefore, in the revised manuscript we chose not to explicitly state any differences in “foci” vs. “puncta” and now refer to all nuclear TDP-43 structures as “foci” (removed the word “puncta” throughout).

2.6 Fig 3: In describing the results of context-dependent fear testing, it is more appropriate to state that significant deficits appeared at 18 months, deleting the word "more" on line 186.

We have deleted the work “more”.

Reviewer #3

3.1 Multiple figures (1b, 1c, 2b, 2c, 4b, 4d, 4f, 4g, 4i, 4j) include data with multiple measurements per field of view and multiple fields of view per condition. It appears that each measurement was considered an "n" for ANOVA or t-tests, but the data structure violates the requirement that data points are independent. More rigorous statistical methods such as mixed effect models should be considered (see DOI: 10.1016/j.neuron.2021.10.030) which in many cases provide more statistical power. Mixed effects models are the more appropriate statistical method for much of their data. Should the authors want to reanalyze their data with this method, they can reach out to me for an introduction to this statistical model.

We have now re-evaluated the figures mentioned using linear mixed effects models, similar to what the reviewer has mentioned. The new statistical measurements have been incorporated into the revised Figures 1, 2, and 5 (formerly Figure 4). A description of the statistical methods used is now provided in the revised methods section.

3.2 In the introduction, the authors write "we avoid both TDP-43 overexpression and disruption of autoregulatory genomic elements of the endogenous Tardbp transcript" but they show that autoregulation is altered. So shouldn't the acetylation sites be considered a genomic element that regulates autoregulation?

We agree and have now stated that our knock-in approach avoids disrupting surrounding genomic elements (as could occur with transgenic or gene replacement strategies, for example) in order to retain the native Tardbp gene in its unaltered form.

3.3 Suggest editing the language regarding potential neurodegeneration/neuron loss as the same results could be obtained with tissue volume and/or developmental effects independent of progressive neurodegeneration.

See comments 1.6 and 2.3 above. The language has been edited to reflect no apparent neurodegeneration.

3.4 Sequencing the top predicted off-target loci in CRISPR'd mice and iPSC cell lines would help show the absence of off-target mutations.

We described in the methods how potential off-target effects were avoided. We assessed the likelihood of off-target mutations using prediction algorithms to ensure low likelihood. All of the predicted exonic off-target sites have 4 mismatches, making them extremely unlikely to be mutated.

3.5 The authors describe a subtle shift in electrophoretic mobility of the SORT1 protein band in figure 7d/e, but it is unclear why the entire SORT1 band should be shifted up in mutant mice given that the RNA analysis suggests that WT species (not the cryptically spliced +ex17b) is still the major RNA that is expressed. In addition, others have shown that the WT versus +ex17b bands can be resolved (see DOI: 10.1073/pnas.1211577110). Perhaps knockout/knockdown cells can facilitate by providing a positive control for sizing/separation of Sort1 by immunoblotting.

Please refer to our RNA-seq data shown in Figure 8A. In WT mice, nearly 80% of Sort1 transcripts lack exon17b, while this number drops to 23% in the TDP-43KQ/KQ mice. Therefore, the abnormally spliced +ex17b becomes the dominant transcript in TDP-43KQ/KQ mice. Given the prominent +ex17b inclusion that we are observing at the transcript level, it is not surprising that we mostly observe the up-shifted ex17b-containing Sort1 protein band. We have been unable to resolve two distinct bands by immunoblotting in mouse tissues using multiple Sort1 antibodies, including those used in Prudencio et al Proc Natl Acad Sci U S A. 2012 Dec 26;109(52):21510-5. Nonetheless, the up-shifted Sort1 protein is clearly the abnormal variant, as it becomes destabilized in our mice. Another possibility is that partial loss of TDP-43 function, as we suspect occurs in the TDP-43KQ/KQ mice, may magnify (or enhance) the effects on Sort1 such that the dominant Sort1 variant observed is the +ex17b containing variant. We suspect this to be true since this phenomenon was also observed in the Prudencio et al study (see Figures 1-2 in that study).

3.6 The authors may try to corroborate their CFTR splicing results by examining fluorescence as it appears that the construct allows for analysis of splicing differences using GFP vs mCherry expression. This is a minor point as RNA-seq analysis demonstrates abundant splicing changes in acetylation-mimic expression models.

We have now removed the CFTR splicing data entirely and replaced it with more robust readouts of endogenous TDP-43 splicing targets both in vitro (Figure 2E, 3B-I) and in vivo (Figure 8B-C).

3.7 Should the bars in figure 3d for 1 and 2 min be colored in grey/pink? It is unclear why they are clear and only outlined in color.

This point is clarified in the revised Figure 4D legend. In our cue-dependent conditioned fear testing, the filled bars beyond 2 min represents the presence of the auditory cue (tone) and the period of statistical analysis.

3.8 The statistical test used (Fisher's exact test?) for determining overlap between transcriptome datasets should be stated.

We clarified our comment in the results section to reflect the use of over-enrichment analysis. In the methods section, it reads “Previously published differentially expressed genes from Hasan et al95 and Polymenidou et al96 were retrieved from the respective publications; significant over-enrichments as well as human gene symbol mappings to mouse orthologs were performed using gprofiler2 (g:Orth).”

Author Response

We thank the reviewers for their work, their careful reading of our manuscript, their appreciative evaluation and their comments and suggestions, which we will consider to ameliorate the paper. 

For now, we anticipate two short considerations.  

We agree that the PCR step in the ADSE evolutive process might introduce a bias in the population and that such effect should be better examined. We have in fact started performing new experiments, among which ADSE evolution cycles without resources. From the elements we currently have, we see the PCR bias effect as minor, not making a significant difference in the emergence and interaction of species we have reported. 

ADSE protocol is markedly simpler than any other evolution protocol based on even the most basic cellular processes. However, many are the experimental parameters which can be changed in ADSE: initial DNAi population (level of randomness vs. combination of designed sequences), resource structure (resource sequence and length, bead-resource linker length and type), capture condition (length and concentration of DNAi, pH, temperature, bead density), amplification step (choice of polymerase and rate of mutation, length of primers, thermal protocol). The availability of these parameters is a strength of ASDE, making possible exploring a large variety of evolution condition and to introduce kinetic drifts (e.g. in the resources). At the same time, the variety of parameters prompted us to make choices as discussed in the article and to stick to them in all our experiments. The exploration of the many variants that can be considered, some of them very interesting, and some of which proposed by the reviewers, would require an important experimental work that we are planning to conduct for a few among these possibilities, to be part of future publications.

Author Response

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

Thank you for the helpful comments regarding our manuscript, "Association between APOL1 risk variants and the occurrence of sepsis among patients hospitalized with infections.” We have revised the title of the manuscript in response to reviewer comments. Additionally, we have updated the manuscript with analyses among patients with pre-existing renal disease alone as well as other items suggested by the reviewers. The Tables have been renumbered to accommodate these revisions.

Public review:

The study has main limitations which need to be addressed and there is lack of functional explanation of carriage. These limitations are: a) the lack of inclusion of non-Black patients; and b) the lack of appropriate explanation if results are false-positive since APOL1 provides risk for chronic renal disease (CRD) and patients with CRD are predisposed to sepsis. Sepsis occurred in 565 Black subjects, of whom 105 (29% ) had APOL1 high-risk genotype and 460 had-low risk genotype. Importantly, the risk for sepsis associated with APOL1 HR variants was no longer significant after adjusting for subjects pre-existing severe renal disease or after excluding these subjects. Thus, the susceptibility pathway seems to be: APOL1 variants > CKD > sepsis diathesis.

Suggestions to the authors:

• The authors need to provide analysis of patients of non-Black origin.

We apologize for not fully clarifying that the APOL1 high-risk genotypes are virtually exclusive to populations of recent African ancestries,1–4 the majority of whom are identified as having Black race in our dataset.5 To illustrate the rarity of APOL1 high-risk genotypes in other reported races, we examined the frequency of these genotypes in White patients who had been hospitalized with infections at VUMC (comparable to the cohort of Black patients used in the study). Compared to the 361 out of 2242 (16.1%) Black patients hospitalized with infections carrying APOL1 high-risk genotypes, there were only 8 carriers of APOL1 high-risk genotypes out of 12,990 White patients (0.06%); of these 8, 2 patients developed sepsis during hospitalization. Due to a low number of carriers (n=8) and limited number of events (n=2), we could not proceed with further analysis. Patients reported as other races (e.g., Asian and American Indian) are less frequent than White or Black patients in the VUMC de-identified EHR; as such, we would anticipate similarly small, if any, numbers of high-risk genotypes among these groups, with insufficient power for meaningful analysis. Comparisons between racial groups that did not have carriage of the APOL1 high-risk genotypes would increase the possibility of confounding by factors associated with racial identity (e.g., social determinants of health), rather than genotype; as such, detected differences would likely reflect those factors, rather than the impact of APOL1.

We have now added clarifying language in the Methods section.

• The Table of demographics needs to include the type of infections and the underlying pathogen.

Microbiological evidence of specific infection types is not available for the majority of records for patients hospitalized with infections (as well as sepsis); indeed, for many patients with common infections (e.g., pneumonia) the pathogen is often not identified.6 While we do not have details regarding the underlying pathogens, we were able to determine infection categories at admission. We now include details regarding the categories of infection based on ICD codes in Supplementary Table 1, and the updated Table 1 now includes that information for the APOL1 high-risk and low-risk groups. Given that individuals could have more than one type of infection, we also tested the number of types of infection and found no significant difference between the high-risk and low-risk genotypes (p=0.77).

• The authors need to provide convincing analysis if results are false-positive since APOL1 provides risk for chronic renal disease (CRD) and patients with CRD are predisposed to sepsis. For this purpose, they have to provide evidence if the sepsis causes (both type of infection and implicated pathogens) in patients with CRD who are carriers of APOL1 variants are different than in patients with CRD who are not carriers of APOL1 variants.

Indeed, we believe the presented findings suggest that the apparent association between APOL1 high-risk genotypes and sepsis is driven by associated pre-existing severe renal disease rather than APOL1 itself; we appreciate the suggestion to conduct additional analyses to assess whether APOL1 high-risk genotypes impact the occurrence of sepsis among those patients with pre-existing severe renal disease. We note that this analysis could also be biased towards detecting a spurious association between APOL1 high-risk genotypes and sepsis if, within the subgroup with pre-existing severe renal disease, patients with high-risk genotypes also have more severe pre-existing renal disease.

Among the patients with pre-existing severe renal disease (n=458), 121 (26.4%) were carriers of the APOL1 high-risk genotypes. First, we assessed the severity of renal disease among these patients, detecting an association between APOL1 high-risk genotypes and greater severity (i.e., CKD stage 5/ESRD) when adjusted for age, sex, and 3 PCs: OR=2.29 (95% CI, 1.42-3.67, p=6.25x10-4). Then, we compared the primary outcome of sepsis in patients with APOL1 high-risk and low-risk genotypes for this subgroup. Despite the potential bias toward detecting an association between sepsis and the high-risk genotype based on the severity of pre-existing renal disease, there was no significant association between the high-risk genotypes and sepsis (OR=1.29, [95% CI, 0.84-1.98, p=0.25]). Finally, we assessed infection categories (as described in the above response) in this subgroup. We found no significant differences between the high-risk and low-risk genotypes in the frequency of any infection category.

These results suggest that the APOL1 high-risk genotypes are not associated with an increased risk of sepsis among patients who have pre-existing severe renal disease. Taken with our other findings, the high-risk genotypes appear to have little or no association with sepsis beyond their association with renal disease. As such, drugs targeting those genotypes would likely have little effect in the acute setting of hospitalization with infection; rather, their primary contribution to the prevention of sepsis would need to target the prevention of underlying renal disease. We have revised our Methods, Results, and Discussion to include these findings.

• Why concentrations of APOL1 were not measured in the plasma of patients?

Although APOL1 high risk genetic variants have been repeatedly associated with renal-related clinical phenotypes, and many candidate mechanisms have been proposed,4 there has been contradictory evidence regarding whether the genetic variants could be linked to altered plasma APOL1 levels or whether APOL1 levels are related to elevated risk of renal disease. This is not surprising since it is the altered biological function of the APOL1 structural variant that is important, rather than the concentration of APOL1 protein. While some studies have detected an association between APOL1 high-risk genotypes and plasma levels among patients with renal disfunction and sepsis,7 other population studies have suggested no association between APOL1 plasma levels and renal function.8 Plasma APOL1 levels are seldom measured in clinical practice and thus were not available in this retrospective cohort. However, given the inconsistency of findings and the underlying biology of APOL1, we believe measurements of levels (rather than function) is unlikely to be illuminating.

• Why analysis towards risk for death is not done?

In the current study, we focused on the risk of in-hospital death. We did not include the risk of out-of-hospital death due to potential data fragmentation. Specifically, we only have access to the patient’s EHRs at VUMC, and death after hospital discharge is not always be included in a patient’s EHR unless relatives contact the hospital. As such, we focused on in-hospital death, which we validated previously with manual chart review.9 Paralleling the design from a previous publication assessing sepsis outcomes, we included discharge to hospice as part of our in-hospital death algorithm,10 as patients with a terminal illnesses are often discharged to hospice. However, to clarify this outcome component, we now refer to in-hospital deaths and discharge to hospice collectively as “short-term mortality.” In this study, of the 84 total patients with the “short-term mortality” outcome, 47 patients were in-hospital deaths and 37 patients were discharged to hospice. Parallel to the short-term mortality, we found no association with in-hospital death alone. Ln 190: discharge to hospice. I am not sure this can be translated in in-hospital mortality. As noted in the above response, we have rephrased this outcome component as “short-term mortality,” following the design of a previous publication assessing sepsis outcomes.10

• The authors need to explain why functional information is not provided.

Functional studies were not performed for several reasons. Animal models are problematic because mice do not have an ortholog to the human APOL1 gene, and the various models developed all have limitations, particularly when second and third perturbations (sepsis and renal impairment) would need to be introduced.11 Also, since we did not observe an association between the genotypes and sepsis independent of pre-existing severe renal disease, we did not pursue additional functional studies. We do describe existing functional analysis in the introduction and briefly in our discussion; we now note this limitation.

• n 162-172: too many assumptions have been used for the trial; thus, progression to sepsis is difficult to define. According to Sepsis-3 sepsis is no more a continuum from infection to sepsis and septic shock. Some patients presented with sepsis (-1, 0, 1 days considered by the authors) and when electronic health records are used, we are not able to detect the exact timepoint of SOFA score turning to a 2-point increase. This is a major limitation of the methodology presented.

Same applies for all comorbidities and data extracted from electronic health records.

Thank you for highlighting this issue. We acknowledge that our choice of wording was unclear. The choice of ICD infection codes during the initial hospitalization window (i.e., -1, 0, 1 days) was aimed to generate a clean cohort of patients hospitalized with infections (i.e., not secondary infections or development of sepsis after an in-hospital procedure), rather than to establish a timeline of progression from infection to sepsis. As you correctly note, our algorithm would capture patients presenting with infection and concurrent sepsis at admission rather than progression to sepsis, and the exact timepoint of the SOFA score meeting the 2-point criterion is difficult to capture through the EHR. Accordingly, we conducted no time-dependent analysis in the current study. To more accurately convey the methodology of the current study (i.e., testing the association between APOL1 high-risk genotypes—which the patients were born with—and the risk of sepsis for patients hospitalized with infections), we revised the manuscript thoroughly, replacing “progression to sepsis” with “occurrence of sepsis” in the title, abstract as well as on pages 7, 8, and 19. We also acknowledge the limitations of using EHR in the Discussion.

• P value significance thresholds were set at 0.05, except for the PWAS where the threshold was set at 0.05/5 (p13). It would be helpful to list at this point what the 5 outcomes were that led to this adjusted threshold.

We have revised the manuscript accordingly.

"Risk of sepsis was significantly increased among patients with high-risk genotypes (OR 1.29, 1.0 to 1.67, P1.29, CI 1.00-1.67, P<0.47)." Some would argue that a confidence interval that includes 1.0 indicates non-significance.

While the lower bound of the confidence interval appears to meet the 1.0 threshold with only 2 decimal places (which would preclude significance), when taken to the 4th decimal place, the value is 1.0037, demonstrating that the 95% CI did not meet or cross under the 1.0 threshold, and thus the odds ratio should be considered significant (as evidenced by the p=0.047). This result is consistent with other studies that have detected an association between the high-risk genotypes and sepsis,7 but you correctly note that readers can discern from the confidence intervals that the finding is not strong.

• The Discussion is too long and should be shortened.

We have revised the Discussion. 

References:

1. Limou S, Nelson GW, Kopp JB, Winkler CA. APOL1 Kidney Risk Alleles: Population Genetics and Disease Associations. Adv Chronic Kidney Dis. 2014;21(5):426-433. doi:10.1053/j.ackd.2014.06.005

2. Kopp JB, Nelson GW, Sampath K, et al. APOL1 genetic variants in focal segmental glomerulosclerosis and HIV-associated nephropathy. J Am Soc Nephrol. 2011;22(11):2129-2137. doi:10.1681/ASN.2011040388

3. Zhang J, Fedick A, Wasserman S, et al. Analytical Validation of a Personalized Medicine APOL1 Genotyping Assay for Nondiabetic Chronic Kidney Disease Risk Assessment. The Journal of Molecular Diagnostics. 2016;18(2):260-266. doi:10.1016/j.jmoldx.2015.11.003

4. Daneshpajouhnejad P, Kopp JB, Winkler CA, Rosenberg AZ. The evolving story of apolipoprotein L1 nephropathy: the end of the beginning. Nat Rev Nephrol. 2022;18(5):307-320. doi:10.1038/s41581-022-00538-3

5. Dumitrescu L, Ritchie MD, Brown-Gentry K, et al. Assessing the accuracy of observer-reported ancestry in a biorepository linked to electronic medical records. Genet Med. 2010;12(10):648-650. doi:10.1097/GIM.0b013e3181efe2df

6. Wiese AD, Griffin MR, Stein CM, et al. Validation of discharge diagnosis codes to identify serious infections among middle age and older adults. BMJ Open. 2018;8(6):e020857. doi:10.1136/bmjopen-2017-020857

7. Wu J, Ma Z, Raman A, et al. APOL1 risk variants in individuals of African genetic ancestry drive endothelial cell defects that exacerbate sepsis. Immunity. 2021;54(11):2632-2649.e6. doi:10.1016/j.immuni.2021.10.004

8. Kozlitina J, Zhou H, Brown PN, et al. Plasma Levels of Risk-Variant APOL1 Do Not Associate with Renal Disease in a Population-Based Cohort. J Am Soc Nephrol. 2016;27(10):3204-3219. doi:10.1681/ASN.2015101121

9. Liu G, Jiang L, Kerchberger VE, et al. The relationship between high density lipoprotein cholesterol and sepsis: A clinical and genetic approach. Clin Transl Sci. 2023;16(3):489-501. doi:10.1111/cts.13462

10. Alrawashdeh M, Klompas M, Simpson SQ, et al. Prevalence and Outcomes of Previously Healthy Adults Among Patients Hospitalized With Community-Onset Sepsis. Chest. 2022;162(1):101-110. doi:10.1016/j.chest.2022.01.016

11. Yoshida T, Latt KZ, Heymann J, Kopp JB. Lessons From APOL1 Animal Models. Front Med (Lausanne). 2021;8:762901. doi:10.3389/fmed.2021.762901

Author Response

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

Reviewer #1:

In this study, Fang H et al. describe a potential pathway, ITGB4-TNFAIP2-IQGAP1-Rac1, that may involve in the drug resistance in triple negative breast cancer (TNBC). Mechanistically, it was demonstrated that TNFAIP2 bind with IQGAP1 and ITGB4 activating Rac1 and the following drug resistance. The present study focused on breast cancer cell lines with supporting data from mouse model and patient breast cancer tissues. The study is interesting. The experiments were well controlled and carefully carried out. The conclusion is supported by strong evidence provided in the manuscript. The authors may want to discuss the link between ITGB4 and Rac1, between IQGAP1 and Rac1, and between TNFAIP2 and Rac1 as compared with the current results obtained. This is important considering some recent publications in this area (Cancer Sci 2021, J Biol Chem 2008, Cancer Res 2023). In addition, some key points need to be addressed in order to support their conclusion in full.

Thanks for your positive comments.

1) It is rarely found studies using the term of "DNA damage drug resistance". Do the authors mean "DNA damage and drug resistance" or "DNA damage-related drug resistance" or "DNA damage-induced drug resistance"? It is better to define "DNA damage drug resistance" in the manuscript if it is not a common term in the field.

We agree with you that the description "DNA damage-related drug resistance" is better so that we revised it uniformly in the manuscript.

2) For Figure 4A, it is stated the IQGAP1 is identified via IP-MS. However, the MS results are not presented in the Figure or in the supplementary. In Figure 4A, only the IP results with silver staining was presented. Moreover, based on the silver staining here, a bunch of proteins were increased in TNFAIP2 overexpression group compared to the vector group. Especially, there is a much clearer band at 52kDa. The authors didn't explain why they chose IQGAP1 and ITGB4 which are less clear than the protein(s) at 52kDa.

Supplementary table 1 is our mass spectrometry results. There are two reasons for choosing ITGB4 and IQGAP1. Firstly, we selected the proteins that indeed interact with TNFAIP2 according to our verification experiments. Secondly, we were interested in the mechanism by which TNFAIP2 promoting DNA damage-related drug resistance, and we found that ITGB4 promoted drug resistance, while IQGAP1 activated Rac1.

3) According to the images in Figure 4C, the efficiency of si-IQGAP1 is limited. The authors could analyze the WB image to confirm the inhibition efficiency of si-IQGAP1.

We analyzed the WB images and the quantitative results are as follows in Author response image 1. The knockdown efficiency is acceptable.

Author response image 1.

4) In Figure 5B, I wonder whether the authors can explain why the IgG could immunoprecipitate similar amount of ITGB4 protein as input group.

In this experiment, the Input group had relatively less loading amount (5%), while the IgG group had nonspecific binding.

5) According to the results from Figure 6B, the inhibition efficiency of shITGB4#1 is much higher than shITGB4#2. However, the effects of shITGB4#1 on GTP-Rac1 are similar to or even weaker than those of shITGB4#2 in both HCC1806 and HCC1937. Can this be explained?

The possible reason is that downregulation of ITGB4 expression to a certain level is sufficient to inhibit the activation of Rac1.

6) In Figure 6F, there are double bands for ITGB4 while only one band shows in other Figures. Please find a better representative image here.

ITGB4 has a cleaved band in addition to the main band. These two bands could be separated when we used a low concentration SDS-PAGE gel.

7) In the manuscript, GAPDH, b-Actin and Tubulin are used in different experiments as internal controls. Is there any specific reason to using different internal controls for different experiments here?

There is no specific reason using different internal controls. These experiments were conducted by different person. Each individual chose different internal controls based on the protein sizes.

8) I cannot find Table 1 for the correlation results for TNFAIP2 and ITGB4. I wonder whether Figure 8E is the Table 1 as is mentioned, since it is stated in line 561 that Figure 8E is "the work model of this paper" but actually Figure 8F is. If Figure 8E is the correlation results, I highly recommended the scatter plots graph is used here to present more clear and visualized correlation between TNFAIP2 and ITGB4.

Figure 8E is indeed the correlation result. In addition, Figure 8E could not be presented as scatter plot graph because the pattern of TNFAIP2 and ITGB4 expression is negative or positive according to the determination of IHC results which was carried out by professional pathologists.

9) Throughout the whole manuscript, no description of N number was found in figure legends or in Methods for in vitro experiments. N number is important for statistical analysis.

All our experiments have set up three replicates. We provide this information in figure legends.

Reviewer #2:

Breast cancer is the most common malignant tumor in women. One of subtypes in breast cancer is so called triple-negative breast cancer (TNBC), which represents the most difficult subtype to treat and cure in the clinic. Chemotherapy drugs including epirubicin and cisplatin are widely used for TNBC treatment. However, drug resistance remains as a challenge in the clinic. The authors uncovered a molecular pathway involved in chemotherapy drug resistance, and molecular players in this pathway represent as potential drug targets to overcome drug resistance. The experiments are well designed and the conclusions drawn mostly were supported by the data. The findings have potential to be translated into the clinic.

Thanks for your positive comments.

1) In Introduction, the statement of "Breast cancer is the most common malignant tumor in women, and the morbidity and mortality rates of female malignant tumors are ranked first in the world" is inaccurate.

We have revised the description as“Breast cancer is the most commonly diagnosed cancer and the leading cause of cancer death in women”.

2) In Materials and Methods, "Immunopurification and silver staining" is not correct, which should be replaced with "Immunoprecipitation and silver staining".

We replaced the description in the manuscript according to your suggestion.

3) It is unclear Why the authors chose the two TNBC cell lines, HCC1806 and HCC1937, for cell models in this work.

We chose these two cell lines according to our previous work“KLF5 promotes breast cancer proliferation, migration and invasion in part by upregulating the transcription of TNFAIP2” (doi: 10.1038/onc.2015.263. Epub 2015 Jul 20).

4) To demonstrate TNFAIP2 and ITGB4 confer TNBC drug resistance in vivo, the knockdown efficiency of animal experiments was not shown.

The knockdown efficiency of animal experiments was shown below. We added this result into Figure 2-figure supplement 2G and Figure 5-figure supplement 2N.

5) I would strongly suggest the authors seek help from a language editing service to improve the manuscript.

We improved the manuscript by using a professional English language editing service and we have carefully revised the manuscript.

Reviewer #3:

In this manuscript, Fang and colleagues found that IQGAP1 interacts with TNFAIP2, which activates Rac1 to promote drug resistance in TNBC. Furthermore, they found that ITGB4 could interact with TNFAIP2 to promote TNBC drug resistance via the TNFAIP2/IQGAP1/Rac1 axis by promoting DNA damage repair.

This work has good innovation and high potential clinical significance. However, there are several unsolved concerns that have to be addressed.

Thanks for your positive comments.

1) In the manuscript, there are four drugs used for in vitro cell experiments, why is olaparib (AZD) not used for in vivo animal experiments？

There are two reasons why we did not choose AZD. First，the killing effect of AZD is not as strong as that of BMN. Second, AZD is more expensive than BMN. We finally chose BMN for animal experiments.

2) In Figure 4B, why the immunoprecipitation experiments is done in HCC1806 cell line？

In our previous study “KLF5 promotes breast cancer proliferation, migration and invasion in part by upregulating the transcription of TNFAIP2” (doi: 10.1038/onc.2015.263. Epub 2015 Jul 20), we found that TNFAIP2 knockdown could obviously inhibit the activation of Rac1 in HCC1806 when compared to the result in HCC1937. So, we used HCC1806 cell line to perform the IP-Mass assay.

3) There should be data showing the knockdown effect of TNFAIP2 and ITGB4 in animal experiments.

We addressed the same question above (Reviewer #2, Question#4).

4) When screening the interaction regions between ITGB4 and TNFAIP2, why the TNFAIP2 protein truncation strategy is to delete the N-terminus？

In fact, we also deleted the C-terminus, but the deletion of C-terminus of TNFAIP2 did not affect the interaction.

5) In the manuscript, "input" should be changed to "Input".

We corrected it.

6) There should be a space between "Figure" and numbers.

We add a space between "Figure" and numbers.

Author Response

Reviewer #1 (Public Review):

Summary:

The authors of this manuscript characterize new anion conducting that is more red-shifted in its spectrum than prior variants called MsACR1. An additional mutant variant of MsACR1 that is renamed raACR has a 20 nm red-shifted spectral response with faster kinetics. Due to the spectral shift of these variants, the authors proposed that it is possible to inhibit the expression of MsACR1 and raACR with lights at 635 nm in vivo and in vitro. The authors were able to demonstrate some inhibition in vitro and in vivo with 635 nm light. Overall the new variants with unique properties should be able to suppress neuronal activities with red-shifted light stimulation.

Strengths:

The authors were able to identify a new class of anion conducting channelrhodopsin and have variants that respond strongly to lights with wavelength >550 nm. The authors were able to demonstrate this variant, MsACR1, can alter behavior in vivo with 635 nm light. The second major strength of the study is the development of a red-shifted mutant of MsACR1 that has faster kinetics and 20 nm red-shifted from a single mutation.

Weaknesses:

The red-shifted raACR appears to work much less efficiently than MsACR1 even with 635 nm light illumination both in vivo (Figure 4) and in vitro (Figure 3E) despite the 20 nm red-shift. This is inconsistent with the benefits and effects of red-shifting the spectrum in raACR. This usually would suggest raACR either has a lower conductance than MsACR1 or that the membrane/overall expression of raACR is much weaker than MsACR1. Neither of these is measured in the current manuscript.

Thank you for addressing this crucial issue. We posit that the diminished efficiency of raACR in comparison to MsACR1 WT can be attributed to the tenfold acceleration of its photocycle. As noted by Reviewer 1, the anticipated advantages associated with a red-shifted opsin, particularly in in vivo preparations, are offset by its accelerated off-kinetics. Consequently, the shorter dwell time of the open state leads to a reduced number of conducted ions per photon. Nevertheless, the operational light sensitivity is not drastically altered compared to MsACR WT (Fig. 3C). We believe that the rapid kinetics offer interesting applications, such as the precise inhibition of single action potentials through holography.

There are limited comparisons to existing variants of ACRs under the same conditions in the manuscript overall. There should be more parallel comparison with gtACR1, ZipACR, and RubyACR in identical conditions in cultured cell lines, cultured neurons, and in vivo. This should be in terms of overall performance, efficiency, and expression in identical conditions. Without this information, it is unclear whether the effects at 635 nm are due to the expression level which can compensate for the spectral shift.

We compared MsACR1 and raACR with GtACR1 in ND cells in supplemental figure 4. We concur that further comparisons could be useful to emphasise both the strengths of MsACRs and applications where they may not be as suitable. We are currently in the process of outlining a separate article. We firmly believe that each ACR variant occupies a distinct application niche, which necessitates a more comprehensive electrophysiological comparison to provide valuable insights to the scientific community.

There should be more raw traces from the recordings of the different variants in response to short pulse stimulation and long pulse stimulation to different wavelengths. It is difficult to judge what the response would be like when these types of information are missing.

We appreciate Reviewer 1's feedback and have compiled a collection of raw photoresponses, encompassing various pulse widths and wavelengths, which can be found in the Supplementary materials (Supplementary Figures 4 and 5).

Despite being able to activate the channelrhodopsin with 635 nm light, the main utility of the variant should be transcranial stimulation which was not demonstrated here.

We concur with Reviewer 1's assessment that MsACR prime application is indeed transcranial stimulation. However, it's worth emphasising that the full advantages of transcranial optical stimulation become most apparent when animals are truly freely moving without any tethered patch cords. Our ongoing research in the laboratory is dedicated to the development of a wireless LED system that can be securely affixed to the animal's skull. We aim to demonstrate the potential of these novell optogenetic approaches in the field of behavioural neuroscience in the coming year.

Figure 3B is not clearly annotated and is difficult to match the explanation in the figure legend to the figure. The action potential spikings of neurons expressing raACR in this panel are inhibited as strongly as MsACR1.

We have enhanced the figure caption and annotations for clarity. The traces presented in Figure 3B are intended to demonstrate the overall effectiveness of each variant. However, it is in the population data analysis, as depicted in Figure 3E, where the meaningful insights are revealed.

For many characterizations, the number of 'n's are quite low (3-7).

We acknowledge Reviewer 1's suggestion regarding the in vivo data and agree with the importance of including more animals, as well as control animals. However, we are committed to adhering to the principles of the 3Rs (Replacement, Reduction, Refinement) in animal research, and given the robustness of our observed effects, we will add animals to reach the minimal number of animals per condition (n = 2) to minimise unnecessary animal usage while ensuring statistical power. We will continue to adhere to the established standards in the field, aiming for a range of 3 to 7 cells per condition, sourced from at least two independent preparations, to ensure the robustness and reliability of our in vitro data.

Reviewer #2 (Public Review):

Summary:

The authors identified a new chloride-conducting Channelrhodopsin (MsACR1) that can be activated at low light intensities and within the red part of the visible spectrum. Additional engineering of MsACR1 yielded a variant (raACR1) with increased current amplitudes, accelerated kinetics, and a 20nm red-shifted peak excitation wavelength. Stimulation of MsACR1 and raACR1 expressing neurons with 635nm in mice's primary motor cortices inhibited the animals' locomotion.

Strengths:

The in vitro characterization of the newly identified ACRs is very detailed and confirms the biophysical properties as described by the authors. Notably, the ACRs are very light sensitive and allow for efficient in vitro inhibition of neurons in the nano Watt/mm^2 range. These new ACRs give neuroscientists and cell biologists a new tool to control chloride flux over biological membranes with high temporal and spatial precision. The red-shifted excitation peaks of these ACRs could allow for multiplexed application with blue-light excited optogenetic tools such as cation-conducting channelrhodopsins or green-fluorescent calcium indicators such as GCaMP.

Weaknesses:

The in-vivo characterization of MsACR1 and raACR1 lacks critical control experiments and is, therefore, too preliminary. The experimental conditions differ fundamentally between in vitro and in vivo characterizations. For example, chloride gradients differ within neurons which can weaken inhibition or even cause excitation at synapses, as pointed out by the authors. Notably, the patch pipettes for the in vitro characterization contained low chloride concentrations that might not reflect possible conditions found in the in vivo preparations, i.e., increasing chloride gradients from dendrites to synapses.

We appreciate Reviewer 2’s feedback regarding missing control experiments. We will respond to these concerns in another section of our manuscript, as suggested. Regarding the chloride gradient, we understand the concerns of Reviewer 2, yet we chose these ionic conditions, particularly as they were used in the initial electrical characterization of GtACR1 in a neuronal context (Mahn et al., 2016). We will make sure to provide this context in our manuscript to justify our choice of ionic conditions.

Interestingly, the authors used soma-targeted (st) MsACR1 and raACR1 for some of their in vitro characterization yielding more efficient inhibition and reduction of co-incidental "on-set" spiking. Still, the authors do not seem to have utilized st-variants in vivo.

At the time of submission, due to the long-term absence of our lab technician, we were not able to produce purified viruses. Therefore, we decided to move on with the submission. We now produced the virus externally, and will provide the experiments.

Most importantly, critical in vivo control experiments, such as negative controls like GFP or positive controls like NpHR, are missing. These controls would exclude potential behavioral effects due to experimental artifacts. Moreover, in vivo electrophysiology could have confirmed whether targeted neurons were inhibited under optogenetic stimulations.

We have several non-injected control animals that we used to calibrate this particular paradigm and never saw similar responses. However, we acknowledge the suggestion of Reviewer 2 and will include the GFP-injected control as recommended.

Some of these concerns stem from the fact that the pulsed raACR stimulation at 635 nm at 10Hz (Fig. 3E) was far less efficient compared to MsACR1, yet the in vivo comparison yielded very similar results (Fig. 4D).

As outlined previously, the accelerated photocycle of raACR results in a reduction in photocurrent amplitude, consequently diminishing the potency of inhibition per photon. In the context of in vitro stimulation, where single action potentials are recorded, this reduction in inhibition efficiency is resolved. However, in the realm of in vivo behavioural analysis, the observed effect is not contingent on single action potentials but rather stems from the disruption of the entire M1 motor network. In this context, despite the reduced efficiency of the fast-cycling raACR, it still manages to interrupt the M1 network, leading to similar behavioural outcomes.

Also, the cortex is highly heterogeneous and comprises excitatory and inhibitory neurons. Using the synapsin promoter, the viral expression paradigm could target both types and cause differential effects, which has not been investigated further, for example, by immunohistochemistry. An alternative expression system, for example, under VGLUT1 control, could have mitigated some of these concerns.

Indeed, we acknowledge the limitations of our current experimental approach. We are in the process of planning and conducting additional experiments involving cre-dependent expression of st-MSACR and st-raACR in PV-Cre mice.

Furthermore, the authors applied different light intensities, wavelengths, and stimulation frequencies during the in vitro characterization, causing varying spike inhibition efficiencies. The in vivo characterization is notably lacking this type of control. Thus, it is unclear why the 635nm, 2s at 20Hz every 5s stimulation protocol, which has no equivalent in the in vitro characterization, was chosen.

We appreciate the valuable comment from the reviewer. The objective of our in vitro characterization is to elucidate the general effects of specific stimulation parameters on the efficiency of neuronal inhibition. For instance, we aim to demonstrate that lower light intensities result in less efficient inhibition, or that pulse stimulation may lead to a less complete inhibition, albeit significantly reducing the energy input into the system.

In the in vivo characterization, we face constraints such as animal welfare considerations and limitations in available laser lines, which prevent us from exploring the entire parameter space as comprehensively as in the in vitro preparation. Additionally, it is important to note that membrane capacitance tends to be higher in vivo compared to dissociated hippocampal neurons. Consequently, we have opted for a doubled stimulation frequency from 10 Hz to 20 Hz and the stimulation pattern of 2 seconds ”on” and 5 seconds “off”. This approach allows the animals to spend less time in an arrested state while still demonstrating the effect of MsACR and variants.

In summary, the in vivo experiments did not confirm whether the observed inhibition of mouse locomotion occurred due to the inhibition of neurons or experimental artifacts.

In addition, the author's main claim of more efficient neuronal inhibition would require them to threshold MsACR1 and raACR1 against alternative methods such as the red-shifted NpHR variant Jaws or other ACRs to give readers meaningful guidance when choosing an inhibitory tool.

The light sensitivity of MsACR1 and raACR1 are impressive and well characterized in vitro. However, the authors only reported the overall light output at the fiber tip for the in vivo experiments: 0.5 mW. Without context, it is difficult to evaluate this value. Calculating the light power density at certain distances from the light fiber or thresholding against alternative tools such as NpHR, Jaws, or other ACRs would allow for a more meaningful evaluation.

Author Response

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

We would like to thank the Editors for the opportunity to submit a revised manuscript, and the Reviewers for their positive evaluations and constructive comments. We feel that the comments and suggestions significantly improved the quality of our manuscript. We addressed all questions and suggestions in a point-by-point fashion below.

Reviewer #1 (Public Review):

This paper proposes and evaluates a new approach for the registration of human hippocampal anatomy between individuals. Such registration is an essential step in group analysis of hippocampal structure and function, and in most studies to date, volumetric registration of MRI scans has been employed. However, it is known that volumetric deformable registration, due to its formulation as an optimization problem that minimizes the combination of an image similarity term and relatively simple geometric regularization terms, fails to preserve the topology of complex structures. In the cerebral cortex, surface-based registration of inflated cortical surfaces is broadly preferred over volumetric registration, which often causes voxels of different tissue types to be matched (e.g., voxels belonging to a sulcus in one individual mapping onto voxels belonging to a gurys in another). The authors recognize that hippocampal anatomy is similarly complex, and, with proper tools, can benefit from surface-based registration. They propose to first unfold the hippocampus to a two-dimensional rectangle domain using their prior HippUnfold technique, and then to perform deformable registration in this rectangle domain, matching geometric features (curvature, thickness, gyrification) between individuals. This registration approach is evaluated by comparing how well hippocampal subfields traced by experts using cytoarchitectural information align between individuals after registration. The authors indeed show that surface-based registration aligns subfields better than volumetric registration applied to binary segmentations of the hippocampal gray matter.

Overall, I find the methods and results in this paper to be convincing. The authors framed the comparison between surface-based and volumetric registration in a fair way, and the results convincingly show the advantage of surface-based registration. One slight limitation of the current study is that it is uncertain whether the benefits demonstrated here translate to in vivo MRI data for which the authors' HippUnfold algorithm is tailored. The current study utilized the unfolding technique used in HippUnfold on manual segmentations of high-resolution ex vivo MRI and blockface 3D volumes, which are likely closer to anatomical ground truth than automated segmentations of in vivo MRI. However, it is reasonable to assume that given that the volumetric registration to which the proposed approach was compared also used this high-detail data, the advantages of surface-based over volumetric registration would extend to in vivo MRI as well. However, I would encourage the authors to perform future evaluations on datasets with available in vivo and ex vivo MRI from the same individuals.

We thank the Reviewer for the positive evaluation and the thoughtful feedback. We address each comment in the red text below.

We have considered the Reviewer suggestion for a demonstration of the gains from our proposed method in MRI, and decided to include a new analysis of 7T in-vivo MRI data from 10 healthy participants (Supplementary Materials 1: in-vivo MRI demonstration).

It is difficult to assess whether changes to the registration methods are indeed an improvement without same-subject “ground-truth” subfield definitions typically obtained from histology. In this new Supplementary Materials section, we demonstrate an overall sharpening of MRI-mapped features as an indirect indication of better inter-subject alignment (similar to the paper referenced in the comment, below). This is an important proof of concept that demonstrates that the gains made in the current project can be translated to in in-vivo MRI. We did not perform a demonstration of these gains in ex-vivo data, since this also comes with a host of challenges including access to such data and deformations and artifacts associated with ev-vivo scanning. However, we believe that the gains provided by our methods are limited mainly by image resolution and so while we note some concern about the gains from this method at 3T MRI, we expect that in ev-vivo gains provided by our method in higher resolution ex-vivo images should be consistent or better.

We have added the following in-text Discussion of this new analysis (p. 13):

“Ravikumar et al. (2021) recently performed flat mapping of the medial temporal lobe neocortex using a Laplace coordinate system as employed here, and showed sharpening of group-averaged images following deformable registration in unfolded space. This indirectly suggests better intersubject alignment. We perform a similar group-averaged sharpening analysis in Supplementary Materials 1: in-vivo demonstration. Though the gains in image sharpness observed here were modest, we note that current MRI resolution and automated segmentation methods allow for only imperfect hippocampal feature measures. We thus expect unfolded registration to grow in importance as MRI and segmentation methods continue to advance. “

I would also like to point out the relevance of the 2021 paper "Unfolding the Medial Temporal Lobe Cortex to Characterize Neurodegeneration Due to Alzheimer's Disease Pathology Using Ex vivo Imaging" by Ravikumar et al. (https://link.springer.com/chapter/10.1007/978-3-030-87586-2_1) to the current work. This paper applied an earlier version of the unfolding method in HippUnfold to ex vivo extrahippocampal cortex and performed registration using curvature features in the rectangular unfolded space, also finding slight improvement with surface-based vs. volumetric registration, so its findings support the current paper.

Thank you, we agree this is a highly relevant paper and have added a summary of it in the newly added Discussion paragraph which also outlines the new Supplementary Materials section (see previous comment).

Overall, the paper has the potential to significantly influence future research on hippocampal involvement in cognition and disease. Outside of simple volumetry studies, most hippocampal morphometry studies rely on volumetric deformable registration of some kind, typically applied to whole-brain T1-weighted MRI scans. With HippUnfold available for anyone to use and not requiring manual registration, the paper provides a strong impetus for using this approach in future studies, particularly where one is interested in localizing effects of interest to specific areas of the hippocampus. Additional evaluation of in vivo HippUnfold using in vivo / ex vivo datasets, would make the use of this approach even more appealing.

We would like to thank the Reviewer for their enthusiasm for the translatability of this work. We hope they are satisfied with our newly added in-vivo evaluation, and we appreciate the thoughtful suggestions.

Reviewer #1 (Recommendations For The Authors):

No additional recommendations.

Reviewer #2 (Public Review):

DeKraker et al. propose a new method for hippocampal registration using a surface-based approach that preserves the topology of the curvature of the hippocampus and boundaries of hippocampal subfields. The surface-based registration method proved to be more precise and resulted in better alignment compared to traditional volumetric-based registration. Moreover, the authors demonstrated that this method can be performed across image modalities by testing the method with seven different histological samples. While the conclusions of this paper are mostly well supported by data, some aspects of the method need to be clarified. This work has the potential to be a powerful new registration technique that can enable precise hippocampal registration and alignment across subjects, datasets, and image modalities.

We thank the Reviewer for their thoughtful evaluation of our paper and helpful comments. We address them in the red text below each comment.

Regarding the methodological clarification of the surfaced-based registration method, the last step of the process needs further clarification. Specifically, after creating the averaged 2D template, it is unclear how each individual sample is registered to sample1's space. If I understand correctly, after creating the averaged 2D template, each individual sample is then registered to sample1's space via the transform from each sample to the averaged template and then the inverse transform from the template to sample1's space. Samples included both left and right hemispheres, so were all samples being propagated to left hemisphere sample 1 space? The authors also note that a measure of the subfield labels overlap with that sample's ground-truth subfield definitions was calculated. Is this a measure of overlap, for example, between sample 3 (registered to sample 1 space) and the ground-truth (unfolded, not registered) sample 3 labels? It would be beneficial to provide a full walkthrough of one example sample to clarify the steps. Clarification of this aspect of the method is critical for understanding the evaluation of the method.

We would like to thank the Reviewer for the suggestion, and have clarified the passage with the following walkthrough example as suggested by the Reviewer (p. 8):

“For example, sample3 was unfolded and then registered to the unfolded average, making up two transformations. These were then concatenated with the inverse transformation of unfolded sample1 to the same unfolded average, and the inverse transformation of native sample1 to unfolded space. This concatenated transformation was used to project labels from sample3 native space directly to sample1 native space, which should ideally lead to near-perfect subfield alignment in sample1 native space. Dice overlap between sample1 and sample3 registered to sample1 was then calculated in sample1 native space.”

Reviewer #2 (Recommendations For The Authors):

Materials and Methods:

In the Data section, it would be helpful for the authors to clarify whether each hippocampal histology sample is from a different individual or not. Additionally, for the 3D-PLI sample, the authors mention that the anterior/posterior parts of the hippocampus were cut off and the labels were extrapolated over the missing regions. It would be useful to know whether the extrapolation was done manually.

Thank you, we have added separate labels (donors 1-4) for each individual from each dataset. We have also added that the 3D-PLI dataset was extrapolated manually. See the revised Materials and Methods: Data section.

A small clarification, but for the morphological features calculated by HippUnfold, is thickness a measure of how much space each subfield takes up in the 2D unfolded space?

Thickness is measured via HippUnfold, and we have clarified in-text that it is done in each subject’s native space (p. 6):

Results:

In the Results section, a brief summary or description of the Dice overlap metric would be helpful. The authors should also clarify if the Dice metric measures the overlap between an individual sample (e.g., sample3) that has been unfolded and registered/propagated to sample1 compared to the sample1 ground-truth subfields.

We thank the Reviewer, and hope this is now clarified alongside the Reviewer’s Public comment with the addition of the example as quoted in our response to that comment.

We also added to our description of Dice overlap as a measurement (p. 8):

“The Dice overlap metric (Dice, 1945), which can also be considered an overlap fraction ranging from 0-1, was calculated for all subjects’ subfields registered to sample1.”

Figure 3:

In Figure 3A, it is unclear what "moving (sample 3)" refers to. Clarification is needed, and it would be helpful to know if this is sample 3 in native space before it has been unfolded/registered. In Figure 3B, there is a missing "native" before "folded" and "(right)" at the end of the sentence. With these edits, the sentence in the caption would read: "Each measure was calculated in unfolded space (left) and again in the first sample's (BigBrain left hemisphere) native folded space (right)."

We thank the Reviewer, and have now changed “moving” to “sample3 before registration”, and added the suggested caption changes. See the revised Figure 3.

Discussion:

In the introduction, the authors provide a detailed description of the traditional 3D volumetric registration technique that utilizes gyral and sucal patterning as the primary feature for registration, along with other features such as thickness and intracortical myelin. Using their surface-based registration, the authors highlight an interesting finding that hippocampal curvature is the most informative individual feature, and thickness and curvature combined are the most informative features for registration and boundary alignment. In the discussion, it would be beneficial for the authors to discuss the relationship between curvature, thickness, and gyrification (e.g., is there overlapping information across these features) and comment on the reliability of these features observed in the current study compared to past work using traditional methods.

This is an interesting point of discussion, thank you for raising it. We’ve added the following paragraph to the Discussion section (p. 13):

“The feature most strongly driving surface-based registration in the present study was curvature. Many neocortical surface-based registration methods focus on gyral and sulcal patterning at various levels (e.g. strong alignment of primary sulci, with weaker weighting on secondary and tertiary sulci) (Miller et al., 2021). In the present study, hippocampal gyri are variable between samples and so could perhaps be thought of as similar to tertiary neocortical gyri, and this may help explain why gyrification was not the primary driving feature in aligning hippocampal subfields. The methods used to quantify gyrification are often related to curvature, but differ across studies. In the hippocampus, unlike in the neocortex, the mouth of sulci are wide and so sulcal depth, which is often used in defining neocortical gyrification index, is not straightforward to measure. Using HippUnfold, gyrification is defined by the extent of tissue distortion between folded and unfolded space, and individual gyri/sulci are hard to resolve in unfolded gyrification maps, but are readily visible in curvature maps. Thus, hippocampal curvature may be more informative simply due to higher measurement precision. Future work could also employ measures like quantitative T1 relaxometry or other proxies of intracortical myelin content (e.g. Tardif et al., 2015; Glasser et al., 2016; Paquola et al. 2018) for hippocampal alignment, but this is not possible in cross-modal work as in the various histology stains examined here.”

Miscellaneous:

There is a typo on page 11, line 318, with extra parentheses: "(e.g., (Borne et al., 2023;..."

Thank you, we have corrected this error.

Reviewer #3 (Public Review):

Dekraker and colleagues previously developed a new computational tool that creates a "surface representation" of the hippocampal subfields. This surface representation was previously constructed using histology from a single case. However, it was previously unclear how to best register and compare these surface-based representations to other cases with different morphology.

In the current manuscript, Dekraker and colleagues have demonstrated the ability to align hippocampal subfield parcellations across disparate 3D histology samples that differ in contrast, resolution, and processing/staining methods. In doing so, they validated the previously generated Big-Brain atlas by comparing seven different ground-truth subfield definitions. This is an impressive and valuable effort that provides important groundwork for future in vivo multi-atlas methods.

We thank the Reviewer for their positive evaluations, and helpful suggestions. We provide responses to the recommendations in the red text below.

Reviewer #3 (Recommendations For The Authors):

There are a few points I think the authors should address, listed below.

1) As the authors are well aware, subfield definitions vary considerably across laboratories. The current paper states that JD labeled the samples using three different atlas references: Ding & Van Hoesen, 2015; Duvernoy et al. ,2013, and Palomero-Gallagher et al., 2020. This is unclear, however, since these three references differ in their subfield definitions. For example, Ding & Van Hoesen and Palomero-Gallagher define a region called the prosubiculum (area between subiculum and CA1) but Duvernoy does not. Please clarify which boundary rules from which particular references were used here. How were discrepancies across these references resolved when applying labels to the current histological samples?

We thank the Reviewer, and have added the following elaboration (p. 5):

“Since these sources differ slightly in their boundary criteria, and no prior reference perfectly matches the present samples, subjective judgment was used to draw boundaries after considering all three prior works. The “prosubiculum” label used by Ding & Van Hoesen and Palomero-Gallagher et al. was included as part of the subicular complex. See Supplementary Materials 2: ground-truth segmentation for more details.”

2) Another comment has to do more with the "style" of how this paper is written, especially given that this paper was submitted to eLIFE (i.e. not a specialty journal). For example, the motivation for the unfolded with and without registration methods was not well described. Similarly, there was almost no justification for the different methods applied in Figure 4 and I fear that the impact of these results will be lost on a non-expert reader.

We added the following elaboration to the last paragraph of the Introduction section to motivate our benchmark against unfolding without registration (p. 3):

“We benchmark this new method against unfolding alone, which provides some intrinsic alignment between subjects (DeKraker et al., 2018) but which we believe can be further improved with the present methods, and against more conventional 3D volumetric registration approaches.”

We also added a Discussion paragraph on the results shown in Figure 4 which we hope helps to make these results more informative and impactful (p. 13):

“The feature most strongly driving surface-based registration in the present study was curvature. Many neocortical surface-based registration methods focus on gyral and sulcal patterning at various levels (e.g. strong alignment of primary sulci, with weaker weighting on secondary and tertiary sulci) (Miller et al., 2021). In the present study, hippocampal gyri are variable between samples and so could perhaps be thought of as similar to tertiary neocortical gyri, and this may help explain why gyrification was not the primary driving feature in aligning hippocampal subfields. The methods used to quantify gyrification are often related to curvature, but differ across studies. In the hippocampus, unlike in the neocortex, the mouth of sulci are wide and so sulcal depth, which is often used in defining neocortical gyrification index, is not straightforward to measure. Using HippUnfold, gyrification is defined by the extent of tissue distortion between folded and unfolded space, and individual gyri/sulci are hard to resolve in unfolded gyrification maps, but are readily visible in curvature maps. Thus, hippocampal curvature may be more informative simply due to higher measurement precision. Future work could also employ measures like quantitative T1 relaxometry or other proxies of intracortical myelin content (e.g. Tardif et al., 2015; Glasser et al., 2016; Paquola et al. 2018) for hippocampal alignment, but this is not possible in cross-modal work as in the various histology stains examined here.”

3) Finally, the application of the current work beyond the current dataset needs to be made more clear. From what I understand, the discussion says that using a multi-atlas approach with HippUnfold is unfeasible at this point. What kind of computational or technical developments need to take place in order for these labeled datasets to be used for this purpose? How can the current labeled datasets be used in other contexts?

The question of translation to other contexts, namely, in-vivo MRI, was also raised by Reviewer 1, and as such we decided to include an additional analysis to explore this question (Supplementary Materials 1: in-vivo MRI demonstration). Validation using ground-truth subfields is not plausible in MRI, and so we show only an indirect validation of intersubject alignment based on the sharpening of group-averaged features following better alignment using the present methods. We believe this new analysis significantly clarifies the applications we have in mind for this work. See the new Supplementary Section for details, and also a summary of this analysis in the Discussion section (p. 13):

“Ravikumar et al. (2021) recently performed flat mapping of the medial temporal lobe neocortex using a Laplace coordinate system as employed here, and showed sharpening of group-averaged images following deformable registration in unfolded space. This indirectly suggests better intersubject alignment. We perform a similar group-averaged sharpening analysis in Supplementary Materials 1: in-vivo demonstration. Though the gains in image sharpness observed here were modest, we note that current MRI resolution and automated segmentation methods allow for only imperfect hippocampal feature measures. We thus expect unfolded registration to grow in importance as MRI and segmentation methods continue to advance. “

Multi-atlas approaches are also presently possible, but we believe HippUnfold can apply unfolding and subfield definition with even higher validity. Unfolding of the hippocampus was previously possible in-vivo but still showed limited intersubject alignment. The present work validates a novel alignment method ex-vivo, and now additionally shows that this can be translated to better alignment even at the resolution of in-vivo imaging. We hope the above new Discussion paragraph also helps to clarify this.

4) A minor comment is that there are three panels (a,b,c) in Figure 4 but the figure legend does not describe them separately.

We thank the Reviewer, and added a Figure legend for parts B and C.

Author Response

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

We thank the reviewers for these helpful and thoughtful comments.

Reviewer #1 (Recommendations For The Authors):

Major comments:

• What was the nature of the 0.1 increase in pH caused by illumination in CheRiff-negative cells? Is this thought to be a temperature effect?

The increase in pHoran4 fluorescence in CheRiff-negative cells is most likely not from a pH change; rather, it most likely reflects blue light-mediated photoactivation of the mOrange-derived chromophore in pHoran4. Similar photoartifacts have been reported in other fluorescent protein reporters (see e.g. Farhi, Samouil L., et al. "Wide-area all-optical neurophysiology in acute brain slices." Journal of Neuroscience 39.25 (2019): 4889-4908.).

The baseline measurement in CheRiff-negative cells is to control for this type of artifact. We subtract the mean signal from the CheRiff-negative cells to correct the signals from the CheRiff-positive cells, as described in the Main Text.

• Does Kir2.1 have a proton conductance? Was the resting pH of HEK cells changed by Kir2.1 expression? Fig 2D suggest basal pH is equivalent +/- Kir2.1 but it would be good to show that data.

This is an interesting question which our data do not answer conclusively. Since we used an intensiometric (as opposed to ratiometric) pH indicator, our measurements only provide relative pH changes. We assumed a constant initial pH. We have revised the text to make clear that this is an assumption.

Prior studies of pH-dependent Kir2.1 activity did not find evidence of a proton current (i.e. no change in current upon extracellular acidification), though the channel is closed by intracellular acidification. See: Ye, Wenlei, et al. "The K+ channel KIR2. 1 functions in tandem with proton influx to mediate sour taste transduction." Proceedings of the National Academy of Sciences 113.2 (2016): E229-E238. We added this information to the text.

The pKa of pHoran4 is 7.5, so a decrease in initial pH would decrease the slope of F vs pH. We observed higher (absolute value) F/F in the Kir2.1 expressing cells than in the non-expressing cells, confirming that the Kir2.1-expressing cells had larger CheRiff-mediated acidification than the Kir2.1-negative cells (Figure 2D). Thus this conclusion remains true regardless of whether Kir2.1 has a proton conductance.

What channels/transporter mediate proton flux in CheRiff + Kir2.1 experiments? Is the increased proton flux simply due to more H+ ions passing through CheRiff when cells are hyperpolarized or may other voltage-dependent processes effect pH?

Fig. 2G-M address this question, specifically. We targeted the blue light in a “zebra” pattern to only activate CheRiff in a subset of cells. We then used voltage imaging to show that the induced voltage spread over a much wider area than the blue-illuminated region, due to gap junction coupling between the cells. If protons flowed through some voltage-dependent channel other than CheRiff, then we would expect the acidification to follow the voltage profile. If protons primarily flowed through the CheRiff, then we would expect the acidification to follow the illumination profile. Fig. 2K and the following quantification show clearly that the acidification followed the illumination profile, and hence the proton current was primarily through CheRiff.

• Is Kir2.1 included in the spatial illumination experiments (Fig. 2G-M)? If so, it would be helpful to note it. The color scheme suggest it is but it would be good to note it explicitly.

Yes. Clarified in text.

• Why is the acidification caused by 10 second of illumination smaller in Fig 2L, as compared to the equivalent experiment in 2D? Is this due to the spatial nature of the illumination? It seems that the pH change at the site of illumination should be equivalent between these 2 experiments.

The illumination protocol between the two experiments has different duty cycles (compare Fig. 2C and 2J), so the time-averaged intensity is different. There can also be batch-to-batch variation in CheRiff expression which would alter the proton flux and thus pH change. To control for this, comparisons were always made between batches of cells prepared together.

• The authors used 150 second illumination to examine pH changes but only 13.5 seconds to differentiate between pH changes caused by the light-activated conductance and those secondary to depolarization. Would pH changes lose their spatial limitations if a similar 150 second illumination was used? This is important because the pH change seen in the "Blue On" region was quite small.

Yes, protons can diffuse between cells via gap junctions, smoothing out the spatial structure of the pH over long times. See e.g. Wu, Ling, et al. "PARIS, an optogenetic method for functionally mapping gap junctions." Elife 8 (2019): e43366.

We used a short (13.5 s) protocol specifically to distinguish CheRiff-mediated acidification from acidification via other conductances in electrically coupled neighboring cells. If we had waited for longer, lateral proton diffusion could have muddied the interpretation of these experiments.

• How long do action potentials shown in between illuminations in Fig 4H (ChR2 3M) last following cessation of illumination?

The closing time, τoff, of the Channelrhodopsins are shown in Table 1. The ChR2-3M has an off-time of almost 2 seconds. The duration of post-stimulus persistent firing is expected to depend on the expression level of the ChR2-3M, the strength of the optogenetic stimulus and the excitation threshold of the neurons, i.e. on how far above threshold the neuron is at the moment the blue light turns off. Thus we expect the post-stimulus firing time to be highly variable between cells and also to depend on optogenetic stimulus strength. In our experiments action potentials were observed throughout the 0.5 s dark interval between stimuli.

• While ChR2-3M construct may have promise for therapeutic applications, those strengths limit its use or basic science applications like circuit mapping. This should be noted in the discussion.

Ok. We now mention this in the discussion.

• Please define EPD50 within the text of the results section.

Ok. Fixed.

Reviewer #2 (Recommendations For The Authors):

This is an interesting manuscript investigating a potential limitation of optogenetic manipulation of cell excitability and its solution. The work is conducted rigorously and explained clearly. I only have minor concerns:

I think the impact of the study could be broadened by examining additional proton permeable opsins for their effects on intracellular pH. A single assay could be used to compare different opsins to CheRiff and show that the problem of intracellular acidification is not limited to CheRiff.

Yes, this is interesting. There are so many opsins and illumination protocols in use that we could not do an exhaustive characterization; we encourage people to test their own opsin under their conditions if doing chronic simulation. The plasmid constructs used for this work are available on Addgene.

I am not clear on what Figure S3A is showing because I cannot see a patterning like the one shown in Fig. 2H. Perhaps a higher magnification could solve the problem.

Figure S3A does not have the zebra-striped pattern of Figure 2H. In Fig S3A, we used just one column of illumination. The point was to test the ability of each opsin to depolarize the HEK cells. We added images of the illumination pattern and adjusted the caption to make this clear.

When discussing the sustained photocurrent of PsCatCh2.0, a reference to Govorunova et al. J. Biol. Chem. 2013 should be added as the low extent of light induced inactivation appears to be, at least in part, a characteristic of the particular type of opsin from P. subcordiformis.

Added reference.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

Please describe the criteria for binocularity of dLGN neurons, and what % of recorded neurons meet this criteria. Do all the example neurons in figure 1D meet the criteria for binocular neurons?

We now include criteria for binocularity of dLGN neurons in the methods section on page 24, and mention the percentage of binocular neurons that we detected. We also indicate which of the example neurons in figure 1D are monocular or binocular according to these criteria. We would like to stress that these percentages are not representative for the level of binocularity in dLGN as a whole, as our recordings were limited to the frontal ipsilateral projection zone of dLGN, which is its most binocular region, and only units with a receptive field within 30o from the center were included in the analysis. We mention this in the discussion on page 23.

Fig 1: Please perform statistical comparison of data presented in Figure 1c by genotype, as in other figures.

We conducted post-hoc Tukey's tests exclusively when a significant interaction between phenotype and genotype was detected in the two-way ANOVA (as seen in Figs. 2B and 3E). This decision was made because interpreting a significant post-hoc test becomes uncertain when there is no interaction, which is evident in Fig. 1C. In that case, the posthoc Tukey's test yielded a p-value of 0.044 for the difference in RF size between KO NOMD and KO MD, while all other comparisons were not significant (WT NO-MD vs WT MD: P=0.15, WT NO-MD vs KO NO-MD: p=0.99, WT MD vs KO MD: p=0.21). However, since there was no significant interaction between genotype and phenotype, we cannot conclude that there is an effect in KO mice that is absent in WT mice. In Fig. 3B, all posthoc Tukey's tests resulted in P-values greater than 0.05.

Fig 1e: There is no justification for splitting the data into two time epochs before and after 150 msec. A repeated measures anova of smaller time bins across the full time course would be more effective/appropriate here.

The reviewer is correct. We have now performed a repeated measures ANOVA.

Fig 2: GABA a1R KO results in a loss/absence of OD plasticity, not a reduction

We agree. We have changed the wording.

Fig 3: Please be specific about the location of V1 recordings. Was layer-specificity determined?

The location of V1 recordings is mentioned in the methods section under “Electrophysiology recordings, visual stimulation and V1 silencing”, page 23. We have assessed OD per depth, but found that we do not have sufficient units to draw any conclusions about differences in plasticity per layer.

Why is feedback from V1 more influential in dLGN OD plasticity in KO?

We believe this is because the reduced thalamic inhibition causes the excitation/inhibition ratio to shift in favor of excitation. We discuss this more extensively on page 19 of the discussion.

Fig 4: Inclusion of a GABA R antagonist protects thalamic axons from muscimol silencing (Liu BH, Wu GK, Arbuckle R, Tao HW, Zhang LI. Defining cortical frequency tuning with recurrent excitatory circuitry. Nat. Neurosci. 2007;10:1594-600.)

We now mention the possible direct influence of muscimol on thalamic axons in the discussion on page 19 and cite the suggested article.

The observation that feedback from primary visual cortex does not contribute to adult visual thalamus plasticity is interesting and important. The authors should expand on their discussion of this observation to include changes in cortical circuitry that may help to explain this observation.

We have expanded this part of the discussion on page 20.

The authors should describe the pathway by which inhibition enables plasticity in dLGN.

We discuss this more extensively on page 17 in the updated manuscript.

Reviewer #2:

1) The current work was basically a follow-up of a previous study in juvenile mice, and the results were also very similar to the juvenile results (Sommeijer et al., 2017). One possible interpretation of the results is that the lack of OD plasticity in adult V1 and dLGN was caused by an early blockade of the development of the inhibitory circuit in dLGN, which retains the dLGN in an immature stage till adulthood. The authors indeed claimed in the discussion that the 2-day OD shift is intact in juvenile dLGN and V1 in KO mice, and provided evidence in supplementary figure that GABAergic and cholinergic synapse amount are similar between WT and KO mice. However, the 7-day OD shift is indeed defected in juvenile V1 and dLGN in KO mice (Sommeijer et al., 2017), and it is possible that this early functional deficit didn't induce a structural remodeling in adulthood. To better support the author's claim that the lack of adult V1 OD plasticity is specifically due to reduced dLGN synaptic inhibition, the author should generate conditional KO mice that dLGN synaptic inhibition was only interfered in adulthood.

In order to address this criticism it is important to discuss the plasticity deficits in dLGN and V1 separately.

Concerning V1 plasticity: We have previously shown that brief MD induces an OD shift in V1 of mice lacking thalamic synaptic inhibition in dLGN. OD plasticity induced by brief MD is a hallmark of critical period plasticity in V1, and it thus seems highly unlikely that critical period onset in V1 is defective or that development of V1 is halted in an immature state that does not support OD plasticity in thalamus-specific GABRA1 deficient mice.

The observed plasticity deficit during the critical period was limited to the second stage of the OD shift in V1, which requires long-term monocular deprivation. The straightforward explanation for this result and our current findings is that both during the critical period and in adulthood, the second stage of OD plasticity in V1 induced by long-term monocular deprivation requires thalamic plasticity or inhibition. The proposed alternative, that lack of thalamic synaptic inhibition during development results in a possible lack of structural change in V1 that would cause a lifelong deficiency selectively affecting OD plasticity induced by long-term monocular deprivation, requires many more assumptions.

Concerning dLGN plasticity: The simplest explanation for the observed lack of OD plasticity in dLGN is that it is a direct consequence of the absence of synaptic inhibition in the KO mice. However, an alternative explanation could indeed be that dLGN is kept in an immature (pre-critical period-like) state due to the developmental absence of synaptic inhibition. This situation would be analogous to that in V1 of GAD65 deficient mice (which have reduced GABA release), in which OD plasticity cannot be induced by brief monocular deprivation during the critical period or in adulthood (Fagiolini and Hensch, 2000). Because this deficit can be reversed by treating the mice with benzodiazepines (allosteric modulators of GABA receptors) at any age, it is thought that development of V1 in GAD65 mice is halted in a pre-critical period-like state until inhibition is strengthened. We cannot exclude that something similar occurs in dLGN of mice lacking thalamic synaptic inhibition, although we did not observe any changes in hallmarks of dLGN maturity, such as reduced receptive field size, and increased cholinergic and inhibitory bouton densities.

However, if the analogy with the developmental deficit in V1 of GAD65 deficient mice is valid, the reduced plasticity is still likely to be a direct consequence of reduced inhibition. In GAD65 deficient mice, long term monocular deprivation during the critical period causes a full OD shift, showing that no additional deficits (besides reduced inhibition) limit OD plasticity in V1 of these mice (Gagiolini and Hensch 2000). And, as already mentioned, increasing inhibition rescues OD plasticity in GAD65 KO mice. Thus, the immature state of V1 in these mice is probably nothing more than a situation in which inhibition tone is too low to support efficient OD plasticity. In dLGN, knocking out GABRA1 at a later age could therefore also create a situation in which inhibition is too low to support thalamic OD plasticity, which is not different from the situation in which the gene is inactivated at birth. Only if lack of synaptic inhibition in thalamus affects another, unknown developmental process that is of importance later in life to support OD plasticity in dLGN, the proposed experiment would result in a different outcome. We are not convinced that this scenario is likely enough to justify repeating most of this study, but now using mice in which GABRA1 is inactivated in dLGN through bilateral AAV-cre injections.

Independently of the exact cause of the plasticity deficit in dLGN, our results make clear that a cortical plasticity deficit in adulthood can have a thalamic origin, which we believe is an important insight that is highly relevant.

We have included part of these arguments in the discussion on page 17.

2) The authors found that in juveniles, dLGN OD shift is dependent on V1 feedback, but not in adults. However, a recent work showed that the effects of V1 silencing on dLGN OD plasticity could differ with various starting points and duration of the V1 silencing and MD (Li et al., 2023). Could the authors provide more details of the MD and V1 silencing for an in-depth discussion?

We discuss some of the findings of the Li et al paper on pages 16 and 20 of the manuscript now.

Author Response

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

Reviewer #1 (Public Review):

Meta-cognition, and difficulty judgments specifically, is an important part of daily decision-making. When facing two competing tasks, individuals often need to make quick judgments on which task they should approach (whether their goal is to complete an easy or a difficult task).

In the study, subjects face two perceptual tasks on the same screen. Each task is a cloud of dots with a dominating color (yellow or blue), with a varying degree of domination - so each cloud (as a representation of a task where the subject has to judge which color is dominant) can be seen an easy or a difficult task. Observing both, the subject has to decide which one is easier.

It is well-known that choices and response times in each separate task can be described by a driftdiffusion model, where the decision maker accumulates evidence toward one of the decisions (”blue” or ”yellow”) over time, making a choice when the accumulated evidence reaches a predetermined bound. However, we do not know what happens when an individual has to make two such judgments at the same time, without actually making a choice, but simply deciding which task would have stronger evidence toward one of the options (so would be easier to solve).

It is clear that the degree of color dominance (”color strength” in the study’s terms) of both clouds should affect the decision on which task is easier, as well as the total decision time. Experiment 1 clearly shows that color strength has a simple cumulative effect on choice: cloud 1 is more likely to be chosen if it is easier and cloud 2 is harder. Response times, however, show a more complex interactive pattern: when cloud 2 is hard, easier cloud 1 produces faster decisions. When cloud 2 is easy, easier cloud 1 produces slower decisions.

The study explores several models that explain this effect. The best-fitting model (the Difference model is the paper’s terminology) assumes that the decision-maker accumulates evidence in both clouds simultaneously and makes a difficulty judgment as soon as the difference between the values of these decision variables reaches a certain threshold. Another potential model that provides a slightly worse fit to the data is a two-step model. First, the decision maker evaluates the dominant color of each cloud, then judges the difficulty based on this information.

Thank you for a very good summary of our work.

Importantly, the study explores an optimal model based on the Markov decision processes approach. This model shows a very similar qualitative pattern in RT predictions but is too complex to fit to the real data. It is hard to judge from the results of the study how the models identified above are specifically related to the optimal model - possibly, the fact that simple approaches such as the Difference model fit the data best could suggest the existence of some cognitive constraints that play a role in difficulty judgments.

The reviewer asks “how the models identified above are specifically related to the optimal model”. We did fit the four models to simulations of the optimal model and found that the Difference model was the closest. However, we did not fit the parameters of the optimal model to the data (no easy feat given the complexity of the model) as the experiment was not designed to incentivize maximization of the reward rate and fitting would have been computationally laborious. We therefore focused on the qualitative features of the optimal model and how they compare to our models. We now also include the optimal model for the known color dominance RT experiment (line 420). We have also added a new paragraph in the Discussion on the optimal model at line 503 comparing it qualitatively to the Difference model.

The Difference model produces a well-defined qualitative prediction: if the dominant color of both clouds is known to the decision maker, the overall RT effect (hard-hard trials are slower than easyeasy trials) should disappear. Essentially, that turns the model into the second stage of the twostage model, where the decision maker learns the dominant colors first. The data from Experiment 2 impressively confirms that prediction and provides a good demonstration of how the model can explain the data out-of-sample with a predicted change in context.

Overall, the study provides a very coherent and clean set of predictions and analyses that advance our understanding of meta-cognition. The field would benefit from further exploration of differences between the models presented and new competing predictions (for instance, exploring how the sequential presentation of stimuli or attentional behavior can impact such judgments). Finally, the study provides a solid foundation for future neuroimaging investigations.

Thank you for your positive comments and suggestions.

Reviewer #2 (Public Review):

Starting from the observation that difficulty estimation lies at the core of human cognition, the authors acknowledge that despite extensive work focusing on the computational mechanisms of decision-making, little is known about how subjective judgments of task difficulty are made. Instantiating the question with a perceptual decision-making task, the authors found that how humans pick the easiest of two stimuli, and how quickly these difficulty judgments are made, are best described by a simple evidence accumulation model. In this model, perceptual evidence of concurrent stimuli is accumulated and difficulty is determined by the difference between the absolute values of decision variables corresponding to each stimulus, combined with a threshold crossing mechanism. Altogether, these results strengthen the success of evidence accumulation models, and more broadly sequential sampling models, in describing human decision-making, now extending it to judgments of difficulty.

The manuscript addresses a timely question and is very well written, with its goals, methods and findings clearly explained and directly relating to each other. The authors are specialists in evidence accumulation tasks and models. Their modelling of human behaviour within this framework is state-of-the-art. In particular, their model comparison is guided by qualitative signatures which are diagnostic to tease apart the different models (e.g., the RT criss-cross pattern). Human behaviour is then inspected for these signatures, instead of relying exclusively on quantitative comparison of goodness-of-fit metrics. This work will likely have a wide impact in the field of decisionmaking, and this across species. It will echo in particular with many other studies relying on the similar theoretical account of behaviour (evidence accumulation).

Thank you for these generous comments.

A few points nevertheless came to my attention while reading the manuscript, which the authors might find useful to answer or address in a new version of their manuscript.

1) The authors acknowledge that difficulty estimation occurs notably before exploration (e.g., attempting a new recipe) or learning (e.g., learning a new musical piece) situations. Motivated by the fact that naturalistic tasks make difficult the identification of the inference process underlying difficulty judgments, the authors instead chose a simple perceptual decision-making task to address their question. While I generally agree with the authors’s general diagnostic, I am nevertheless concerned so as to whether the task really captures the cognitive process of interest as described in the introduction. As coined by the authors themselves, the main function of prospective difficulty judgment is to select a task which will then ultimately be performed, or reject one which won’t. However, in the task presented here, participants are asked to produce difficulty judgments without those judgements actually impacting the future in the task. A feature thus key to difficulty judgments thus seems lacking from the task. Furthermore, the trial-by-trial feedback provided to participants also likely differ from difficulty judgments made in real world. This comment is probably difficult to address but it might generally be useful to discuss the limitations of the task, in particular in probing the desired cognitive process as described in introduction. Currently, no limitations are discussed.

We have added a Limitations paragraph to the Discussion and one item we deal with is the generalization of the model to more complex tasks (line 539).

2) The authors take their findings as the general indication that humans rely on accumulation evidence mechanisms to probe the difficulty of perceptual decisions. I would probably have been slightly more cautious in excluding alternative explanations. First, only accumulation models are compared. It is thus simply not possible to reach a different conclusion. Second, even though it is particularly compelling to see untested predictions from the winning model in experiment #1 to be directly tested, and validated in a second experiment, that second experiment presents data from only 3 participants (1 of which has slightly different behaviour than the 2 others), thereby limiting the generality of the findings. Third, the winning model in experiment #1 (difference model) is the preferred model on 12 participants, out of the 20 tested ones. Fourth, the raw BIC values are compared against each other in absolute terms without relying on significance testing of the differences in model frequency within the sample of participants (e.g., using exceedance probabilities; see Stephan et al., 2009 and Rigoux et al., 2014). Based on these different observations, I would thus have interpreted the results of the study with a bit more caution and avoided concluding too widely about the generality of the findings.

Thank you for these suggestions.

i) We have now make it clear in the Results (line 126) that all four models we examine are accumu-lation models. In addition, we have added a paragraph on Limitations (line 530) in the Discussion where we explain why we only consider accumulation models and acknowledge that there are other non-accumulation models.

ii) Each of three participants in Experiment 2 performed 18 sessions making it a large and valuabledataset necessary to test our hypothesis. We have now included a mention of the the small number of participants in Experiment 2 in a Limitations paragraph in the Discussion (line 539).

iii) As suggested, we have now calculated exceedance probabilities for the 4 models which gives[0,0.97,0.03,0]. This shows that there is a 0.97 probability of the Difference model being the most frequent and only a 0.03 probability of the two-step model. We have included this in the results on line 237.

3) Deriving and describing the optimal model of the task was particularly appreciated. It was however a bit disappointing not to see how well the optimal model explains participants behaviour and whether it does so better than the other considered models. Also, it would have been helpful to see how close each of the 4 models compared in Figures 2 & 3 get to the optimal solution. Note however that neither of these comments are needed to support the authors’ claims.

The reviewer asks how close each of the four models is to the optimal solution. We did fit the four models to simulations of the optimal model and found that the Difference model was the closest. However, we did not fit the parameters of the optimal model to the data (no easy feat given the complexity of the model) as the experiment was not designed to incentivize maximization of the reward rate and fitting would have been computationally laborious. We therefore focused on the qualitative features of the optimal model and how they compare to our models. We now also include the optimal model for the known color dominance RT experiment (line 420). We have also added a new paragraph in the Discussion on the optimal model at line 503 comparing it qualitatively to the Difference model.

4) The authors compared the difficulty vs. color judgment conditions to conclude that the accumulation process subtending difficulty judgements is partly distinct from the accumulation process leading to perceptual decisions themselves. To do so, they directly compared reaction times obtained in these two conditions (e.g. ”in other cases, the two perceptual decisions are almost certainly completed before the difficulty decision”). However, I find it difficult to directly compare the ’color’ and ’difficulty’ conditions as the latter entails a single stimulus while the former comprises two stimuli. Any reaction-time difference between conditions could thus I believe only follow from asymmetric perceptual/cognitive load between conditions (at least in the sense RT-color < RT-difficulty). One alternative could have been to present two stimuli in the ’color’ condition as well, and asking participants to judge both (or probe which to judge later in the trial). Implementing this now would however require to run a whole new experiment which is likely too demanding. Perhaps the authors could instead also acknowledge that this a critical difference between their conditions, which makes direct comparison difficult.

We feel we can rule out that participants make color decisions (as in the color task) to make difficulty decisions. For example, making a color choice for 0% color strength takes longer than a difficulty choice for 0:52% color strengths. Thus, the difficulty judgment does not require completion of the color decisions. Therefore, average reaction time for a single color patch (C𝑆1) can be longer than the reaction time for the difficulty task which contains the same coherence (C𝑆1) for one of the patches. This is true despite the difficulty decision requiring monitoring of two patches (which might be expected to be slower than monitoring one patch). We have added this in to the Discussion at line 449.

Reviewer #3 (Public Review):

The manuscript presents novel findings regarding the metacognitive judgment of difficulty of perceptual decisions. In the main task, subjects accumulated evidence over time about two patches of random dot motion, and were asked to report for which patch it would be easier to make a decision about its dominant color, while not explicitly making such decision(s). Using 4 models of difficulty decisions, the authors demonstrate that the reaction time of these decisions are not solely governed by the difference in difficulties between patches (i.e., difference in stimulus strength), but (also) by the difference in absolute accumulated evidence for color judgment of the two stimuli. In an additional experiment, the authors eliminated part of the uncertainty by informing participants about the dominant color of the two stimuli. In this case, reaction times were faster compared to the original task, and only depended on the difference between stimulus strength.

Overall, the paper is very well written, figures and illustrations clearly and adequately accompanied the text, and the method and modeling are rigor.

The weakness of the paper is that it does not provide sufficient evidence to rule out the possibility that judging the difficulty of a decision may actually be comparing between levels of confidence about the dominant color of each stimulus. One may claim that an observer makes an implicit color decision about each stimulus, and then compares the confidence levels about the correctness of the decisions. This concern is reflected in the paper in several ways:

We tested a Difference in confidence model (line 315) in the orginal paper and showed it was inferior to the Difference model. We did this for experiment 2, RT task so that we could fit the unknown color condition and try to predict the known color condition. To emphasize this model (which we think the reviewer may have missed) we have moved the supplementary figure to the main results (now Fig. 6) as we think it is very cool that we were able to discard the confidence model.

When comparing the confidence model to the Difference we found the difference model was pre-Δ ferred with BIC of 38, 56, 47. We are unsure why the reviewer feels this “does not provide sufficient evidence to rule out the possibility that judging the difficulty of a decision may actually be comparing between levels of confidence about the dominant color of each stimulus.” We regard this as strong evidence.

1) It is not clear what were the actual instructors to the participants, as two different phrasings appear in the methods: one instructs participants to indicate which stimulus is the easier one and the other instructs them to indicate the patch with the stronger color dominance. If both instructions are the same, it can be assumed that knowing the dominant color of each patch is in fact solving the task, and no judgment of difficulty needs to be made (perhaps a confidence estimation). Since this is not a classical perceptual task where subjects need to address a certain feature of the stimuli, but rather to judge their difficulties, it is important to make it clear.

We now include the precise words used to instruct the participant (line 604): “Your task is to judge which patch has a stronger majority of yellow or blue dots. In other words: For which patch do you find it easier to decide what the dominant color is? It does not matter what the dominant color of the easier patch is (i.e., whether it is yellow or blue). All that matters is whether the left or right patch is easier to decide”.

Knowing both colors or the dominant color is not sufficient to solve the task. Knowing both are yellow does not tell you which has more yellow which is what you need to estimate to solve the task. Again, we tested a confidence model in the original version of the paper and showed it was a poor model compared to the Difference model.

2) Two step model: two issues are a bit puzzling in this model. First, if an observer reaches a decision about the dominant color of each patch, does it mean one has made a color decision about the patches? If so, why should more evidence be accumulated? This may also support the possibility that this is a ”post decision” confidence judgment rather than a ”pre decision” difficulty judgment. Second, the authors assume the time it takes to reach a decision about the dominant color for both patches are equal, i.e., the boundaries for the ”mini decision” are symmetrical. However, it would make sense to assume that patches with lower strength would require a longer time to reach the boundaries.

In the Two-step model we assume a mini decision is made for the color of each stimulus. However, the assumption is that this is made with a low bound so it is not a full decision as in a typical color decision. Again estimating the colors from the mini decision does not tell you which is easier so you need to accumulate more evidence to make this judgment. In fact the Race model is a version of the two step in which no further accumulation is made after the initial decision and this model fits poorly (we now explain this on line 185). We assume for simplicity that the first stimulus to cross a bound triggers both mini color decisions. So although the bounds are equal the one with stronger color dominance is more likely to hit the bound first.

We have already addressed this concern about the comparison with confidence above.

3) Experiment 2: the modification of the Difference model to fit the known condition (Figure 5b),can also be conceptualized as the two-step model, excluding the ”mini” color decision time. These two models (Difference model with known color; two-step model) only differ from each other in a way that in the former the color is known in advance, and in the second, the subject has to infer it. One may wonder if the difference in patterns between the two (Figure 3C vs. Figure 6B) is only due to the inaccuracies of inferring the dominant color in the two-step model.

In Experiment 2 the participant is explicitly informed as to the color dominance of both stimuli. Therefore, assuming the two-step model skips the first step and uses this explicit information in the second step, the difference and two-step model are identical for modeling Experiment 2. We explain this now on line 277.

As the reviewer suggests, differences in predictions between the Difference and Two-step arise from trials in which there is a mismatch between the inferred dominant colors from the two-step model and the color associated with the final DVs in the Difference model. We now explain this on line 187. We do not see this as a problem of any sort but just defines the difference between the models. Note that the new exceedance analysis now strongly supports the Difference model as the most common model among the participants.

An additional concern is about the controlled duration task: Why were these specific durations chosen (0.1-1.65 sec; only a single duration was larger than 1sec), given the much longer reaction times in the main task (Experiment 1), which were all larger on average than 1sec? This seems a bit like an odd choice. Additionally, difficulty decision accuracies in this version of the task differ between known and unknown conditions (Figure 7), while in the reaction time version of the same task there were no detectable differences in performance between known and unknown conditions (Figure 6C), just in the reaction times. This discrepancy is not sufficiently explained in the manuscript. Could this be explained by the short trial durations?

The reviewer asks about the choice of stimulus durations in Experiment 2. First, RTs in Experiment 1 do not only reflect the time needed to make decisions but also contain non-decision times (0.23-0.47 s). So to compare decision time in RT and controlled duration experiment one must subtract the non-decision time from the RTs (the non-decision time is not relevant to the controlled duration experiment). Second, the model specifically predicts that differences in performance between the known and unknown color dominance conditions are largest for short duration stimulus presentation trials (see Fig. 7). We explain this on line 346. For long durations, performance pretty much plateaus, and many decisions have already terminated (Kiani 2008). We sample stimulus durations from a discrete truncated exponential distribution to get roughly equal changes in accuracy between consecutive durations (which we now explain at line 345).

Group consensus review

The reviewers have discussed with each other, and they have discussed a series of revisions which, if carried out, would make their evaluation of your paper even more positive. I outline them below in case you would be interested in revising your paper based on these reviews. You will see below that the reviewers share overall a quite positive evaluation of your study. All three limitations described in the Public Reviews could be addressed explicitly in the discussion which for the moment is limited to description and generalization of findings.

1) The model selection procedure should be amended and strengthened to provide clearer results. As noted by one of the reviewers during the consultation session, ”the Difference model just barely wins over the two-step model, and the two-step model might produce the same prediction for the next experiment.” You will also see below that Reviewer #2 provides guidance to improve the model selection process: ”[...] the second experiment presents data from only 3 participants (1 of which has slightly different behaviour than the 2 others), thereby limiting the generality of the findings. Third, the winning model in experiment #1 (difference model) is the preferred model on 12 participants, out of the 20 tested ones. Fourth, the raw BIC values are compared against each other in absolute terms without relying on significance testing of the differences in model frequency within the sample of participants (e.g., using exceedance probabilities; see Stephan et al., 2009 and Rigoux et al., 2014).” Altogether, model selection appears currently to be the ’weakest’ part of the paper (Difference model vs. Two-step model, model comparison, how to better incorporate the optional model with the other parts). It would be great if you would improve this section of the Results.

Thank you for these suggestions.

i) We have now make it clear in the Results (line 126) that all four models we examine are accumu-lation models. In addition, we have added a paragraph on Limitations (line 530) in the Discussion where we explain why we only consider accumulation models and acknowledge that there are other non-accumulation models.

ii) Each of three participants in Experiment 2 performed 18 session making it a large and valuabledataset necessary to test our hypothesis. We have now included a mention of the the small number of participants in Experiment 2 in a Limitations paragraph in the Discussion (line 539).

iii) We have now calculated exceedance probabilities for the 4 models which gave [0,0.97,0.03,0]. This shows that there is a 0.97 probability of the Difference model being the most frequent and only a 0.03 probability of the two-step model. We have included this in the results on line 237.

2) All reviewers have noted that the relation of the optimal model with the human data and theother models should be clarified and discussed in a revised version of the manuscript. You will find their specific comments in their individual reviews, appended below.

We now include the optimal model for the known color dominance RT experiment (line 420). We have also added a new paragraph in the Discussion on the optimal model at line 503 comparing it to the Difference model.

3) Finally, the exclusion strategy is also unclear at the moment and should be clarified and discussed explicitly somewhere in a revised version of the manuscript. Reviewers were wondering why so many participants were excluded from Experiment 1, and only 3 participants were included in Experiment 2. This should also be clarified better in the manuscript.

We have clarified the exclusion criteria in the Methods at line 651 as a new subsection.

The data quality problem with MTurk is well documented (Chmielewski, M & Kucker SC. 2020. An MTurk Crisis? Shifts in Data Quality and the Impact on Study Results. Social Psychological and Personality Science, 11, 464-473). Given that this was an online experiment on MTurk, it is hard to know exactly why some participants showed low accuracy, but it’s likely that some may have misunderstood the instructions in the difficulty task or they may have been unmotivated to do well in this highly repetitive task. Either reason would be problematic for our model comparisons that are based on choice-RT patterns. Note that the cut-offs we chose for inclusion were purely based on accuracy, whereas the modeling approach considered RTs, which importantly were not used as a inclusion criterion (see revised methods). Moreover, accuracy cut-offs were fairly lenient and mainly aimed to exclude participants who appeared to be guessing/misunderstood instructions (for reference: mean sensitivity of participants who were included was 2x higher than the cut-offs we used).

Each of three participants in Experiment 2 performed 18 session making it a large and valuable dataset necessary to test our hypothesis. We have now included a mention of the the small number of participants in Experiment 2 in a Limitations paragraph in the Discussion (line 539).

Reviewer #1 (Recommendations For The Authors):

Thank you for an excellent paper, I enjoyed reading it a lot. I have a few questions that could potentially clarify some aspects for the reader.

(1) It seems from the model fit plots (Figure 3) that the RT predictions of the model tend to overshoot in cases where one of the clouds is very easy. Could you include potential interpretations of this effect?

We assume the reviewer is examining the Difference Model (i.e. the preferred model) panel when commenting on the overshoot. It is true the predictions for the highest coherence (bottom purple line) for RT is above the data but it is barely outside the data errorbars of 1 s.e. To be honest we regard this as a pretty good fit and would not want to over-interpret this small mismatch.

(2) On page 4, around line 121, the study discusses the ”criss-crossing” effect in the RT data. You mention that the fact that RTs are long in hard-hard trials compared to easy-easy trials could be important here: ”These tendencies lead to a criss-cross pattern..”. It is confusing since, for instance, the race model does not have a criss-cross, but still exhibits the overall effect. I was intrigued bythe criss-crossing, and after some quick simulations, I found that the equation RT2 ∗ = 2 − 2 ∗ Cs12 − Cs22 + 6 ∗ (Cs1 ∗ Cs2)2 can (very roughly) replicate Figure 1d (bottom panel), so it seems that the criss-crossing effect must be produced by some interactive effect of color strengths on RTs. I wonder if you could provide a better explanation of how this interactive effect is generated by the model, given that it is the main interesting finding in the data. I believe at this point the intuition is not well-outlined.

The criss cross arises through an interaction of the coherences as the reviewer suspects. That is, for the Difference model the RT related to abs(|Coh1|- |Coh2|). If we replace the first abs with a square we get

|coh1|2 + |coh2|2 − 2|coh1||coh2|

The larger this is, the smaller the RT so

RT = constant − coh12 − coh22 + 2|coh1||coh2|

which is very similar to the formula the reviewer mentions.

We now supply an intuition as to why the criss-cross arises in the Difference model (line 167). We do not get a criss-cross in the race model, because there the RT is determined by the Race that that reaches a bound first. Because the races are independent, RTs will be fastest when coherence is high for either stimuli.

(3) Am I wrong in my intuition that the two-step model would produce very similar predictions as the Difference model for Experiment 2? It would be great to discuss that either way since the twostep model seems to produce very close quantitative and pretty much the same qualitative fit to the data of Experiment 1.

In Experiment 2 the participant is explicitly informed about the color dominance of both stimuli. Therefore, assuming the two-step model skips the first step and uses this explicit information in the second step, the difference and two-step model are identical for modeling Experiment 2. We explain this now on line 277.

(4) The inclusion of the optimal model is great. It would be beneficial to provide some more connections to the rest of the paper here. Would this model produce similar predictions for Experiment 2, for instance?

We now include the optimal model for the known color dominance RT experiment (line 420). We have also added a new paragraph in the Discussion on the optimal model at line 503 comparing it to the Difference model.

(5) In the Methods, it is quite striking that out of 51 original participants, most were excluded and only 20 were studied. It is not easy to trace through this section why and how and who was excluded, so it would be great if this information was organized and presented more clearly.

We have clarified this in the Methods at line 651 as a new subsection in the Methods. We also explain that exclusion was not made on RT data which is our main focus in the models.

Reviewer #2 (Recommendations For The Authors):

• As detailed in the ’public review’, a more cautious discussion, notably delineating the limitations of the study would be appreciated.

• In their models, the authors assume that participants sequentially allocate attention between the two stimuli, alternating between them. Did the authors test this assumption and did they consider the possibility that participants could sample from both stimuli in parallel? In particular, does the conclusion of the model comparison also holds under this parallel processing assumption?

Our results are not affected by whether participants sample the stimulus sequentially through alternation or in a parallel manner (Kang et al., 2021). What does change is the parameters of the model (but not their predictions/fits). In the parallel model, information is acquired at twice the rate of the serial model. We can, therefore, obtain the parameters of parallel models (that has serial and parallel models): 𝜅𝑝 = 𝜅𝑠/√2, 𝑢𝑝 = 𝑢𝑠√2, 𝑎𝑝 = 𝑎𝑠/2 and 𝑑𝑝 = 2𝑑𝑠 (Eq. 2). We now explain𝑠 𝑝 identical predictions to the serial model) directly from the parameters of the current sequential models simply by adjusting the parameters that depend on the time scale (subscripts and for this on line 518.

• I found the small paragraph corresponding to lines 193-196 particularly difficult to understand. If the authors could think of a better way to phrase their claim, it would probably help.

We have rewritten this paragraph at line 211

• I found a type on line 122: ”wheres” instead of ”whereas”.

Corrected

• I found a type on line 181: ”or” instead of ”of”.

Yes corrected

• Figure #2 is extremely useful in understanding the models and their differences, make sure it remains after addressing the reviews!

Thank you, this figure is retained.

Reviewer #3 (Recommendations For The Authors):

All comments are detailed in the public review, with some clarifications here:

1) The confusing instructions to the participants are detailed here: under ”overview of experimental tasks” in the methods it says: ”They were instructed... to indicate whether the left or right stimulus was the easier one” (line 520), and below it ”they were required to indicate which patch had the stronger color dominance...” (line 524).

We have clarified the instructions by providing the actual text displayed to participants in the methods and have ensured consistency in the method to talk about judging the easier stimulus (line 604).

The instructions were “Your task is to judge which patch has a stronger majority of yellow or blue dots. In other words: For which patch do you find it easier to decide what the dominant color is? It does not matter what the dominant color of the easier patch is (i.e., whether it is yellow or blue). All that matters is whether the left or right patch is easier to decide”.

2) Minor comments: Line 76: ”that” should be ”than”.

Thanks, corrected

Line 574: ”variable duration task” means ”controlled duration task”?

Yes, corrected

Line 151: ”or” should be ”of”.

Corrected

Author Response

We appreciate the opportunity to publish our research in eLife. Both reviewers highlight our state-of-the-art oxygen isotope sampling approach, which has allowed us to establish that early-formed primate enamel does not show a large or consistent isotopic offset due to intensive nursing. This means we can be more confident in employing early-forming teeth to probe environmental conditions—an issue that has handicapped past paleoenvironmental studies—documenting seasonal rainfall variation in the tropics at an extremely fine-scale.

Reviewer 1 requests that we elaborate on the ecology and behavior of orangutans, particularly in reference to the issue of isotopic enrichment within forest canopies—a topic we devote a paragraph to in the discussion. We appreciate the opportunity to add additional context during revision, noting here that our previous comparisons of terrestrial baboons and semi-terrestrial tantalus monkeys in the Bushenyi District (Uganda) do show modest isotopic differences between species, consistent with a canopy effect (Green et al. 2022). However, this is less of an issue for comparisons of Sumatran and Bornean orangutans given their ecological and behavioral similarities. We agree that variation in the canopy heights/positions of orangutan food sources may contribute to enamel oxygen isotope variation, in addition to the seasonal rainfall trends we observe in our datasets. Importantly, our published and on-going work on western chimpanzees has revealed strong annual oxygen isotope trends concordant with local rainfall patterns. The consistency and amplitude of seasonal oxygen isotope oscillations in such datasets suggest that arboreal primates are not less useful than terrestrial primates for reconstruction of rainfall seasonality.

We clarify that while Reviewer 1 states that we measured 6 teeth, Tables 1 and 2 and the first sentence of the results make it clear that we measured 18 teeth in this study.

Reviewer 2 asks for further detail about comparisons between modern and fossil orangutan teeth that support inferences of climate variation, which we will endeavour to add in the revised manuscript.

Author Response

We thank Editors and Reviewers for their positive evaluation of our work and appreciation of new findings and applied interdisciplinary approaches. We also thank for pointing out manuscript weaknesses as well as for all suggestions and advices that can strengthen this manuscript. We apologise for mistakes, overstatements or discrepancies in citing figures as well as omitted references.

The first part of the manuscript focuses on the Tetrahymena RSP3 genes mutants.  Tetrahymena genome encodes three RSP3 paralogs that are the components of different radial spokes and likely form homo- and heterodimers. Thus, the proteomic analyses of Tetrahymena radial spokes are more complicated compared to the similar analyses in organisms having a single RSP3 protein.

Next, we attempted to identify proteins specific for each RS type. Conducting this research, we took advantage of six different radial spoke knockout mutants (RSP3A-KO, RSP3B-KO, RSP3C-KO, CFAP206-KO, CFAP61-KO, and CFAP91-KO) and compared wild-type and mutants’ ciliomes using two methods, LFQ and TMT (for each mutant the experiment was repeated three times). Comparative analyses of the wild-type and mutants ciliomes allowed us to identify Tetrahymena radial spoke proteins, in the case of RS1 (WT versus RSP3A-KO), RS2 (WT versus RSP3B-KO, RSP3C-KO, and CFAP206-KO), and RS3 (wild-type versus  CFAP61-KO and CFAP91-KO). The extensive proteomic analyses were combined with detailed bioinformatics studies and co-immunoprecipitation and BioID assays to verify the presence of identified proteins in RS complexes. 

Importantly, in the case of RS1 and RS2 spokes, our findings are in agreement with data obtained for Chlamydomonas and mammalian radial spokes. Thus, it is very likely, that newly discovered RS1 and RS2 proteins as well as identified Tetrahymena RS3 proteins are also true RS subunits.

As an outcome of this part, we propose a model of the RS protein composition in a ciliate Tetrahymena. We agree that this model requires further experimental verification (for example by pull-down experiments).  However, considering the number of identified proteins, this is a considerable amount of additional work that we would like to publish as separate papers. We would like to add that our current analyses of additional RS3 mutant (that will be published separately) support findings regarding RS3 proteomic composition.

Reviewer 2:

The control for the bio-ID experiment was WT cells. Since there are many hits in the experiment, a better control would have been a strain with free BirA, or BirA fused to a protein that is distant from the radial spokes, such as one of the outer-dynein arm proteins, or a ciliary membrane protein.

The BirA* tag is approximately 30 kDa protein and thus it can be transported to cilia by diffusion. BirA* ligase present throughout the cilia could randomly biotinylate proteins including radial spoke proteins. Thus, expression of the BirA* alone is not the best control. We have performed numerous BioID experiments in which BirA* tag was fused with T/TH subunits (CFAP43, CFAP44, Urbanska et al., 2018), subunits of the small complex positioned parallel to N-DRC (CCDC113, CCDC96, Bazan et al., 2021), CFAP69, SPEF2A (C1b central apparatus complex, Joachimiak et al., 2021), N-DRC proteins (Ghanaeian et al., Biorxiv, 2023) and subunits of other ciliary complexes (our unpublished data). The comparison of the earlier obtained BioID data with RSP BioID data, prove that identified proteins are specifically associated with radial spokes. Therefore, in our model, wild-type cells are a good control for BioID experiments.

Author Response

Reviewer 1 Public Review

The authors aim to theoretically explain the wide range of time scales observed in cortical circuits in the brain – a fundamental problem in theoretical neuroscience. They propose that the variety of time scales arises in recurrent neural networks with heterogeneous units that represent neuronal assemblies of different sizes that transition through sequences of high- and low-activity metastable states. When transitions are driven by intrinsically generated noise, the heterogeneity leads to a wide range of escape times (and hence time scales) across units. As a mathematically tractable model, they consider a recurrent network of heterogeneous bistable rate units in the chaotic regime. The model is an extension of the previous model by Stern et al (Phys. Rev. E, 2014) to the case of heterogeneous self-coupling parameters. Biologically, this heterogeneous parameter is interpreted as different assembly sizes. The chaoticity acts as intrinsically generated noise-driving transitions between bistable states with escape times that are indeed widely distributed because of the heterogeneity. The distribution is successfully fitted to experimental data. Using previous dynamic mean-field theory, the self-consistent auto-correlation function of the driving noise in the mean-field model is computed (I guess numerically). This leaves the theoretical problem of calculating escape times in the presence of colored noise, which is solved using the unified colored-noise approximation (UCNA). They find that the log of the correlation time of a given unit increases quadratically with the self-coupling strength of that unit, which nicely explains the distribution of time scales over several orders of magnitude. As a biologically plausible implementationof the theory, they consider a spiking neural network with clustered connectivity and heterogeneous cluster sizes (extension of the previous model by Mazzucato et al. J Neurosci 2015). Simulations of this model also exhibit a quadratic increase in the log dwell time with cluster size. Finally, the authors demonstrate that heterogeneous assemblies might be useful to differentially transmit different frequency components of a broadband stimulus through different assemblies because the assembly size modulates the gain.

I found the paper conceptually interesting and original, especially the analytical part on estimating the mean escape times in the rate network using the idea of probe units and the UCNA. It is a nice demonstration of how chaotic activity serves as noise-driving metastable activity. Calculating the typical time scales of such metastable activity is a hard theoretical problem, for which the authors made considerable advancement. The conclusions of this paper are mostly well supportedby simulations and mathematical analysis, but some aspects need to be clarified and extended, especially concerning the biological plausibility of the rate network model and its relation to the spiking neural network model as well as the analytical calculation of the mean dwell time.

Question 1a. The theory is based on a somewhat unbiological network of bistable rate units. It seems to only loosely apply to the implementation with a spiking neural network with clustered architecture, which is used as a biological justification of the rate model. In the spiking model, a wide distribution of time scales also emerges as a consequence of noise-induced escapes in combination with heterogeneity. Apart from this analogy, however, the mechanisms for metastability seem to be quite different: firstly, the functional units in the spiking neural network are presumably not bistable themselves but multistability only emerges as a network effect, i.e. from the interaction with other assemblies and inhibitory neurons. (This difference yields anti-correlations between assemblies in the spiking model, in marked contrast to the independence of bistable rate units (if N is large).) Secondly, transitions between metastable states are presumably not driven by chaotic dynamics but by finite-size fluctuations (e.g. Litwin-Kumar and Doiron 2012). The latter is also strongly dependent on assembly size. More precisely, the mechanism of how assembly size shapes escape times T seems to be different: in the rate model the self-coupling ("assembly size") predominantly affects the effective potential, whereas in the spiking network, the assembly size predominantly affects the noise. Therefore, the correspondence between the rate model and the spiking model should probably be regarded in a looser sense than presented in the paper.

Answer 1a. We thank the Reviewer for suggesting to clarify the relationship between the rate and spiking model. In this answer, we first show that the dynamicalmodes in the spiking network are E/I cluster pairs, then we show that assemblies are bistable due to the large self-couplings, and third we discuss whether transitions between high and low activity states are driven by chaos or finite size effects, including correlations between assemblies.

We first elucidated the dynamical modes in the spiking network and how those can be related to the rate network. Using an approach from (1, 2), we considered the mean-field theory for the spiking network, reducing the degrees of freedom from N neurons to 2p+2 E/I assemblies (plus E/I background populations), then we identified the approximate dynamical modes as E/I cluster pairs emerging as the Schur eigenvectors of the mean field-reduced coupling matrix. Comparing the eigenvalue distribution of the full vs. the mean field-reduced coupling matrix, we found that the slow timescales capturing the assemblies metastable dynamics correspond to the p−1 large positive eigenvalues corresponding to the Schur modes. The heterogeneity in timescales of the spiking model arises from the heterogeneous distribution of these gapped eigenvalues, reflecting the hierarchy in assembly sizes and assembly self-couplings in the mean field approach. We then analyzed the eigenvalues in the rate network with a lognormal self-coupling distribution and found a similar picture, where the slow units are related to the large eigenvalues in the coupling matrix (Appendix 2). We also note that in the rate network, there is no gap in the eigenvaluedistributionas there are many units with small values of the self-couplings. On the other hand in the spiking network the large eigenvalues are p − 1, where p is the number of assemblies, and they are gapped. These new analyses clarify the correspondence between rate network units and spiking network E/I cluster pairs, arising from the Schur picture.

We now discuss previous studies to examine whether bistability in the spiking network arises from assembly self-couplings or from other effects. Previous mean-field analyses of spiking networks with clustered connectivity showed that the bistability of assembly dynamics is due to the presence of a large self-coupling, rather than from the interactions with other assemblies. We briefly summarize the published evidence for this. The seminal work of (3) showed that in a network with assemblies, a bifurcation in network dynamics emerges when the assembly self-coupling JEE+ > Jc exceeds a critical value Jc; beyond this value, a low and a high activity stable state coexist. Although in this network these two states are stable, more recent work from (4, 5) showed that finite size effects (small assembly size) can destabilize the states, leading to the metastable regime. When the inhibitory population is homogeneous, as in these last two articles, metastability arises from finite size effects and it is sensitive to network parameters (5) and (6). Specifically, when one scales both the network size and the E assembly size, metastability disappears (5). Moreover, when the I population is homogeneous, then E clusters are anti-correlated, as correctly suggested by the Reviewer. However, our model differs from the ones just discussed in that the inhibitory population is also arranged in assemblies, which are reciprocally paired with E assemblies. In this class of E/I clustered models, metastability is robust to changes in network parameters (see (6)). More specifically, in our revised version, we show that metastable dynamics persists when scaling up the network size to N = 10,000 neurons (and scaling up network size with N). A crucial difference between the model with homogeneous I population vs the model with I assemblies (i.e., our model), is that in the former the assemblies are anti-correlated, while in the latter case the assemblies are uncorrelated (see Fig. 1), the same as in the rate network. These results suggest that transitions between metastable states in the spiking network may be driven by a coexistence of two effects: on the one hand, finite size effects due to the small assembly size, and on the other hand, by the heterogeneity in the inter-assembly couplings. Although the former effect is absent in the rate network, the latter is the driver of the chaotic activity observed in the rate network. Thus it is plausible that rate-based chaotic dynamics might also contribute to the metastable activity in the spiking network, although more targeted work should be performed to answer this question. In the revised version of the manuscript, we overhauled the subsection ’A reservoir of timescales in E-I spiking networks’, Fig. 5, and Appendix 2, by adding an extensive explanation of the emergence of slow timescales from the large eigenvalues in the Schur basis, and its comparison between spiking and rate network. In particular, we highlighted the differences between rate and spiking networks and the fact that finite size effects might be at play in the latter case.

Furthermore, the prediction of the rate model is a quadratic increase of log(T), however, the data shown in Fig.5b do not seem to strongly support this prediction. More details and evidence that the data "was best fit with a quadratic polynomial" would be necessary to test the theoretical prediction.

We increased the clarity and strengthened the support for the data in Fig 5b as "best fit with a quadratic polynomial" by addinga plot, inset in Fig 5b, alongsidea detailed explanation of the fitting procedure in Methods section (e). Figure 5b inset displays a cross-validatedmodel selection’s training and test errors for polynomial fit. The test error shows a minimal error at a polynomial degree 2, supporting the claim that the best fit was achieved with a quadratic polynomial. In Methods section (e), under "Model selection for timescale fit," we added a detailed description of the cross-validation procedure by which the fit was obtained. A quote from that section in the revised manuscript can also be found in this document under answer 11.

Question 2. The time scale of a bistable probe unit driven by network-generated "noise" is taken to be the mean dwell time T (mean escape time) in a metastable state. It seems that the expressions Eq.4 and Eq.21 for this time are incorrect. The mean dwell time is given by the mean first-passage time (MFPT) from one potential minimum to the opposite one includingthe full passage across the barrier. At least, the final point for the MFPT should be significantly beyond the barrier to complete the escape. However, the authors only compute the MFPT to a location −xc slightly before the barrier is reached, at which point the probe unit has not managed to escape yet (e.g. it could go back to −x2 after reaching −xc instead of further going to +x2). It is not clear whether the UCNA can be applied to such escape problems because it is valid only in regions, where the potential is convex, and thus the UCNA may break down near the potential barrier. Indeed, the effective potential is not defined near the barrier (see forbidden zone in Fig.4b), and hence it is not clear how to calculate the mean escape time. Nonetheless, the incomplete MFPT computedby the authors seems to qualitatively predict the dependence on the self-coupling parameter s, at least in the example of Fig.4c. However, if the incomplete MFPT is taken as a basis, then the incomplete MFPT should also be used for the white-noise case for a fair comparison. It seems that the corresponding white-noise case is given by Eq.4 with τ1 = 0, which still has the same dependence on the self-coupling s2, contrary to what is claimed in the paper (it is unclear how the curve for the white-noise case in Fig.4 was obtained). Note that the UCNA has been designed such that it is valid for both small and large τ1 (thus, it is also unclear why the assumption of large τ1 is needed).

Answer 2. We are deeply grateful to the Reviewer for this critical evaluation of our UCNA calculation of the escape times. We will first clarify our rationale and then discuss comparison with the white noise case. The idea behind our calculation is indeed that when starting from the left minimum −x2, the probe effectively escapes to +x2 before reaching the limit of the UCNA support region at −xc. First, our simulations show (Fig 4b light blue colored area) that the probe almost exclusively visits the valid areas |x| > xc: our new analysis shows that the fraction of activity spent in the forbidden region is (1.8+/ −0.4)×10−3 (mean±SD over 10 probe units run with parameters as in Fig. 4a-b), confirming the fact that the histogram of x values from simulations has almost null support in the forbidden region |x| < xc. This is also supported by the representative simulation time course in Fig. 4a which exhibits abrupt jumps between the two bistable states. We then estimated the ’escape point’ from simulations as follows: for a transition from the x = −s2 well towards the x = +x2 well, the escape point is defined as the point where x on the side of the source well, i.e. x < 0, but the trajectory starts accelerating towards the target well (positive second derivative). We found that the distribution of escape points was predominantly in the allowed region (93.8%). This analysis supports our method to calculate the MFPT and confirms that our calculation is performed in the valid UCNA region. In the revised version of the manuscript, we added a clarification of this point with text and a new supplementary figure in Fig. 4 Suppl. 1. Regarding the comparison with white noise, we compared white-noise-driven probe dynamics with a probe driven by a network (effectively represented by the colored noise). To adequately make this comparison, we replaced the input coming from the network into the probe unit (Eq 1. rhs last term) with white noise. The rest of the terms in this equation were left untouched to maintain the exact probe’s self-response properties. This procedure aims to understand the unique contribution of the colored noise generated by the network to each unit dynamics by removing its "colored" correlated input contribution but otherwise leaving all dynamical properties the same. For clarity of the manuscript on this subject, we added a paragraph about it under "A comparison with white noise" in Methods section (d).

We can estimate the mean first passage time (MFPT) of a probe unit driven by white noise with Eq. 4. The procedure described above for switching the network drive with white noise also dictates the parameter values to use in Eq. 4 for the case of white noise. First, with no correlation in white noise τ1 = 0. Second, D, the magnitude of the drive inherits its value from the network (see also Eq. 22) as the strength of the white noise (its integral around zero as a δ function). The results are presented in Fig 4. To strengthen the results and improve the clarity of the text, we expanded the content of Fig 4c. The plot now includes both the results of simulations (Fig. 4c green line) and estimation by mean first passage time (Fig. 4c green dashed line) for white noise, as explained above. We note that the potential in the white noise case (Fig. 4b green dashed line) does include a concave part. Indeed,the agreementbetweenthe distributionretrieved from simulations (Fig. 4b light green area) and its locations’ visit probability approximated by theory (Eq. 19 with τ1 = 0, Fig. 4b green line) are not in full agreement. However, this probability is still a good approximation. As a result, the mean first passage time (Eq. 4, Fig. 4c green dashed line) is a good approximation. The great advantage of having Eq. 4 as an approximation for the mean first passage time is that it clearly explainsthe contributionof each part of the dynamical equation (Eq. 1) towards achieving long timescales. Mainly, since log<T> depends on τ1 linearly, its exponent, the mean first passage time depends on tau1 exponentially. Hence the importance of the color in the input and the vast differences between the network drive and the white noise.

Question 3. The given argument that the time-scale separation arises as network effect is not very clear. Apart from the issue of a fair comparison of colored and white noise raised in point 1 above, an external colored noise with matched statistics that drives a single bistable unit would yield the same MFPT and thus would be an alternative explanation independent of the network dynamics.

Answer 3. The goal of our investigation was to uncover a neural mechanism that induces heterogeneous timescales in a self-consistent way. The idea of self-consistencyis the central tenet of our approach, namely, that a timescale distribution must arise due to the internal dynamics of a recurrent circuit without the need to invoke an external auxiliary force driving it. If we had an external colored noise with matched statistics driving the probe unit, then we would still have to explain which mechanism would give rise to that particular statistics of the colored noise - with the most natural explanation being a recurrent network with time-varying activity.

The second ingredient in our argument demonstrating that it is a network effect is the following. If the time-scale separation was not a network effect, but rather a property of a single probe unit, then it would persist regardless of the specific features of the noise driving the unit. To test this hypothesis, we compared the scenarios of the same probe unit driven by the self-consistent noise generated by the rest of the network, as opposed to white noise, and found that the time-scale separation is not present in the second case. Thus, the time-scale separation is not an intrinsic property of the probe unit, but, rather, it relies on the unit being part of a recurrent network generating a specific kind of noise. This argument is explained in the last paragraph of the section ’Separation of timescales in the bistable chaotic regime’.

Question 4. The UCNA has assumptions and regimes of validity that are not stated in the paper. In particular, it assumes an Ornstein-Uhlenbeck noise, which has an exponential auto-correlation function, and local stability (region where potential is convex). Because the self-consistent auto-correlation function is generally not exponential and the probe unit also visits regions where the potential is concave, the validity of the UCNA is not clear. On the other hand, the assumption of large correlation time might be dropped as the UCNA’s main feature is that it works for both large and small correlation times.

Answer 4. We thanks the Reviewer again for this critical evaluation of our assumptions, however, we believe that our approach is justified because of the following two arguments. First, although the UCNA was derived in case of an OU process, it has since then been successfully applied to different classes of noise, including multiplicative noise, harmonic noise, and others (see e.g. (7–9). To the best of our knowledge, the UCNA has never been applied before to noise whose autocorrelation arises from chaotic dynamics, whose hallmark is a vanishing slope at zero lag, markedly different from the OU process. To address the concern about concavity, we performed the additional analyses discussed in our answer to Question 2, showing that the probe unit never visits regions where the potential is concave, which would lie outside of the support of the potential. Because of these two considerations, we believe that the UCNA is valid in our scenario, as suggested by the good agreement between theory and simulation at large values of the self-couplingsin Fig. 4c. Finally, we thank the Reviewer for bringing up the fact that UCNA works for both large and small correlation times, we fixed that in the revised manuscript.

Author Response

Reviewer #2 (Public Review):

The work is very clearly designed, executed, and written. The transcription output data is rigorous and well quantified, and the fit of the TF binding model clearly shows agreement with experiments in the case of cooperativity, but not in its absence, making a strong case for the authors' conclusion.

How the Hidden Markov Model fit results (promoter kon and koff values) lead to the observed effects on transcription output is less clear. For instance, Dl1 deletion results in a small increase in kon and a moderate increase in koff, which seems at odds with the other variants. Yet all variants exhibit similar transcription output profiles. One other intriguing observation is that the promoter states in Fig. 4C&D do not look dramatically different in their kinetics, yet the input transcription traces exhibit a 3-fold amplitude difference. Maybe the authors can clarify these apparent discrepancies.

We thank the reviewer for insightful comments. The reduction in transcription output is mainly due to the decrease in transcription amplitude. We have done further analysis to demonstrate that the loading rate of Pol II, correlated to the initial slope of transcription, is significantly reduced in the mutants. We measured the initiation rate by calculating the slope of the MS2 traces and correlated it to the Pol II loading rate. As expected, the initiation rate in wildtype is higher than in mutant embryos. This additional analysis suggests that the drastic reduction in transcriptional amplitude is due to the reduced Pol II loading rate, not kon, and corroborates the previously shown results and conclusions (Bothma et al., PNAS 2014, PMID: 24994903; Garcia et al., Curr. Biol. 2013, PMID: 24139738). We have added this plot in Figure 4H in the revised manuscript, which shows the initiation rates of the wildtype and mutant embryos, and revised the manuscript as follows.

We have added this in the Introduction (Page 4):

We find that mutating a single TF (Dl or Twi) binding site in the enhancer significantly reduces mRNA production of the target gene, mainly through lowering transcriptional amplitude by reducing RNA polymerase (Pol) II loading rate, without significantly delaying the timing of initiation or affecting the probability of activation.

We have added this in the Results (Page 15):

Previously, we demonstrated that the mutations affect mRNA production through transcriptional amplitude (Figure 2E). This could be because either the mutations hinder the Pol II loading rate or reduce the time the promoter is in the ON state….

In addition, we find that the Pol II loading rate is significantly reduced in the mutant embryos compared to the wildtype (Figure 4H). This confirms that the lower transcriptional amplitude mainly results from the promoter’s inability to effectively load Pol II, along with an additional contribution from the reduced time the promoter spends in the ON state.

We have added this in the Discussion (Page 16):

This reduction is mainly due to the decreased transcriptional amplitude, driven by a lower rate of Pol II loading… and, Since the amount of time the promoter spends in the ON state is not affected by the mutations, the lower transcriptional amplitude can be mainly attributed to the promoter’s inability to effectively load Pol II (Figure 2E, Figure 4D-F).

The HMM is utilized to tease apart the changes in transcriptional kinetics. Our analysis revealed that the HMM provides some explanation for the reduction in transcriptional output in TF binding site mutants. For this reason, we must examine the results in a broader context. As pointed out, Dl1 site deletion has a slightly different effect on kon and koff. However, its transcription output is similar to the other mutants (Figure 4D and E). This is due to the fact that the changes in kon and koff are significantly less drastic than the changes in the transcription amplitude and Pol II loading rates, contributing less to the mRNA production. In our analysis, the amplitude is a separate parameter than the kon and koff rates, which are calculated from the HMM.

We have added the following in the Discussion to address this concern (Page 17):

However, we note that the HMM only provides some explanation for the reduction in transcriptional activity since the changes in kon and koff are less drastic than the changes in transcriptional output. Since the amount of time the promoter spends in the ON state is not affected by the mutations, the lower transcriptional amplitude can be mainly attributed to the promoter’s inability to effectively load Pol II (Figure 2E, Figure 4D, H).

The authors observe cooperativity between TF binding sites and transcription output, which their model suggests is driven by TF binding cooperativity ("We propose that the cooperativity allows TF binding sites with moderate or weak affinities to recruit more TFs to the enhancer"). This is plausible and likely, but not rigorously demonstrated; another possibility could be cooperativity at the step of transcription activation. One could verify that the binding step is the cooperative one via ChIP-qPCR in the different variants, but given the cautious wording of the paper, this is not absolutely necessary.

We thank the reviewer for suggesting this experiment. Unfortunately, due to the experimental design, performing ChIP-qPCR was not feasible. There are two copies of snaSEmin enhancer region, one within the endogenous genome and the one within the transgene. For this reason, proper amplification in qPCR was challenging as the primers would recognize two distinct portions of the genome. We designed primers such that the forward primer would recognize both the endogenous and transgene enhancer region (inevitable) and the reverse primer would recognize only the transgene. Yet, we did not observe the expected fold change in amplification as the concentration of DNA was modulated. Hence, we did not proceed to perform ChIPqPCR.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors investigated plausible circuit mechanisms for their recently reported effect of NMDAR antagonists on the synchrony of prefrontal neurons in a cognitive task. On the basis of previously proposed computational network models of spiking excitatory and inhibitory neurons and their mean-field and linear stability analysis descriptions, they show that a specific network configuration set close to the onset of instability of the asynchronous state can replicate qualitatively key empirical observations. For such a network, a small increase in external drive causes a large increase in neuronal synchrony, and this is not happening if NMDAR-dependent transmission is reduced. This shows parallelism with the empirical data thus representing its first neural network explanation.

The paper provides valuable insights into possible mechanisms related to cortical dysfunction under NMDAR hypofunction, a topic of importance for several neuropsychiatric disorders. However, the fact that the manuscript remains at a rather abstract level and does not attempt a closer match to the experimental data is a limitation of the study.

1) The manuscript is strongly based on state diagrams and parametric descriptions of neural dynamics in a computational model that has been extensively studied before (Brunel, Wang 2003). Many of the parametric dependencies of this model shown here were already reported before, although not specifically altering concurrently external inputs and NMDAR-dependent transmission as done now. The main novelty of the study is the application of this framework to a specific empirical dataset of great scientific relevance. However, the manuscript emphasizes the model exploration in relation to a limited set of effects in the data (changes in synchrony immediately before motor response) and not so much the comparison to the neural recordings more generally (for instance, firing rates, other time periods in the task, etc.)

We are grateful to the Reviewer for thoroughly reviewing the manuscript and the constructive critique. Our work is built on the computational framework that has been developed earlier in several seminal computational and theoretical studies, including Compte et al. (2000) and Brunel and Wang (2003), that we acknowledge throughout our paper. However, we would like to emphasize, without diminishing the importance of these earlier studies, that our work provides new theoretical and computational insights on the impact of NMDAR synaptic transmission modulation on spiking dynamics by further developing the theoretical framework of Brunel and Wang (2003). For example, in Brunel and Wang (2003) it is stated that “NMDA conductances could be removed from all simulations without affecting any of the results” (p. 416). In fact, equations provided in Brunel and Wang (2003) are only for the special case of the oscillatory instability growth rate λ=0 and they do not include the NMDAR synaptic conductances. Thus, the consideration presented in Brunel and Wang (2003) cannot explain the NMDAR-dependent modulation of synchrony effect observed in Zick et al. (2018). In our study, we extended the theoretical framework of Brunel and Wang (2003) and provided equations that explicitly include both λ and NMDAR conductance. It is this extension of the framework that allowed us to provide an NMDAR dependent mechanism to explain the Zick et al. (2018) effect.

In the revised manuscript, by suggestion of Reviewer 2, we have further extended theoretical consideration and obtained an analytic approximation in closed form for the oscillatory instability growth rate λ describing the dependence on the AMAPR, NMDAR, GABAR synaptic conductances and external rate. We believe that this is the first paper in which such approximation for the instability growth rate λ accounting for the effects of more realistic synaptic currents is obtained. Based on this consideration, we have now provided in a new Results section “Dependence of oscillatory instability growth rate on synaptic parameters” a substantially more detailed theoretical account of the precise mechanism implemented in our model for the transition between the steady and oscillatory states and the lack thereof when the NMDAR conductance is blocked.

We agree with the reviewer that it would be beneficial for the paper to extend the model exploration in relation to other measurable variables provided by neural data such us firing rates. At the reviewers’ suggestions we have now carried out new series of simulations with transient external inputs and compared the simulation results with the dynamics of both synchrony and firing rates that were estimated from neural data. We address these questions in more detail in the corresponding points in the Recommendations for the authors section below.

2) As discussed in the introduction, empirical data available suggests that 0-lag synchrony in prefrontal networks is affected by manipulations that reduce NMDAR function (Zick et al. 2018) and by manipulations that enhance NMDAR function (Zick et al. 2021). The computational model presented in this manuscript does not show this U-shaped behavior and the discussion does not mention this. It should be discussed whether the model can accommodate this or not.

This is a very good point which we now explicitly address in a new section in the revised Discussion (‘Potential U-shaped relation between NMDAR function and spike synchrony’, see new text in blue starting at line 953). The reviewer provides an excellent insight by noting that that our prior neural recording data (specifically convergent reduction in 0-lag synchrony in monkey drug and mouse genetic models) could be explained by an inverted U-shaped relationship between NMDAR function and 0-lag synchrony. In the new section we also note the precedent for such a relationship by drawing a parallel to the work of Vijayraghavan, Arnsten and colleagues (2007) showing an inverted U-shaped relationship between D1R synaptic actions and the strength of persistent activity in monkey prefrontal neurons during working memory tasks.

However, in the new section we note also that we cannot yet conclude that the relationship between 0-lag spike synchrony and NMDAR activation is indeed an inverted U-shaped function based on our neural data. Reaching this conclusion would require completing a dose-response function between the concentration of NMDAR agonist (or antagonist) administered and the strength of 0-lag synchrony (which we have not done). In addition, we note in the new section that we can’t conclude the reduction of 0-lag synchrony in mouse prefrontal cortex is indeed due to increased expression of NMDAR, since deletion of Dgcr8, given its role in miRNA synthesis, would be expected to upregulate the expression of many different mRNA corresponding to many different genes. However, the possibility of a U-shaped relation is an important and interesting one, which we now fully discuss.

Reviewer #2 (Public Review):

In this paper, the authors carry out neural circuit modeling to theoretically elucidate the mechanism underlying the empirically observed (in a previous study by some of the current authors) reduction in neural synchrony in the monkey prefrontal cortex (PFC), as a result of NMDAR blockade. Empirically it was previously found that in monkeys performing a cognitive control task, PFC neurons exhibit precisely timed synchronous firing, especially in the short period before the monkey's response, leading to "0-lag" (zero in the 1-2 millisecond timescale) spiking correlations. This signature of synchrony was then found to be extinguished or diminished with the systemic administration of an NMDAR antagonist.

In the current study, the authors simulate and analyze a network of excitatory and inhibitory spiking neurons as a model of a local PFC circuit, to elucidate the mechanism underlying this effect. The model network is composed of leaky integrate-and-fire neurons with conductance-based synaptic inputs and is sparsely and randomly connected as in the classic studies of balanced networks in which neurons fire irregularly as observed in the cortex. Using mean-field theory, the authors start by mapping out the phase boundary between the asynchronous irregular and synchronous irregular states in the network as a function of network parameters controlling synaptic connectivity and external background inputs (which they parametrize as ratios of recurrent or external currents mediated by AMPAR, NMDAR or GABAA). The transition between the two phases corresponds to a Hopf-like bifurcation above which synchronous oscillations with frequency in the gamma-band (or above) emerge. It is found that with an increase in external inputs, a network in the asynchronous state (but close to criticality) can switch to the synchronous state. Based on this, the authors hypothesize that an increase in the external drive is the mechanism underlying the empirically observed increase in synchrony before the behavioral response. It is then shown that a reduction in NMDAR conductance (keeping AMPAR or GABAR conductances fixed) has the opposite effect, and pushes the network towards the asynchronous state, and can counteract or weaken the effect of increased external input. In both cases increase or decrease in synchrony is quantified by an increase or decrease in 0-lag pairwise correlations; transition to synchrony is shown to also lead to the development of nonzero-lag peaks in the average spiking correlation reflecting gamma-band oscillations. The authors then show that (with the appropriate choice of primary network parameters) their proposed mechanisms for the (natural) increase in synchrony via an increase in external inputs and the weakening of this effect with the weakening of NMDA conductances do semi-quantitatively match the observed changes in 0-lag synchrony and nonzero lag peaks in spiking correlations. Finally, they discuss the effect of the balance between average NMDA and GABA currents in the primary (baseline) network on the above effects.

Strengths:

• The modeling and analysis are solid and overall this work succeeds in providing a convincing mechanistic explanation for the specific empirically observed effects in monkey PFC: the natural task-dependent modulation of 0-lag synchrony and its extinction with NMDA blockage.

• The manuscript is very readable and the figures and plots are clearly described.

• The mathematical mean-field analysis in the Methods section is also sound and well written and does/can (see below) provide a sufficient mathematical explanation of the simulation results.

We appreciate the positive comments.

Weaknesses:

1) I found the intuitive explanation of the effects of external input or NMDAR conductance on synchrony incomplete. While simulations and mean-field analysis both predict this effect, the mean-field theory and the linearization analysis and stability analysis can be used to further shed light on the precise mechanism by which external input and NMDAR conductance promote synchrony (or destabilization of the asynchronous state).

2) An important natural question (which is relevant to the connection with schizophrenia) is what are the distinct roles of AMPAR-based and NMDAR-based excitation on the transition to synchrony, and this is not addressed in this study. It would be important to clarify what is special/distinct about NMDAR in the current findings.

3) In the Introduction and Discussion, the authors speculate on the possible connection between their empirical and theoretical findings (on the effect of NMDAR hypofunction on synchronous spiking) and the pathogenesis of schizophrenia. While this is not central to the findings of the paper, because it is relevant to the broader significance and impact of this work I will note the following. Their proposed specific link to pathogenesis is as follows: the reduction in precisely timed synchrony resulting from NMDAR hypofunction can disrupt spike-timing dependent plasticity (STDP) and lead to "disconnection" of cortical circuits as observed in schizophrenia. Letting aside the fact that observations in schizophrenia relate to functional connectivity and not synaptic connectivity, previous theoretical studies of STDP in spiking networks do not support the claim that lack of synchronous activity would lead to disconnection of the circuit.

Thank you for the thorough review and critique, bringing up these important issues. We address them in detail in the corresponding points in the Recommendations for the authors section below.

Reviewer #3 (Public Review):

The starting point of the paper is the observation by the group of Matthew Chafee that zero-lag correlations in pairs of prefrontal cortex neurons transiently increase close to the motor response in a dot-pattern expectancy task', and that this increase in synchrony is abolished by NMDA blockers. The goal of this paper is to understand the mechanisms of this NMDA-dependent increase in synchrony using computational modeling. They simulate and analyze a network of sparsely connected spiking neurons in which synaptic interactions are mediated by AMPA, NMDA, and GABA conductances with realistic time constants. In this network, it had been shown previously that when parameters are such that the network is close to a bifurcation separating asynchronous from synchronous oscillatory states, an increase in external inputs can push the network towards synchrony. They show that when the NMDA component of synaptic inputs is removed, the network moves away from the bifurcation, and thus the same increase in external inputs no longer leads to a significant increase in synchronization.

Thus, this study provides a potential explanation for the NMDA-dependent increase of synchrony observed in their data. The authors further argue that this effect might be responsible for symptoms observed in schizophrenia, through spike-timing-dependent mechanisms. Overall, this is an interesting study, but there are several weaknesses that dampened my initial enthusiasm: In particular, the model predicts a tight link between synchrony and mean firing rate that should hold during the whole task, not only at the time of the motor response but this is not explored by the authors.

Thank you for critically reviewing the manuscript and valuable comments. We address them in the corresponding points in the Recommendations for the authors section below.

Also, the relationship between changes in synchrony due to NMDAR dysfunction and schizophrenia is not very convincing. Many forms of synaptic plasticity, including STDP are dependent on NMDA receptors, and thus synaptic plasticity in schizophrenic patients is likely to be impacted independently of any synchrony. Thus, the link between the results of this paper and schizophrenia seems tenuous.

These are good points. To address them we have limited the link between the current study and schizophrenia in the Introduction to the motivation for the original neurophysiological experiments (as this link dictated the pharmacological and genetic manipulations we employed in the animal models). We have also added a new section to the Discussion with the heading ‘Spike timing disruptions and rewiring of prefrontal local circuits via STDP’ where we discuss the complexity of the interaction between STDP, synchrony, and connectivity in prior modeling studies. Namely, it is difficult to predict whether loss of synchronous spiking would cause disconnection via STDP without additional data. We acknowledge this constraint on our original hypothesis that asynchrony would cause disconnection considering these prior theoretical studies in this new section. In this section, we also note that altered NMDAR function that has been implicated in schizophrenia could impact STDP directly independently of any change in spike synchrony (see new blue text, starting at line 950) as suggested.

Author Response

Reviewer #1 (Public Review):

Esmaily and colleagues report two experimental studies in which participants make simple perceptual decisions, either in isolation or in the context of a joint decision-making procedure. In this "social" condition, participants are paired with a partner (in fact, a computer), they learn the decision and confidence of the partner after making their own decision, and the joint decision is made on the basis of the most confident decision between the participant and the partner. The authors found that participants' confidence, response times, pupil dilation, and CPP (i.e. the increase of centro-parietal EEG over time during the decision process) are all affected by the overall confidence of the partner, which was manipulated across blocks in the experiments. They describe a computational model in which decisions result from a competition between two accumulators, and in which the confidence of the partner would be an input to the activity of both accumulators. This model qualitatively produced the variation in confidence and RTs across blocks.

The major strength of this work is that it puts together many ingredients (behavioral data, pupil and EEG signals, computational analysis) to build a picture of how the confidence of a partner, in the context of joint decision-making, would influence our own decision process and confidence evaluations. Many of these effects are well described already in the literature, but putting them all together remains a challenge.

We are grateful for this positive assessment.

However, the construction is fragile in many places: the causal links between the different variables are not firmly established, and it is not clear how pupil and EEG signals mediate the effect of the partner's confidence on the participant's behavior.

We have modified the language of the manuscript to avoid the implication of a causal link.

Finally, one limitation of this setting is that the situation being studied is very specific, with a joint decision that is not the result of an agreement between partners, but the automatic selection of the most confident decisions. Thus, whether the phenomena of confidence matching also occurs outside of this very specific setting is unclear.

We have now acknowledged this caveat in the discussion in line 485 to 504. The final paragraph of the discussion now reads as follows:

“Finally, one limitation of our experimental setup is that the situation being studied is confined to the design choices made by the experimenters. These choices were made in order to operationalize the problem of social interaction within the psychophysics laboratory. For example, the joint decisions were not made through verbal agreement (Bahrami et al., 2010, 2012). Instead, following a number of previous works (Bang et al., 2017, 2020) joint decisions were automatically assigned to the most confident choice. In addition, the partner’s confidence and choice were random variables drawn from a distribution prespecified by the experimenter and therefore, by design, unresponsive to the participant’s behaviour. In this sense, one may argue that the interaction partner’s behaviour was not “natural” since they did not react to the participant's confidence communications (note however that the partner’s confidence and accuracy were not entirely random but matched carefully to the participant’s behavior prerecorded in the individual session). How much of the findings are specific to these experimental setting and whether the behavior observed here would transfer to real-life settings is an open question. For example, it is plausible that participants may show some behavioral reaction to a human partner’s response time variations since there is some evidence indicating that for binary choices such as those studied here, response times also systematically communicate uncertainty to others (Patel et al., 2012). Future studies could examine the degree to which the results might be paradigm-specific.”

Reviewer #2 (Public Review):

This study is impressive in several ways and will be of interest to behavioral and brain scientists working on diverse topics.

First, from a theoretical point of view, it very convincingly integrates several lines of research (confidence, interpersonal alignment, psychophysical, and neural evidence accumulation) into a mechanistic computational framework that explains the existing data and makes novel predictions that can inspire further research. It is impressive to read that the corresponding model can account for rather non-intuitive findings, such as that information about high confidence by your collaborators means people are faster but not more accurate in their judgements.

Second, from a methodical point of view, it combines several sophisticated approaches (psychophysical measurements, psychophysical and neural modelling, electrophysiological and pupil measurements) in a manner that draws on their complementary strengths and that is most compelling (but see further below for some open questions). The appeal of the study in that respect is that it combines these methods in creative ways that allow it to answer its specific questions in a much more convincing manner than if it had used just either of these approaches alone.

Third, from a computational point of view, it proposes several interesting ways by which biologically realistic models of perceptual decision-making can incorporate socially communicated information about other's confidence, to explain and predict the effects of such interpersonal alignment on behavior, confidence, and neural measurements of the processes related to both. It is nice to see that explicit model comparison favor one of these ways (top-down driving inputs to the competing accumulators) over others that may a priori have seemed more plausible but mechanistically less interesting and impactful (e.g., effects on response boundaries, no-decision times, or evidence accumulation).

Fourth, the manuscript is very well written and provides just the right amount of theoretical introduction and balanced discussion for the reader to understand the approach, the conclusions, and the strengths and limitations.

Finally, the manuscript takes open science practices seriously and employed preregistration, a replication sample, and data sharing in line with good scientific practice.

We are grateful to the reviewer for their positive assessment of our work.

Having said all these positive things, there are some points where the manuscript is unclear or leaves some open questions. While the conclusions of the manuscript are not overstated, there are unclarities in the conceptual interpretation, the descriptions of the methods, some procedures of the methods themselves, and the interpretation of the results that make the reader wonder just how reliable and trustworthy some of the many findings are that together provide this integrated perspective.

We hope that our modifications and revisions in response to the criticisms listed below will be satisfactory. To avoid redundancies, we have combined each numbered comment with the corresponding recommendation for the Authors.

First, the study employs rather small sample sizes of N=12 and N=15 and some of the effects are rather weak (e.g., the non-significant CPP effects in study 1). This is somewhat ameliorated by the fact that a replication sample was used, but the robustness of the findings and their replicability in larger samples can be questioned.

Our study brings together questions from two distinct fields of neuroscience: perceptual decision making and social neuroscience. Each of these two fields have their own traditions and practical common sense. Typically, studies in perceptual decision making employ a small number of extensively trained participants (approximately 6 to 10 individuals). Social neuroscience studies, on the other hand, recruit larger samples (often more than 20 participants) without extensive training protocols. We therefore needed to strike a balance in this trade-off between number of participants and number of data points (e.g. trials) obtained from each participant. Note, for example, that each of our participants underwent around 4000 training trials. Strikingly, our initial study (N=12) yielded robust results that showed the hypothesized effects nearly completely, supporting the adequacy of our power estimate. However, we decided to replicate the findings because, like the reviewer, we believe in the importance of adequate sampling. We increased our sample size to N=15 participants to enhance the reliability of our findings. However, we acknowledge the limitation of generalizing to larger samples, which we have now discussed in our revised manuscript and included a cautionary note regarding further generalizations.

To complement our results and add a measure of their reliability, here we provide the results of a power analysis that we applied on the data from study 1 (i.e. the discovery phase). These results demonstrate that the sample size of study 2 (i.e. replication) was adequate when conditioned on the results from study 1 (see table and graph pasted below). The results showed that N=13 would be an adequate sample size for 80% power for behavoural and eye-tracking measurements. Power analysis for the EEG measurements indicated that we needed N=17. Combining these power analyses. Our sample size of N=15 for Study 2 was therefore reasonably justified.

We have now added a section to the discussion (Lines 790-805) that communicates these issues as follows:

“Our study brings together questions from two distinct fields of neuroscience: perceptual decision making and social neuroscience. Each of these two fields have their own traditions and practical common sense. Typically, studies in perceptual decision making employ a small number of extensively trained participants (approximately 6 to 10 individuals). Social neuroscience studies, on the other hand, recruit larger samples (often more than 20 participants) without extensive training protocols. We therefore needed to strike a balance in this trade-off between number of participants and number of data points (e.g. trials) obtained from each participant. Note, for example, that each of our participants underwent around 4000 training trials. Importantly, our initial study (N=12) yielded robust results that showed the hypothesized effects nearly completely, supporting the adequacy of our power estimate. However, we decided to replicate the findings in a new sample with N=15 participants to enhance the reliability of our findings and examine our hypothesis in a stringent discovery-replication design. In Figure 4-figure supplement 5, we provide the results of a power analysis that we applied on the data from study 1 (i.e. the discovery phase). These results demonstrate that the sample size of study 2 (i.e. replication) was adequate when conditioned on the results from study 1.”

We conducted Monte Carlo simulations to determine the sample size required to achieve sufficient statistical power (80%) (Szucs & Ioannidis, 2017). In these simulations, we utilized the data from study 1. Within each sample size (N, x-axis), we randomly selected N participants from our 12 partpincats in study 1. We employed the with-replacement sampling method. Subsequently, we applied the same GLMM model used in the main text to assess the dependency of EEG signal slopes on social conditions (HCA vs LCA). To obtain an accurate estimate, we repeated the random sampling process 1000 times for each given sample size (N). Consequently, for a given sample size, we performed 1000 statistical tests using these randomly generated datasets. The proportion of statistically significant tests among these 1000 tests represents the statistical power (y-axis). We gradually increased the sample size until achieving an 80% power threshold, as illustrated in the figure.The the number indicated by the red circle on the x axis of this graph represents the designated sample size.

Second, the manuscript interprets the effects of low-confidence partners as an impact of the partner's communicated "beliefs about uncertainty". However, it appears that the experimental setup also leads to greater outcome uncertainty (because the trial outcome is determined by the joint performance of both partners, which is normally reduced for low-confidence partners) and response uncertainty (because subjects need to consider not only their own confidence but also how that will impact on the low-confidence partner). While none of these other possible effects is conceptually unrelated to communicated confidence and the basic conclusions of the manuscript are therefore valid, the reader would like to understand to what degree the reported effects relate to slightly different types of uncertainty that can be elicited by communicated low confidence in this setup.

We appreciate the reviewer’s advice to remain cautious about the possible sources of uncertainty in our experiment. In the Discussion (lines 790-801) we have now added the following paragraph.

“We have interpreted our findings to indicate that social information, i.e. partner’s confidence, impacts the participants beliefs about uncertainty. It is important to underscore here that, similar to real life, there are other sources of uncertainty in our experimental setup that could affect the participants' belief. For example, under joint conditions, the group choice is determined through the comparison of the choices and confidences of the partners. As a result, the participant has a more complex task of matching their response not only with their perceptual experience but also coordinating it with the partner to achieve the best possible outcome. For the same reason, there is greater outcome uncertainty under joint vs individual conditions. Of course, these other sources of uncertainty are conceptually related to communicated confidence but our experimental design aimed to remove them, as much as possible, by comparing the impact of social information under high vs low confidence of the partner.”

In addition to the above, we would like to clarify one point here with specific respect to the comment. Note that the computer-generated partner’s accuracy was identical under high and low confidence. In addition, our behavioral findings did not show any difference in accuracy under HCA and LCA conditions. As a consequence, the argument that “the trial outcome is determined by the joint performance of both partners, which is normally reduced for low-confidence partners)” is not valid because the low-confidence partner’s performance is identical to that of the high-confidence partner. It is possible, of course, that we have misunderstood the reviewer’s point here and we would be happy to discuss this further if necessary.

Third, the methods used for measurement, signal processing, and statistical inference in the pupil analysis are questionable. For a start, the methods do not give enough details as to how the stimuli were calibrated in terms of luminance etc so that the pupil signals are interpretable.

Here we provide in Author response image 1 the calibration plot for our eye tracking setup, describing the relationship between pupil size and display luminance. Luminance of the random dot motion stimuli (ie white dots on black background) was Cd/m2 and, importantly, identical across the two critical social conditions. We hope that this additional detail satisfies the reviewer’s concern. For the purpose of brevity, we have decided against adding this part to the manuscript and supplementary material.

Author response image 1.

Calibration plot for the experimental setup. Average pupil size (arbitrary units from eyelink device) is plotted against display luminance. The plot is obtained by presenting the participant with uniform full screen displays with 10 different luminance levels covering the entire range of the monitor RGB values (0 to 255) whose luminance was separately measured with a photometer. Each display lasted 10 seconds. Error bars are standard deviation between sessions.

Moreover, while the authors state that the traces were normalized to a value of 0 at the start of the ITI period, the data displayed in Figure 2 do not show this normalization but different non-zero values. Are these data not normalized, or was a different procedure used? Finally, the authors analyze the pupil signal averaged across a wide temporal ITI interval that may contain stimulus-locked responses (there is not enough information in the manuscript to clearly determine which temporal interval was chosen and averaged across, and how it was made sure that this signal was not contaminated by stimulus effects).

We have now added the following details to the Methods section in line 1106-1135.

“In both studies, the Eye movements were recorded by an EyeLink 1000 (SR- Research) device with a sampling rate of 1000Hz which was controlled by a dedicated host PC. The device was set in a desktop and pupil-corneal reflection mode while data from the left eye was recorded. At the beginning of each block, the system was recalibrated and then validated by 9-point schema presented on the screen. For one subject was, a 3-point schema was used due to repetitive calibration difficulty. Having reached a detection error of less than 0.5°, the participants proceeded to the main task. Acquired eye data for pupil size were used for further analysis. Data of one subject in the first study was removed from further analysis due to storage failure.

Pupil data were divided into separate epochs and data from Inter-Trials Interval (ITI) were selected for analysis. ITI interval was defined as the time between offset of trial (t) feedback screen and stimulus presentation of trial (t+1). Then, blinks and jitters were detected and removed using linear interpolation. Values of pupil size before and after the blink were used for this interpolation. Data was also mid-pass filtered using a Butterworth filter (second order,[0.01, 6] Hz)[50]. The pupil data was z-scored and then was baseline corrected by removing the average of signal in the period of [-1000 0] ms interval (before ITI onset). For the statistical analysis (GLMM) in Figure 2, we used the average of the pupil signal in the ITI period. Therefore, no pupil value is contaminated by the upcoming stimuli. Importantly, trials with ITI>3s were excluded from analysis (365 out of 8800 for study 1 and 128 out 6000 for study 2. Also see table S7 and Selection criteria for data analysis in Supplementary Materials)”

Fourth, while the EEG analysis in general provides interesting data, the link to the well-established CPP signal is not entirely convincing. CPP signals are usually identified and analyzed in a response-locked fashion, to distinguish them from other types of stimulus-locked potentials. One crucial feature here is that the CPPs in the different conditions reach a similar level just prior to the response. This is either not the case here, or the data are not shown in a format that allows the reader to identify these crucial features of the CPP. It is therefore questionable whether the reported signals indeed fully correspond to this decision-linked signal.

Fifth, the authors present some effective connectivity analysis to identify the neural mechanisms underlying the possible top-down drive due to communicated confidence. It is completely unclear how they select the "prefrontal cortex" signals here that are used for the transfer entropy estimations, and it is in fact even unclear whether the signals they employ originate in this brain structure. In the absence of clear methodical details about how these signals were identified and why the authors think they originate in the prefrontal cortex, these conclusions cannot be maintained based on the data that are presented.

Sixth, the description of the model fitting procedures and the parameter settings are missing, leaving it unclear for the reader how the models were "calibrated" to the data. Moreover, for many parameters of the biophysical model, the authors seem to employ fixed parameter values that may have been picked based on any criteria. This leaves the impression that the authors may even have manually changed parameter values until they found a set of values that produced the desired effects. The model would be even more convincing if the authors could for every parameter give the procedures that were used for fitting it to the data, or the exact criteria that were used to fix the parameter to a specific value.

Seventh, on a related note, the reader wonders about some of the decisions the authors took in the specification of their model. For example, why was it assumed that the parameters of interest in the three competing models could only be modulated by the partner's confidence in a linear fashion? A non-linear modulation appears highly plausible, so extreme values of confidence may have much more pronounced effects. Moreover, why were the confidence computations assumed to be finished at the end of the stimulus presentation, given that for trials with RTs longer than the stimulus presentation, the sensory information almost certainly reverberated in the brain network and continued to be accumulated (in line with the known timing lags in cortical areas relative to objective stimulus onset)? It would help if these model specification choices were better justified and possibly even backed up with robustness checks.

Eight, the fake interaction partners showed several properties that were highly unnatural (they did not react to the participant's confidence communications, and their response times were random and thus unrelated to confidence and accuracy). This questions how much the findings from this specific experimental setting would transfer to other real-life settings, and whether participants showed any behavioral reactions to the random response time variations as well (since several studies have shown that for binary choices like here, response times also systematically communicate uncertainty to others). Moreover, it is also unclear how the confidence convergence simulated in Figure 3d can conceptually apply to the data, given that the fake subjects did not react to the subject's communicated confidence as in the simulation.

Author Response

Joint Public Review

This manuscript utilizes Drosophila melanogaster as a model system to functionally characterize the role of genes previously associated with obstructive pulmonary disease (COPD) in epithelial barrier function. Using genetic and imaging approaches, the authors characterised a previously unrecognised role of intestinal Acetylcholine receptor (AchR) signalling, in the regulation of epithelial barrier function. The working model proposes that Acetylcholine (Ach) produced by enteroendocrine cells (EEs) and enteric neurons signals to AchR in enterocytes (ECs). This signalling activates the secretion of the Peritrophic membrane (PM) through the regulation of the exocytic protein Syt4. In this way, Ach/AchR signalling works to protect epithelial barrier function and organismal tolerance to ingested damaging agents, such as those causing oxidative stress.

Overall, the data presented support the main model of the paper: EC AchR activation is necessary to maintain epithelial barrier function. The evidence, however, on the mechanisms downstream of AchR, namely, the involvement of this signalling pathway in the regulation of Syt4 is weak.

The work in this manuscript represents an important proof of concept for the use of the Drosophila midgut as a model to functionally interrogate genes from human genetic association studies in pathologies affecting epithelial homeostasis.

We would like to thank the reviewers for their positive assessment of the significance of the study. The reviewers point out that the reported data support the conclusions of the manuscript and request additional studies to elucidate the downstream mechanism in more detail. We have now edited our manuscript according to the specific requests, including additional data and further clarifications of our model. We believe these new data and edits significantly improve the manuscript and hope that it is now acceptable for publication in eLife

Author Response

Reviewer #1 (Public Review):

Mano et. al. use a combination of behavioral, genetic silencing, and functional imaging experiments to explore the temporal properties of the optomotor response in Drosophila. They find a previously unreported inversion of the behavior under high contrast and luminance conditions and identify potential pathways mediating the effect.

Strengths:

Quantifications of optomotor behavior have been performed for many decades. Despite a large number of previous studies, the authors still find something fundamentally novel: under high contrast conditions and extended stimulation periods, the behavior becomes dynamic over time. The turning response shows an initial transient positive following response. The amplitude of the behavior then decreases and even inverts such that animals show an anti-directional rotation response. The authors systematically explore the stimulation feature space, including large ranges of spatial and temporal frequencies and conditions with high and low contrast. They also test two wild-type fly species and even compare experiments across two different labs and setups. From these data, it seems clear that the behavior is robust and largely depends on the brightness of the stimulation, rearing conditions, and genetic background. The authors discuss that these effects have not clearly been reported elsewhere beforehand, and convincingly argue why this may be the case.

In general, the presented behavioral quantifications illustrate the importance of further experimental studies of the temporal dynamics of behavior in response to dynamically varying stimulus features, across different stimulus types, genetic backgrounds, and model animal systems. It also illustrates the importance of relating the conditions that animals experience in the laboratory to the ones they would experience in the wild. As the authors mention, the brightness during a sunny day can reach values as high as 4000 cd/m2, while experimental stimulation in the lab has so far often been orders of magnitude below that.

The study then systematically explores potential neural elements involved in the behavior. Through a set of silencing experiments, they find that T4 and T5 neurons, as expected, are required for motion behaviors. On the other hand, silencing HS cells largely abolishes the 'classical' syn-directional response but leaves anti-directional turning intact. On the other hand, silencing CH cells abolishes the anti-directional response but leaves the syn-directional behavior intact. Through functional imaging in T4, T5, HS, and CH neurons, the authors could show that none of these neurons shows a response inversion depending on contrast level. Together, these experiments nicely illustrate that the dynamics do not seem to be computed within the early parts of visual processing, but they must happen on the level of the lobula plate or further downstream.

Weaknesses:

While the authors have already explored various parameters of the experiment, it would have been nice to see additional experiments regarding the initial adaptation phase. The experiments in Figure 2e, where the authors show front-to-back or back-to-front gratings before the rotation phase, are a good start. What would the behavioral dynamics look like if they had exposed animals to long periods of static high or low contrast gratings, whole field brightness, or darkness? Such experiments would surely help to better understand the stimulus features on which the adaptation elements operate. It would be interesting to explore to what degree such static stimuli impact the subsequent behavioral dynamics.

To address this question, we have added a new adaption condition, in which a high contrast, stationary sinusoidal grating is presented for 5 seconds before the high contrast rotational stimulus is presented (new Figure 2 – Supp. Fig. 1). We find that the turning looks identical to the case of a gray adapter. These results drive home the point that the direction of motion of the adapter is what matters most.

Given the dynamics of the behavior, it would probably also be worth looking at the turning dynamics after the stimulus has stopped. If direction-selective adaptation mechanisms are regulating the turning response, one may find long-lasting biases even in the absence of stimulation. If the authors have more data after the stimulus end, it would be good to further expand the time range by a few seconds to show if this is the case or not (for example, in Figure 1b).

We now show these dynamics in Figure 1. See Essential Revision #1.

Another important experiment could be to initially perform experiments in a closed-loop configuration, and then quickly switch to open-loop. The closed-loop configuration should allow the motion computing circuitry to adapt to the chosen environmental conditions. Explorations of the changes in turning response dynamics after such treatments should then enable further dissections of the mechanisms of adaptation. Closed-loop experiments under different contrast conditions have already been performed (for example, Leonhardt et al. 2016), which also showed complex response dynamics after stimulus on- and offset. It would be great to discuss the current open-loop experiments, and maybe some new closed-loop results, in relation to the previous work.

We have performed these suggested experiments; please see Essential Revision #2.

The authors mention the different rearing conditions, and there is one experiment in Figure S2 which mentions running experiments at 25 deg C. But it is not clear from the Methods at which temperature all other experiments have been performed. It is also not clear at which temperature the shibire block experiments were performed. As such experiments require elevated temperatures, I assume that all behavioral experiments have been performed at such levels? How high were those?

Our apologies for leaving out this important information. In DAC’s lab, behavioral experiments are run at 34-36ºC in a room maintaining ~50% relative humidity (this yields ~25% RH in the box with the experiment, as we now note in the methods). These conditions yield high quality, reproducible behavior, especially since this temperature elicits strong walking behavior. In TRC’s lab, behavioral experiments are similarly run at 34ºC in a room maintaining ~50% relative humidity (similarly with ~25% RH in the experimental box), for similar reasons. We have now added these details to the methods sections for each lab’s behavioral experiments.

What does the fly see before and after the stimulus (i.e. the gray boxes in all figures)? Are these periods of homogenous gray levels or are these non-moving gratings with the luminance and contrast of the subsequent stimulus? It would be important to add this information to the methods and to the figure illustrations or legends.

In the figures, gray is a uniform luminance screen that appears before and after the stimuli, with luminance matched to the mean stimulus luminance. We have now included this in the methods section where we describe how stimuli were generated in each lab.

It would be nice to discuss the potential location where the motion adaptation may be implemented in the brain. A small model scheme as an additional figure could further help to discuss how such computations may be mechanistically implemented, helping readers to think about future experimental dissections of the behavior.

Following this suggestion, we have created a diagram that shows a potential mechanistic implementation of the behavior observed, and summarizes our results (new Figure 6 – Supp. Fig. 2). There are many other possible alternatives that we do not show, including exactly how an opposing signal could ramp up under the conditions of these experiments. In the figure caption, we remind readers what locations have been excluded for this sort of computation. We reference this diagram where we discuss subtraction in the Discussion.

For setting up similar experiments in other labs, the authors need to better describe how they measured the luminance of the arena. Do they simply report the brightness delivered by the Lightcrafter system, or did they measure this with a lux-meter? If so, at which distance was the measurement performed and with which device? Given that the behavior is sensitive to the specific properties of the stimulus, it will be important to report these numbers carefully to enable other groups to reproduce effects.

In brief, since these are rear projection screens, we can easily measure light intensity by placing a power meter in front of the screen. This gives us the photon flux in watts, which can be converted to lumens by a standard conversion and then into candelas by making the approximation that our screen scatters into 2π steradians. Dividing by the sensor area gives us our desired candelas per square-meter. We have now added this methodology to the methods section.

Author Response

Reviewer #1 (Public Review):

Summary:

The study assesses the impact of testing contacts of cases in school classes when identified, rather than at the end of quarantine, on various outcomes such as secondary infections, tracing delay, and identification of the possible source of infection. The authors find that the intervention likely reduced tracing delay and increased the number of possible infection sources. However, due to unmeasured confounding, it remains unclear if secondary transmission actually decreased. The analysis requires clarification and further explanation in parts.

Major strengths and weaknesses:

The study benefits from the assessment of various outcomes in contact tracing in addition to changes in transmission, such as tracing delay, and the identification of putative infectors; however the assumption that other cases found in households are infectors of the index case rather than putative infectees, may introduce significant bias, but this is not mentioned in the Discussion despite being significant. It is difficult to understand the intervention in Figure 1 due to unclear labelling and incomplete descriptions in the caption. The authors mention that the same school class could be included multiple times for multiple outbreaks - was there a time cutoff for inclusion? I had a lot of trouble interpreting or reproducing the values given in Table 1. Firstly, the methods used to produce the RRs given are not described in the methods section of the paper. What are the outcomes - "classes" and "indexes" are poroly defined. Is this output from univariate or multivariate regression model, and what is the link function? I was also unable to reproduce the RRs listed in the table despite attempting several methods. The closest numbers I achieved were by crudely dividing the risks (e.g. for the RR for known infection source I took the ratio of indexes for which a school contact was suspected pre and post-intervention (644/1175)/(146/429) = 1.61), but if this is the case then the unknown class is by definition not the reference category. This is the same for the other RRs stated in the table. The methods used should be clarified and results updated if erroneous. The mediation analysis components and their relevance to the study could be better explained in the methods and results.

Achievement of aims and support for conclusions:

The authors partially achieved their aims by demonstrating a likely decrease in tracing delay and an increase in possible infection sources. However, the study's inability to determine if secondary transmission decreased due to unmeasured confounding limits the conclusiveness of the findings. The authors should reiterate the main numerical results in the first few paragraphs of the discussion.

Impact on the field and utility of methods and data:

This study has the potential to impact the field by highlighting the benefits of testing contacts earlier in school classes. The findings on reduced tracing delay and increased identification of infection sources can inform future strategies and interventions. However, clarity on the analysis methods, as well as the results, are necessary to ensure the utility and reliability of the findings.

We thank the reviewer for his encouraging comments, we completely agree with the interpretation of our findings. Nevertheless, the intervention under evaluation is not exactly as descried by the reviewer. In fact, the change of contact tracing targeted mostly the tracing in household cases. Investigation in schools used the immediate testing of all contacts already before the intervention, even if after the intervention the timeliness increased. It was in the household where we had a clear change with immediate testing of all asymptomatic family contacts.

The assumption of direction of infection: We understand the reviewer’s point and we agree that such an assumption would introduce an important bias. Nevertheless, we do not assume any direction of the infection. We only report the conclusions of the field investigation conducted during the school outbreak about a known source of infection for the index case.

On the contrary, in our conceptual framework, we make the hypothesis that introducing backward contact tracing for all cases in the community (mostly household infections) asymptomatic cases in school age were more promptly identified and this improved the surveillance of school outbreaks and possibly reduced transmission in school outbreaks. This increase in timeliness could occur whatever the direction of infection within the household was, i.e. from the symptomatic adult to the asymptomatic child or the other way round.

Figure 1: we completely changed figure 1 according to reviewer’s suggestions.

Table 1: it has been split in two tables, the first describe the characteristics of the classes and index cases and the outcomes of the outbreaks, and the second is a table showing the association between possible confounders and the main outcome. We are sorry; trying to make the paper shorter, we made the table very unclear.

Repeated outbreaks in the same class: we thank the reviewer for this point. We did not define a time limit to distinguish two episodes. The outbreaks were defined by the field investigations. If the class was involved in two investigations, public health operators firstly tried to assess if there was a direct link between the two. Actually, it was impossible that two outbreaks were considered independent if there was less than 21 days between the two index cases notifications. We added a sentence in the methods.

Mediation analysis rationale: we added a DAG to explain the mediation analysis, we also changed the results reporting following step by step the preliminary results to introduce the mediation analysis to justify the selection of the mediators and the confounders.

Discussion: we added the main findings in a quantitative way at the beginning of the discussion.

Reviewer #2 (Public Review):

This is a review of "Effect of an enhanced public health contact tracing intervention on the secondary transmission of SARS-CoV-2 in educational settings: the four-way decomposition analysis", by Djuric et al.

In late 2020, a province in northern Italy implemented a new testing regimen for all contacts of people known to have COVID-19, offering them SARS-CoV-2 testing immediately after the detection of the index case instead of at the end of a quarantine period. The authors of this study investigated whether this policy change reduced secondary transmission of SARS-CoV-2 in schools. In addition to studying this primary outcome, they examined two "process" outcomes; whether this policy of testing earlier enabled public health officials to more successfully identify the source of infection of the index case, and if the time interval from detection of the index case to testing of contacts in the educational setting reduced.

They concluded that the time between detection of the index case and testing of contacts did reduce before and after the policy change. Similarly, the proportion of cases for which the source of infection was identified also increased after the policy change. Both of these "process" indicators correlated with reduced secondary transmission, though only identifying the source of infection was associated with a statistically significant (at the 5% level) reduction in secondary transmission.

Strengths of this paper

Educational settings experienced significant disruption during the COVID-19 pandemic, and efforts to better understand the spread of SARS-CoV-2 in schools - and how to mitigate this spread - are of significant public health importance. This paper, therefore, addresses an important topic.

Additionally, the authors describe a detailed dataset comprising case and contact tracing data from over 1,600 index cases with in-school contacts. The richness of the data described in Table 1 provides a good opportunity to conduct a natural experiment on the potential impact of testing contacts immediately after exposure on secondary transmission. The authors also appropriately acknowledge that this interrupted time series study would be insufficient to provide causal information, given the potential for confounders.

Finally, the primary statistical method (a four-way decomposition analysis) was new to me, but - from the references cited - seems appropriate. Given the relative novelty of this method, more space could be dedicated to explaining it in the methods.

Weakness of this paper

Although the paper tackles an important topic with an appropriate dataset, the analyses feel insufficient to fully support the authors' conclusions.

First and most critically, it is difficult to understand exactly what the primary outcome of the study is. Both the median number of secondary cases per class and the proportion of classes that experienced any secondary transmission are presented in Table 1, but - at least in the unadjusted analyses - point in different directions regarding the impact of the effect of the intervention (albeit neither strongly). For example, before the policy change, the median number of secondary cases per index case is 2, while after the policy change, it has reduced to 1. In contrast, before the policy change 37% of classes experienced any secondary transmission, but after the policy change, this had increased to 39% of classes. In some of the adjusted analyses, "number of secondary cases" is stated as the outcome variable, but that is not fully defined. The "attack rate", which is well defined in the methods, could be one option for use as a consistent primary outcome, however, it is only provided for the total study population and the attack rates pre- or post-policy change are not presented or compared.

Additionally, although using a "process measure" as a secondary outcome could be valuable - especially in a natural experiment like this, where identifying a causal relationship with a complex outcome like secondary transmission will be difficult - it was somewhat unclear how the process measures described in this study were measured, or their validity. For example, the reduced time between detection of the index case and testing of contacts seems unsurprising, since the intervention itself is to test contacts immediately after the index case is identified. Additionally, the results describe reductions in median testing delay and median tracing delay, but only testing delay is defined in the methods.

Finally, there is existing published literature that provides additional context on the impact of testing on secondary transmission within schools that arguably provides a higher level of evidence than the current study, but is not cited by the authors. A key limitation of this study - which the authors acknowledge - is the interrupted time series nature of their study, which is open to confounding by other important factors that happened at the same time, including but not limited to: changes in overall incidence of COVID-19; viral evolution (e.g. the emergence of the Alpha variant (B.1.1.7) which occurred during this study and which significantly altered the risk of secondary transmission); the efficiency of the contact tracing system (including skill and size of the contact tracing workforce); and the availability of non-molecular diagnostic tests (e.g. lateral flow devices) that might allow individuals to change their behaviors even without enrolling in this study. Examples of alternative studies which might reduce some of this potential confounding include around 400 schools in Los Angeles County, California, USA, that implemented "test to stay" in 2021 and were compared to 1,600 schools that did not implement "test to stay" [https://www.cdc.gov/mmwr/volumes/70/wr/mm705152e1.htm] and a cluster-randomized trial of daily testing of exposed contacts to study in-school transmission in England, UK, also in 2021 [https://www.sciencedirect.com/science/article/pii/S0140673621019085]. Although these examples describe slightly different interventions involving enhanced testing of exposed contacts, they both compared educational settings with and without the intervention across the same time periods; and the UK study in particular has methodological advantages over this current paper, including randomization. While the findings in the current paper did not contradict these earlier, stronger papers, the example from this province should be placed in context with the totality of evidence around testing in schools.

We thank the reviewer for his encouraging and useful comments.

We have completely reframed Table 1 and split it in two separate tables. We have added suggested references.

According to the reviewer’s suggestions, we tried to better describe the main outcome and to justify our choice. We also added a definition of testing delay that was missing. We added a box explaining in plain language all the outputs of the mediation analysis. We improved reporting of the descriptive data in table 1, including attack rate.

Furthermore, we better explained the choice of process outcomes and how they were related to the main outcome a priori and what changes were expected under the hypothesis that the intervention worked correctly. In particular, we agree that a reduction in the time to testing was unsurprising, in fact, this was just to check that the intervention was actually and correctly implemented; increasing the proportion of index cases with a known source of infection (and the proportion of asymptomatic index cases, that was not identified in the initial protocol but we identified later as an important process indicator) is a process indicator suggesting that more index cases have been identified as a consequence of a household investigation, i.e. the change in tracing helped in early detection of school exposure.

Regarding the proportion of classes with secondary transmission, we added a sentence in the discussion explaining why we did not expect that this would change after the intervention. In fact, as described in the new figure 1, household contacts were immediately quarantined before as well as after the intervention, what changed is that they are timely identified as contacts and therefore school contacts are identified and isolated. Only if a secondary transmission in the class already occurred we could reduce transmission in the class, i.e. we are preventing tertiary cases not secondary. Nevertheless, the number of classes investigated is also expected to change, so it was difficult to predict if the proportion of investigated classes with transmission should increase or decrease.

In the discussion, we reported examples of studies that applied an experimental or semi-experimental design and thus overcame the main limits of our observational study. Nevertheless, we also highlighted that the intervention we are evaluating in this study was particularly difficult to be conducted in a trial or a semi-experimental setting, in fact, we are trying to evaluate a change in the contact tracing in the community that occurred during the peak of the second wave.

Author Response

Reviewer #1 (Public Review):

Briggs et al use a combination of mathematical modelling and experimental validation to tease apart the contributions of metabolic and electronic coupling to the pancreatic beta cell functional network. A number of recent studies have shown the existence of functional beta cell subpopulations, some of which are difficult to fully reconcile with established electrophysiological theory. More generally, the contribution of beta cell heterogeneity (metabolism, differentiation, proliferation, activity) to islet function cannot be explained by existing combined metabolic/electrical oscillator models. The present studies are thus timely in modelling the islet electrical (structural) and functional networks. Importantly, the authors show that metabolic coupling primarily drives the islet functional network, giving rise to beta cell subpopulations. The studies, however, do not diminish the critical role of electrical coupling in dictating glucose responsiveness, network extent as well as longer-range synchronization. As such, the studies show that islet structural and functional networks both act to drive islet activity, and that conclusions on the islet structural network should not be made using measures of the functional network (and vice versa).

Strengths:

• State-of-the-art multi-parameter modelling encompassing electrical and metabolic components.

• Experimental validation using advanced FRAP imaging techniques, as well as Ca2+ data from relevant gap junction KO animals.

• Well-balanced arguments that frame metabolic and electrical coupling as essential contributors to islet function.

• Likely to change how the field models functional connectivity and beta cell heterogeneity.

Weaknesses:

• Limitations of FRAP and electrophysiological gap junction measures not considered.

• Limitations of Cx36 (gap junction) KO animals not considered.

• Accuracy of citations should be improved in a few cases.

We thank reviewer 1 for their positive comments, including the many strengths in the approaches, arguments and impact. We do note the weaknesses raised by the reviewer and have addressed them following the comments below.

We would like to also note that when we refer to metabolic activity driving the functional network, we are not referring to metabolic coupling between beta cells. Rather we mean that two cells that show either high levels of metabolic activity (glycolytic flux) or that show similar levels metabolic activity will show increased synchronization and thus a functional network edge as compares to cells with elevated gap junction conductance. Increased metabolic activity would likely generate increased depolarizing currents that will provide an increased coupling current to drive synchronization; whereas similar metabolic activity would mean a given coupling current could more readily drive synchronized activity. We have substantially rewritten the manuscript to clarify this point.

Reviewer #2 (Public Review):

In their present work, Briggs et al. combine biophysical simulations and experimental recordings of beta cell activity with analyses of functional network parameters to determine the role played by gap-junctional coupling, metabolism, and KATP conductance in defining the functional roles that the cells play in the functional networks, assess the structure-function relationship, and to resolve an important current open question in the field on the role of so-called hub cells in islets of Langerhans.

Combining differential equation-based simulations on 1000 coupled cells with demanding calcium, NAPDH, and FRAP imaging, as well as with advanced network analyses, and then comparing the network metrics with simulated and experimentally determined properties is an achievement in its own right and a major methodological strength. The findings have the potential to help resolve the issue of the importance of hub cells in beta cell networks, and the methodological pipeline and data may prove invaluable for other researchers in the community.

However, methodologically functional networks may be based on different types of calcium oscillations present in beta cells, i.e., fast oscillations produced by bursts of electrical activity, slow oscillations produced by metabolic/glycolytic oscillations, or a mixture of both. At present, the authors base the network analyses on fast oscillations only in the case of simulated traces and on a mixture of fast and slow oscillations in the case of experimental traces. Since different networks may depend on the studied beta cell properties to a different extent (e.g., fast oscillation-based networks may, more importantly, depend on electrical properties and slow oscillationbased networks may more strongly depend on metabolic properties), it is important that in drawing the conclusions the authors separately address the influence of a cell's electrical and metabolic properties on its functional role in the network based on fast oscillations, slow oscillations, or a mixture of both.

We thank reviewer 2 for their positive comments, including addressing the importance of this study as it pertains to islet biology and acknowledging methodological complexities of this study. We also thank the reviewer for their careful reading and providing useful comments. We have integrated each comment into the manuscript. Most importantly, we have now extended our analysis to both fast and slow oscillations by incorporating an additional mathematical model of coupled slow oscillations and performing additional experimental analysis of fast, slow, and mixed oscillations.

Reviewer #3 (Public Review):

Over the past decade, novel approaches to understanding beta cell connectivity and how that contributes to the overall function of the pancreatic islet have emerged. The application of network theory to beta cell connectivity has been an extremely useful tool to understand functional hierarchies amongst beta cells within an islet. This helps to provide functional relevance to observations from structural and gene expression data that beta cells are not all identical.

There are a number of "controversies" in this field that have arisen from the mathematical and subsequent experimental identification of beta "hub" cells. These are small populations of beta cells that are very highly connected to other beta cells, as assessed by applying correlation statistics to individual beta cell calcium traces across the islet.

In this paper Briggs et al set out to answer the following areas of debate:

They use computational datasets, based on established models of beta cells acting in concert (electrically coupled) within an islet-like structure, to show that it is similarities in metabolic parameters rather than "structural" connections (ie proximity which subserves gap junction coupling) that drives functional network behaviour. Whilst the computational models are quite relevant, the fact that the parameters (eg connectivity coefficients) are quite different to what is measured experimentally, confirm the limitations of this model. Therefore it was important for the authors to back up this finding by performing both calcium and metabolic imaging of islet beta cells. These experimental data are reported to confirm that metabolic coupling was more strongly related to functional connectivity than gap junction coupling. However, a limitation here is that the metabolic imaging data confirmed a strong link between disconnected beta cells and low metabolic coupling but did not robustly show the opposite. Similarly, I was not convinced that the FRAP studies, which indirectly measured GJ ("structural") connections were powered well enough to be related to measures of beta cell connectivity.

The group goes on to provide further analytical and experimental data with a model of increasing loss of GJ connectivity (by calcium imaging islets from WT, heterozygous (50% GJ loss), and homozygous (100% loss). Given the former conclusion that it was metabolic not GJ connectivity that drives small world network behaviour, it was surprising to see such a great effect on the loss of hubs in the homs. That said, the analytical approaches in this model did help the authors confirm that the loss of gap junctions does not alter the preferential existence of beta cell connectivity and confirms the important contribution of metabolic "coupling". One perhaps can therefore conclude that there are two types of network behaviour in an islet (maybe more) and the field should move towards an understanding of overlapping network communities as has been done in brain networks.

Overall this is an extremely well-written paper which was a pleasure to read. This group has neatly and expertly provided both computational and experimental data to support the notion that it is metabolic but not "structural" ie GJ coupling that drives our observations of hubs and functional connectivity. However, there is still much work to do to understand whether this metabolic coupling is just a random epiphenomenon or somehow fated, the extent to which other elements of "structural" coupling - ie the presence of other endocrine cell types, the spatial distribution of paracrine hormone receptors, blood vessels and nerve terminals are also important.

We thank reviewer 3 for their positive comments, including the methodology, writing style, and the importance of this paper to the broader islet community. We thank the reviewer for their very in-depth and helpful comments. We have addressed each comment below and made significant changes to the manuscript according. We conducted more FRAP experiments and separated results into slow, fast, and mixed oscillations. We included analysis of an additional computational model that simulates slow calcium oscillations. Additionally, we substantially rewrote the paper to clarify that we are not referring to metabolic coupling and speak on the broader implications of network theory and our findings.

Reviewer #4 (Public Review):

This manuscript describes a complex, highly ambitious set of modeling and experimental studies that appear designed to compare the structural and functional properties of beta cell subpopulations within the islet network in terms of their influence on network synchronization. The authors conclude that the most functionally coupled cell subpopulations in the islet network are not those that are most structurally coupled via gap junctions but those that are most metabolically active.

Strengths of the paper include (1) its use of an interdisciplinary collection of methods including computer simulations, FRAP to monitor functional coupling by gap junctions, the monitoring of Ca2+ oscillations in single beta cells embedded in the network, and the use of sophisticated approaches from probability theory. Most of these methods have been used and validated previously. Unfortunately, however, it was not clear what the underlying premise of the paper actually is, despite many stated intentions, nor what about it is new compared to previous studies, an additional weakness.

Although the authors state that they are trying to answer 3 critical questions, it was not clear how important these questions are in terms of significance for the field. For example, they state that a major controversy in the field is whether network structure or network function mediates functional synchronization of beta cells within the islet. However, this question is not much debated. As an example, while it is known that there can be long-range functional coupling in islets, no workers in the field believe there is a physical structure within islets that mediates this, unlike the case for CNS neurons that are known to have long projections onto other neurons. Beta cells within the islets are locally coupled via gap junctions, as stated repeatedly by the authors but these mediate short-range coupling. Thus, there are clearly functional correlations over long ranges but no structures, only correlated activity. This weakness raises questions about the overall significance of the work, especially as it seems to reiterate ideas presented previously.

We thank reviewer 4 for their positive comments, including our multidisciplinary use of mathematical models and experimental imaging techniques. We have now included an additional model of slow oscillations (the Integrated Oscillator Model) to improve our conclusions. We also thank reviewer 4 for the insightful comments. We have carefully reviewed each comment and made significant changes to the manuscript accordingly. In particular, we have significantly rewritten the introduction and discussion attempting to clarify what is new in our manuscript and what is previously shown. Additionally, we agree with the reviewers’ sentiment that there is little debate over whether, for example, there are physical structures within the islet that mediate long-range functional connections. However, there is current debate over whether functional beta-cell subpopulations can dictate islet dynamics (see [11]–[13]). This debate can be framed by observing whether these functional subpopulations emerge from the islet due to physical connections (structural network) or something more nuisance (such as intrinsic dynamics). We have reframed the introduction and discussion to clarify this debate as well as more clearly state the premise of the paper.

Specific Comments

1). The authors state it is well accepted that the disruption of gap junctional coupling is a pathophysiological characteristic of diabetes, but this is not an opinion widely accepted by the field, although it has been proposed. The authors should scale back on such generalizations, or provide more compelling evidence to support such a claim.

Thank you for pointing this out, we have provided more specific citations and changes the wording from “well accepted” to “has been documented”. See Discussion page 13 lines 415-416.

2) The paper relies heavily on simulations performed using a version of the model of Cha et al (2011). While this is a reasonable model of fast bursting (e.g. oscillations having periods <1 min.), the Ca2+ oscillations that were recorded by the authors and shown in Fig. 2b of the manuscript are slow oscillations with periods of 5 min and not <1 min, which is a weakness of the model in the current context. Furthermore, the model outputs that are shown lack the well-known characteristics seen in real islets, such as fast-spiking occurring on prolonged plateaus, again as can be seen by comparing the simulated oscillations shown in Fig. 1d with those in Fig. 2b. It is recommended that the simulations be repeated using a more appropriate model of slow oscillations or at least using the model of Cha et al but employed to simulate in slower bursting.

The reviewer raises an important point and caveat associated with our simulated model and experimental data. This point was also made by other reviewers, and a similar response to this comment can be found elsewhere in response to reviewer 2 point 6. To address this comment, we have performed several additional experiments and analyses:

1) We collected additional Ca2+ (to identify the functional network and hubs) and FRAP data (to assess gap junction permeability) in islets which show either pure slow, pure fast, or mixed oscillations. We generated networks based on each time scale to compare with FRAP gap junction permeability data. We found that the conclusions of our first draft to be consistent across all oscillation types. There was no relationship between gap junction conductance, as approximated using FRAP, and normalized degree for slow (Figure 3j), fast (Figure 3 Supp 1d,e), or mixed (Figure 3 Supp 1g,h) oscillations. We also include discussion of these conclusions - See Results page 7 lines 184-186 and lines 188-191, Discussion page 12 lines 357-360.

2) We also performed additional simulations with a coupled ‘Integrated Oscillator Model’ which shows slow oscillations because of metabolic oscillations (Figure 2). We compared connectivity with gap junction coupling and underlying cell parameters. In this case, there is an association between functional and structural networks, with highly-connected hub cells showing higher gap junction conductance (Figure 2f) but also low KATP channel conductance (gKATP) (Figure 2e). However, there are some caveats to these findings – given the nature of the IOM model, we were limited to simulating smaller islets (260 cells) and less heterogeneity in the calcium traces was observed. Additional analysis suggests the greater association between functional and structural networks in this model was a result of the smaller islets, and the association was also dependent on threshold (unlike in the Cha-Noma fast oscillator model) robust. These limitations and results are discussed further (Discussion page 11 lines 344-354).

Additionally, in the IOM, the underlying cell dynamics of highly-connected hub cells are differentiated by KATP channel conductance (gKATP), which is different than in the fast oscillator model (differentiated by metabolism, kglyc). However this difference between models can be linked to differences in the way duty cycle is influenced by gKATP and kglyc (Figure 1h, Figure 2g). In each model there was a similar association between duty cycle and highly-connected hub cells. We also discuss these findings (Discussion page 11 lines 334-343).

Overall these results and discussion with respect to the coupled IOM oscillator model can be found in Figure 2, Results page 6 lines 128-156 and Discussion page 11 lines 332-354.

3) Much of the data analyzed whether obtained via simulation or through experiment seems to produce very small differences in the actual numbers obtained, as can be seen in the bar graphs shown in Figs. 1e,g for example (obtained from simulations), or Fig. 2j (obtained from experimental measurements). The authors should comment as to why such small differences are often seen as a result of their analyses throughout the manuscript and why also in many cases the observed variance is high. Related to the data shown, very few dots are shown in Figs. 1eg or Fig 4e and 4h even though these points were derived from simulations where 100s of runs could be carried out and many more points obtained for plotting. These are weaknesses unless specific and convincing explanations are provided.

We thank the reviewer for these comments, which are similar to those of reviewer 2 (point 4) and reviewer 3 (point 6). Indeed there is some variability between cells in both simulations and experiments related to the metabolic activity in hubs and non-hubs. The variability points to potentially other factors being involved in determining hubs beyond simply kglyc, including a minor role for gap junction coupling structural network and potentially cell position and other intrinsic factors. We now discuss this point – see Discussion page 12 lines 364-266.

The differences between hubs and nonhubs appear small because the value of kglyc is very small. For figure 1e, the average kglyc for nonhubs was 1.26x10-4 s-1 (which is the average of the distribution because most cells are non hubs) while the average kglyc for hubs was 1.4x10-4 s-1 which is about half of a standard deviation higher. The paired t-test controls for the small value of average kglyc.

For simulation data each of the 5 dots corresponds to a simulated islet averaged over 1000 cells (or 260 cells for coupled IOM). The computational resources are high to generate such data so it is not feasible to conduct 100s of runs. Again, we note the comparisons between hubs and non-hubs are paired, and we find statistically significant differences for kglyc in figure 1 using only 5 paired data points. That we find these differences indicates the substantial difference between hubs and non-hubs. This is further supported all effect sizes being much greater than 0.8 for all significantly different findings (Cha Noma - kglyc: 2.85, gcoup: 0.82) (IOM: gKATP: 1.27, gcoup: 2.94) – We have included these effect sizes in the captions see Figure 1 and 2 captions (pages 34, 36)

To consider all of the available data rather than the average across an entire islet, we created a kernel density estimate the kglyc for hubs and nonhubs created by concatenating every single cell in each of the five islets. A kstest results in a highly significant difference (P<0.0001) between these two distributions.

Author response image 1.

4) The data shown in Fig. 4i,j are intended to compare long-range synchronization at different distances along a string of coupled cells but the difference between the synchronized and unsynchronized cells for gcoup and Kglyc was subtle, very much so.

Thank you for pointing out these subtle differences. The y-axis scale for i and j is broad to allow us to represent all distances on a single plot. After correction for multiple comparison, the differences were still statistically significant. As the reviewer mentioned in point 3, each plot contains only five data points, each of which represent the average of a single simulated islet, therefore we are not concerned about statistical significance coming from too large of a sample size. We also checked the differences between synchronized and nonsynchronized cell pairs in figure 4 panels e and h (now figure 5 e, h). These are the same data as i and j but normalized such that all of the distances could be averaged together. We again found statistical significance between synchronized and non-synchronized cell pairs. As can be seen in Author response image 2 the difference between synchronized and non-synchronized cell pairs is greater than the variability between simulated islets. Thus, in this case the variability is not substantial.

Author response image 2.

5) The data shown in Fig. 5 for Cx36 knockout islets are used to assess the influence of gap junctional coupling, which is reasonable, but it would be reassuring to know that loss of this gene has no effects on the expression of other genes in the beta cell, especially genes involved with glucose metabolism.

This is an important point. Previous studies have assessed that no significant change in NAD(P)H is observed in Cx36 deficient islets – see Benninger et al J.Physiol 2011 [14]. Islet architecture is also retained. Further the insulin secretory response of dissociated Cx36 knockout beta cells is the same as that of dissociated wildtype beta cells, further indicating no significant defect in the intrinsic ability of the beta cell to release insulin – see Benninger et al J.Physiol 2011 [14]. We now Mention these findings in the discussion. See Discussion page 14 lines 459-464.

6) In many places throughout the paper, it is difficult to ascertain whether what is being shown is new vs. what has been shown previously in other studies. The paper would thus benefit strongly from added text highlighting the novelty here and not just restating what is known, for instance, that islets can exhibit small-world network properties. This detracts from the strengths of the paper and further makes it difficult to wade through. Even the finding here that metabolic characteristics of the beta cells can infer profound and influential functional coupling is not new, as the authors proposed as much many years ago. Again, this makes it difficult to distill what is new compared to what is mainly just being confirmed here, albeit using different methods.

Thank you for the suggestion, we have made significant modifications throughout the Introduction, Discussion and Results to be clearer about what is known from previous work and what is newly found in this manuscript.

Reviewer #5 (Public Review):

The authors use state-of-the-art computation, experiment, and current network analysis to try and disaggregate the impact of cellular metabolism driving cellular excitability and structural electrical connections through gap junctions on islet synchronization. They perform interesting simulations with a sophisticated mathematical model and compare them with closely associated experiments. This close association is impressive and is an excellent example of using mathematics to inform experiments and experimental results. The current conclusions, however, appear beyond the results presented. The use of functional connectivity is based on correlated calcium traces but is largely without an understood biophysical mechanism. This work aims to clarify such a mechanism between metabolism and structural connection and comes out on the side of metabolism driving the functional connectivity, but both are required and more nuanced conclusions should be drawn.

We thank reviewer 5 for their positive comments, including our multifaceted experimental and computational techniques. We also found the reviewers careful reading and thoughtful comments to be very helpful and we have worked to integrate each comment into our manuscript. It is evident from the reviewer comments that we did not clearly explain what was meant by our conclusions concerning the functional network reflecting metabolism rather than gap junctions. We have conducted significant rewriting to show that we are not concluding that communication (metabolic or electric) occurs due to conduits other than gap junctions. Rather, our data suggest that the functional network (which reflects calcium synchronization) reflects intrinsic dynamics of the cells, which include metabolic rates, more than individual gap junction connections.

References referred to in this response to reviewers document:

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[2] N. L. Farnsworth, A. Hemmati, M. Pozzoli, and R. K. Benninger, “Fluorescence recovery after photobleaching reveals regulation and distribution of connexin36 gap junction coupling within mouse islets of Langerhans,” The Journal of physiology, vol. 592, no. 20, pp. 4431–4446, 2014.

[3] C.-L. Lei, J. A. Kellard, M. Hara, J. D. Johnson, B. Rodriguez, and L. J. Briant, “Beta-cell hubs maintain Ca2+ oscillations in human and mouse islet simulations,” Islets, vol. 10, no. 4, pp. 151–167, 2018.

[4] N. R. Johnston et al., “Beta cell hubs dictate pancreatic islet responses to glucose,” Cell metabolism, vol. 24, no. 3, pp. 389–401, 2016.

[5] V. Kravets et al., “Functional architecture of pancreatic islets identifies a population of first responder cells that drive the first-phase calcium response,” PLoS Biology, vol. 20, no. 9, p. e3001761, 2022.

[6] H. Ren et al., “Pancreatic α and β cells are globally phase-locked,” Nature Communications, vol. 13, no. 1, p. 3721, 2022.

[7] A. Stožer et al., “From Isles of Königsberg to Islets of Langerhans: Examining the function of the endocrine pancreas through network science,” Frontiers in Endocrinology, vol. 13, p. 922640, 2022.

[8] J. Zmazek et al., “Assessing different temporal scales of calcium dynamics in networks of beta cell populations,” Frontiers in physiology, vol. 12, p. 337, 2021.

[9] M. E. Corezola do Amaral et al., “Caloric restriction recovers impaired β-cell-β-cell gap junction coupling, calcium oscillation coordination, and insulin secretion in prediabetic mice,” American Journal of Physiology-Endocrinology and Metabolism, vol. 319, no. 4, pp. E709–E720, 2020.

[10] J. M. Dwulet, J. K. Briggs, and R. K. P. Benninger, “Small subpopulations of beta-cells do not drive islet oscillatory [Ca2+] dynamics via gap junction communication,” PLOS Computational Biology, vol. 17, no. 5, p. e1008948, May 2021, doi: 10.1371/journal.pcbi.1008948.

[11] B. E. Peercy and A. S. Sherman, “Do oscillations in pancreatic islets require pacemaker cells?,” Journal of Biosciences, vol. 47, no. 1, pp. 1–11, 2022.

[12] G. A. Rutter, N. Ninov, V. Salem, and D. J. Hodson, “Comment on Satin et al.‘Take me to your leader’: an electrophysiological appraisal of the role of hub cells in pancreatic islets. Diabetes 2020; 69: 830–836,” Diabetes, vol. 69, no. 9, pp. e10–e11, 2020.

[13] L. S. Satin and P. Rorsman, “Response to comment on satin et al.‘Take me to your leader’: An electrophysiological appraisal of the role of hub cells in pancreatic islets. Diabetes 2020; 69: 830–836,” Diabetes, vol. 69, no. 9, pp. e12–e13, 2020.

[14] R. K. Benninger, W. S. Head, M. Zhang, L. S. Satin, and D. W. Piston, “Gap junctions and other mechanisms of cell–cell communication regulate basal insulin secretion in the pancreatic islet,” The Journal of physiology, vol. 589, no. 22, pp. 5453–5466, 2011.

[15] R. Fried, Erectile dysfunction as a cardiovascular impairment. Academic Press, 2014. [16] T. Pipatpolkai, S. Usher, P. J. Stansfeld, and F. M. Ashcroft, “New insights into KATP channel gene mutations and neonatal diabetes mellitus,” Nature Reviews Endocrinology, vol. 16, no. 7, pp. 378–393, 2020.

[17] A. M. Notary, M. J. Westacott, T. H. Hraha, M. Pozzoli, and R. K. P. Benninger, “Decreases in Gap Junction Coupling Recovers Ca2+ and Insulin Secretion in Neonatal Diabetes Mellitus, Dependent on Beta Cell Heterogeneity and Noise,” PLOS Computational Biology, vol. 12, no. 9, p. e1005116, Sep. 2016, doi: 10.1371/journal.pcbi.1005116.

[18] J. V. Rocheleau, G. M. Walker, W. S. Head, O. P. McGuinness, and D. W. Piston, “Microfluidic glucose stimulation reveals limited coordination of intracellular Ca2+ activity oscillations in pancreatic islets,” Pro ceedings of the National Academy of Sciences, vol. 101, no. 35, pp. 12899–12903, 2004. [19] R. K. Benninger, M. Zhang, W. S. Head, L. S. Satin, and D. W. Piston, “Gap junction coupling and calcium waves in the pancreatic islet,” Biophysical journal, vol. 95, no. 11, pp. 5048–5061, 2008.

Author Response

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

Reviewer #1 (Public Review):

This article is interested in how butterfly, or more precisely, butterfly wing scale precursor cells, each make precisely patterned ultrastructures made of chitin.

To do this, the authors sought to use the butterfly Parides eurimedes, a papilionid swallowtail, that carries interesting, unusual structures made of 1) vertical ridges, that lack a typical layered stacking arrangement; and 2) deep honeycomb-like pores. These two features make the organism chosen a good point of comparison with previous studies, including classic papers that relied on electronic microscopy (SEM/TEM), and more recent confocal microscopy studies.

The article shows good microscopy data, including detailed, dense developmental series of staining in the Parides eurimedes model. The mix of cell membrane staining, chitin precursor, and F-actin staining is well utilized and appropriately documented with the help of 3D-SIM, a microscopy technique considered to provide super-resolution (here needed to visualize sub-cellular processes).

The key message from this article is that F-actin filaments are later repurposed, in papilionid butterflies, to finish the patterning of the inter-ridge space, elaborating new structures (this was not observed so far in other studies and organisms). The model proposed in Figure 6 summarized these findings well, with F-actin reshaping it itself into a tulip that likely pulls down a chitin disk to form honeycombs. These interpretations of the microscopy data are interesting and novel.

There are two other points of interest, that deserve future investigation:

1) The authors performed immunolocalizations of Arp2 and pharmacological inhibitions of Arp2/3, and found some possible effect on honeycomb lattice development. The inter-ridge region of the butterfly Papilio polytes, which lacks these structures, did not seem to be affected by drug treatments. Effects where time- dependent, which makes sense. These data provide circumstantial evidence that Arp2/3 is involved in the late role of F-actin formation or re-organisation.

2) The authors perform a comparative study in additional papilionids (Fig. 6 in particular). I find these data to be quite limited without a dense sampling, but they are nonetheless interesting and support a second-phase role of F-actin re- organisation.

The article is dense, well produced and succinctly written. I believe this is an interesting and insightful study on a complex process of cell biology, that inspires us to look at basic phenomena in a broader set of organisms.

We thank the reviewer for the positive appraisal.

Reviewer #2 (Public Review):

The manuscript by Seah and Saranathan investigates the cell-based growth mechanism of so called honeycomb-structures in the upper lamina of papilionid wing scales by investigating a number of different species. The authors chose Parides eurimedes as a focus species with the developmental pathway of five other papilionid as a comparative backup. Through state-of-the-art microscopy images of different developmental steps, the author find that the intricate f-actin filaments reorganise, support cuticular discs that template the air holes that form the honeycomb lattice. The manuscript is well written and easy to follow, yet based on a somewhat limited sample size for their focus species, limiting attempts to suppress expression and alter structure shape.

The fact that the authors find a novel reorganisation mechanism is exciting and warrants further research, e.g. into the formation of other microscale features or smaller scale structures (e.g. the mentioned gyroid networks).

We thank the reviewer for the positive appraisal.

The authors place their results in the discussion in the light of current literature (although the references could be expanded further to include the breadth of the field). However, the mechanistic explanation completely ignores the mechanical properties of the membranes as an origin of some of the observed phenomena (see McDougal's work for example) and places the occurence of some features into Turing patterns and Ostwald ripening, which I find somewhat unlikely and I suggest that the authors discover this aspects further in the discussion.

We thank the reviewer for these suggestions. We have added more references from the current literature to more accurately reflecting the breadth of the field. McDougal et al. 2021. discuss the nature of biomechanical forces (differential growth and buckling) on the membrane and deposited cuticle shaping the formation of longitudinal ridges. However, here it is the invagination of the plasma membrane bearing the deposited cuticle that is our main concern. Nevertheless, we agree future studies should indeed consider the mechanical properties of the membranes, in addition, to explain some of the observed features. We have clarified this in our discussion.

I have little concerns regarding the experimental approach beyond the somewhat limited sample size. One thing the authors should more clearly mention are the pupation periods for all investigated species as only the periods for two species are named.

Yes, unfortunately, we were only able to obtain pupae with pupation dates for two species. We have clarified this point in the methods.

Reviewer #1 (Recommendations For The Authors):

Suggestion for improvement.

I recommend adopting a magenta/green (or orange/azure) color scheme to make the figures accessible to most color vision types. This does not require re-doing the figure and could be processed on the rendered JPG/TIF figures with the following procedure :

1) open the rendered figures in Photoshop in RGB mode

2) go to Channel Mixer

3) Select Output Channel : Blue

4) set Blue 100%-->0% and Red 0-->100%

This will change Red to Magenta without affecting luminosity.

Similar solutions should be available in other software including GIMP.

Of note this is a late fix and ideally, color encoding could be done upstream in the microscopy file extraction software (e.g. Fiji), but I do not think this heavier solution is needed here.

We thank the reviewer for this suggestion. In order to be more inclusive, we have redone the figures and videos in a yellow+magenta color scheme.

Reviewer #2 (Recommendations For The Authors):

References: Some literature is missing that could be considered by the authors e.g.

https://doi.org/10.1098/rstb.2020.0505 https://doi.org/10.1101/2023.06.01.542791

https://doi.org/10.1098/rsfs.2011.0082 https://doi.org/10.1557/mrs.2019.21

https://iopscience.iop.org/article/10.1088/2040- 8986/aaff39/meta https://doi.org/10.1364/OE.20.008877

We have added more references as suggested.

Placing the captions next to the figures, particularly in the SI will help accessibility.

We agree. We believe this would be done during article production.

113: chiefly?

We have replaced ‘chiefly’ with ‘focusing mainly on’.

160: how do you know the scales are more scletorized already? Just because it's later in development?

Yes, that is what we are alluding to here. We have made edits to clarify this sentence.

186: Specify sample size.

We have specified the sample size ‘(N = 15)’ here.

309: Multilayered cover scales would be more accurate.

Thanks for the suggestion. We have changed ‘structurally-colored cover scales’ to ‘multilayered cover scales’ as suggested.

Please check the literature list again for accurate references.

Thanks for the suggestion. We have gone through the references and fixed any missing information.

Author Response:

Thank you very much for selecting our paper for peer review and for the thorough evaluation of our manuscript. We appreciate your assessment and the reviewers’ comments that value our work and identify important points that will enable us to improve the paper. We are now working on key experiments to further test the hypothesis that ROCK is essential for the formation, growth, and morphology of the sea urchin larval skeleton. We will address the reviewers’ comments in detail in the revised version of the paper that we will submit after completing the experiments, but for now, there are two points we would like to clarify.

We thank the first reviewer for the appreciation of this paper and of our previous work where we studied calcium vesicle dynamics in whole embryos (Winter et al, Plos Com Biol 2021). In Winter et al 2021, we found that the skeleton (spicules) doesn’t grow when the embryos are immobilized in either control or treated embryos. As a consequence, we cannot determine the role of ROCK in vesicle trafficking and exocytosis based on experiments conducted in whole embryos. We are developing an alternative assay for vesicle tracking using cell cultures, but that is beyond the scope of this current work.

As for the second reviewer’s criticism of the usage of Y-27632 to block ROCK activity: The ROCK inhibitor concentrations we used (30-80µM) are similar the those commonly used in mammalian systems and in Drosophila to block ROCK activity, for example: (Becker et al., 2022; Canellas-Socias et al., 2022; Fischer et al., 2009; Kagawa et al., 2022; Segal et al., 2018; Su et al., 2022). The manufactory datasheet indicates that: “Y-27632 dihydrochloride is a selective ROCK inhibitor (Ki values are 0.14-0.22, 0.3, 25, 26 and > 250 μM for ROCK1 (p160 ROCK), ROCK2, PKA, PKC and MLCK respectively)”. That is, the affinities of Y-27632 for ROCK kinases are at least 100 times higher than those for PKC, PKA, and MLCK. Furthermore, these Ki values are based on biochemistry assays where the activity of the inhibitor is tested in-vitro with the purified protein. Therefore, these concentrations are not relevant to cell or embryo cultures where the inhibitor has to penetrate the cells and affect ROCK activity in-vivo. Y-27632 activity was studied both in-vitro and in-vivo in Narumiya, Ishizaki and Ufhata, Methods in Enzymology 2000 (Narumiya et al., 2000). This paper reports similar concentrations to the ones indicated in the manufactory data sheet for the in-vitro experiments, but shows that 10µM concentration or higher are effective in cell cultures. As stated above, we will add additional experimental verifications to the revised version, but even at this stage, the concentrations we used and the agreement between our pharmacological and genetic perturbations suggests that the affected protein is indeed ROCK.

We share the reviewers and editors wish to identify the molecular targets of ROCK and the specific cellular processes that ROCK is involved in, and we are actively working on achieving this goal. However, we believe that this paper is an important step towards illuminating the cellular components that participate in biomineral construction and the feedback between the cellular machinery and gene expression.

Best,

Smadar, in the name of all co-authors.

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• Fischer, R.S., Gardel, M., Ma, X., Adelstein, R.S., Waterman, C.M., 2009. Local cortical tension by myosin II guides 3D endothelial cell branching. Curr Biol 19, 260-265.
• Kagawa, H., Javali, A., Khoei, H.H., Sommer, T.M., Sestini, G., Novatchkova, M., Scholte Op Reimer, Y., Castel, G., Bruneau, A., Maenhoudt, N., Lammers, J., Loubersac, S., Freour, T., Vankelecom, H., David, L., Rivron, N., 2022. Human blastoids model blastocyst development and implantation. Nature 601, 600-605.
• Narumiya, S., Ishizaki, T., Uehata, M., 2000. Use and properties of ROCK-specific inhibitor Y-27632. Methods Enzymol 325, 273-284.
• Segal, D., Zaritsky, A., Schejter, E.D., Shilo, B.Z., 2018. Feedback inhibition of actin on Rho mediates content release from large secretory vesicles. J Cell Biol 217, 1815-1826.
• Su, Y., Huang, H., Luo, T., Zheng, Y., Fan, J., Ren, H., Tang, M., Niu, Z., Wang, C., Wang, Y., Zhang, Z., Liang, J., Ruan, B., Gao, L., Chen, Z., Melino, G., Wang, X., Sun, Q., 2022. Cell-in-cell structure mediates in-cell killing suppressed by CD44. Cell Discov 8, 35.