Author response:

Reviewer #1 (Public review):

Summary:

The topic of nanobody-based PET imaging is important and holds great potential for real-world applications since nanobodies have many advantages over full sized immunoglobulins and small molecules.

Strengths:

The submitted manuscript contains quite a bit of interesting data from a collaborative team of well-respected researchers. The authors are to be congratulated for presenting results that may not have turned out the way they had hoped, and doing so in a transparent fashion.

Weaknesses:

However, the manuscript could be considered to be a collection of exploratory findings rather than a complete and mature scientific exposition. Most of the sample sizes were 3 per group, which is fine for exploratory work, but insufficient to draw strong statistically robust conclusions for definitive results.

We thank reviewer #1 for the  review of our work. We appreciate reviewer’s #1 comment on our intent to publish our results in the most transparent fashion, which is the case. We would point out that due to the technical challenges and cost of generating all the different nanobody-radiometal tracer conjugates, we included 3 repeats per group, which is the minimum required  to perform statistical comparisons. We plan to add additional controls to the manuscript that were not initially included to limit the length of the manuscript. These additional controls  will lend more weight to our conclusions.

Reviewer #2 (Public review):

Summary:

This is a strong and well-described study showing for the first time the use and publicly available resources to use a specific PET tracer to track proliferating transplanted cells in vivo, in a full murine immunecompetent environment.

In this study the authors described a previously developed set of VHH-based PET tracers to track transplants (cancer cells, embryo's) in a murine immune-competent environment.

Strengths:

Unique set of PET tracer and mouse strain to track transplanted cells in vivo without genetic modification of the transplanted cells. This is a unique asset, and a first-in-kind.

Weaknesses:

- Some methodological aspects and controls are missing

- No clinical relevance?

We thank reviewer #2 for their review of our work. We support reviewer’s 2 view on the strength of being able to track transplanted cells in vivo without the need of any sort of manipulation of the transferred cells.  We plan to add additional controls to the manuscript that were not initially included to limit the length of the manuscript. These additional controls will lend more weight to our conclusions. We emphasize that although no clear clinical applications immediately derive  from our studies, this work  still offers better-suited tools for pre-clinical studies that require the ability to track transplanted cells in in vivo . We will resubmit a revised version shortly.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this manuscript, the authors recorded cerebellar unipolar brush cells (UBCs) in acute brain slices. They confirmed that mossy fiber (MF) inputs generate a continuum of UBC responses. Using systematic and physiological trains of MF electrical stimulation, they demonstrated that MF inputs either increased or decreased UBC firing rates (UBC ON vs. OFF) or induced complex, long-lasting modulation of their discharges. The MF influence on UBC firing was directly associated with a specific combination of metabotropic glutamate receptors, mGluR2/3 (inhibitory) and mGluR1 (excitatory). Ultimately, the amount and ratio of these two receptors controlled the time course of the effect, yielding specific temporal transformations such as phase shifts.

Overall, the topic is compelling, as it broadens our understanding of temporal processing in the cerebellar cortex. The experiments are well-executed and properly analyzed.

Strengths:

(1) A wide range of MF stimulation patterns was explored, including burst duration and frequency dependency, which could serve as a valuable foundation for explicit modeling of temporal transformations in the granule cell layer.

(2) The pharmacological blockade of mGluR2/3, mGluR1, AMPA, and NMDA receptors helped identify the specific roles of these glutamate receptors.

(3) The experiments convincingly demonstrate the key role of mGluR1 receptors in temporal information processing by UBCs.

Weaknesses:

(1) This study is largely descriptive and represents only a modest incremental advance from the previous work (Guo et al., Nat. Commun., 2021). 

We feel that the present study is a major advance.  It builds on (Guo et al., Nat. Commun., 2021) in which we examined the effects of bursts of 20 stimuli at 100 spk/s.  In that study we found that differential expression of mGluR1 and mGluR2 let to a continuum of temporal responses in UBCs, but AMPARs make a minimal contribution for such bursts. It was not known how UBCs transform realistic mossy fiber input patterns. Here we provide a comprehensive evaluation of a wide range of input patterns that include a range of bursts comprised of 1-20 stimuli, sustained stimulation with stimulation of 1 spk/s to 60 spk/s. This more thorough assessment of UBC transformations combined with a pharmacological assessment of the contributions of different glutamate receptor subtypes provided many new insights: 

• We found that UBC transformations are comprised of two different components: a slow temporally filtered component controlled by an interplay of mGluR1 and mGluR2, and a second component mediated by AMPARs that can convey spike timing information. NMDARs do not make a major contribution to UBC firing. The finding that UBCs simultaneously convey two types of signals, a slow filtered response and responses to single stimuli, has important implications for the computational potential of UBCs and fundamentally changes the way we think about UBCs.  

• We found that with regard to the slow filtered component mediated by mGluR1 and mGluR2, we could extend the concept of a continuum of responses evoked by 20 stimuli at 100 spk/s (Guo et al., Nat. Commun., 2021) to a wide range of stimuli. It was not a given that this would be the case.   

• The contributions of AMPARs was surprising. Even though snRNAseq data did not reveal a gradient of AMPAR expression across the population of UBCs (Guo et al., Nat. Commun., 2021), we found that there was a gradient of AMPA-mediated responses, and that the AMPA component was also most prominent in cells with a large mGluR1 component. Our finding that AMPAR accessory proteins exhibit a gradient across the population, which could account for the gradient of AMPAR responses, will prompt additional studies to test their involvement. 

(2) The MF activity used to mimic natural stimulation was previously collected in primates, while the recordings were conducted in mice.

Our first task was to determine the firing properties of mossy fibers under physiological conditions in UBC rich cerebellar regions. Previous studies have estimated this in anesthetized mice using whole cell granule cell recordings (Arenz et al., 2008; Witter & De Zeeuw 2015). However, for assessing firing patterns during awake behavior, we felt that the most comprehensive data set available in a UBC rich cerebellar region was for mossy fibers involved in smooth pursuit in monkeys (David J. Herzfeld and Stephen G. Lisberger). This revealed the general features of mossy fiber firing that helped us design stimulus patterns to thoroughly probe the properties of MF to UBC transformations. The firing patterns are designed to investigate the transformations for a wide range of activity patterns and have important general implications for UBC transformations that are likely applicable to UBCs in different species that are activated in different ways.   

(3) Inhibition was blocked throughout the study, reducing its physiological relevance.

The reviewer correctly brings up the very important issue of inhibition in shaping UBC responses.  It is well established that UBCs are inhibited by Golgi cells (Rousseau et al., 2012), and we recently showed that some UBCs are also inhibited by PCs (Guo et al., eLife, 2021). This will undoubtedly influence the firing of UBCs in vivo. We considered examining this issue, but felt that brain slice experiments are not well suited to this. In contrast to MF inputs that can be activated with a realistic activity pattern, it is exceedingly difficult to know how Golgi cells and Purkinje cells are activated under physiological conditions. Each UBC is activated by a single mossy fiber, but inhibition is provided by Golgi cells that are activated by many mossy fibers and granule cells, and PCs that are controlled by many granule cells and many other PCs. In addition, we found that many Golgi cells do not survive very well in slices, and the axons of many PCs are severed in brain slice. Although limitations of the slice preparation prevent us from determining the role of inhibition in shaping UBC responses, we have added a section to the discussion in which we address the important issue of inhibition and UBC responses.   

Reviewer #2 (Public review):

This study addresses the question of how UBCs transform synaptic input patterns into spiking output patterns and how different glutamate receptors contribute to their transformations. The first figure utilizes recorded patterns of mossy fiber firing during eye movements in the flocculus of rhesus monkeys obtained from another laboratory. In the first figure, these patterns are used to stimulate mossy fibers in the mouse cerebellum during extracellular recordings of UBCs in acute mouse brain slices. The remaining experiments stimulate mossy fiber inputs at different rates or burst durations, which is described as 'mossy-fiber like', although they are quite simpler than those recorded in vivo. As expected from previous work, AMPA mediates the fast responses, and mGluR1 and mGluR2/3 mediate the majority of longer-duration and delayed responses. The manuscript is well organized and the discussion contextualizes the results effectively.

The authors use extracellular recordings because the washout of intracellular molecules necessary for metabotropic signaling may occur during whole-cell recordings. These cell-attached recordings do not allow one to confirm that electrical stimulation produces a postsynaptic current on every stimulus. Moreover, it is not clear that the synaptic input is monosynaptic, as UBCs synapse on one another. This leaves open the possibility that delays in firing could be due to disynaptic stimulation. Additionally, the result that AMPAmediated responses were surprisingly small in many UBCs, despite apparent mRNA expression, suggests the possibility that spillover from other nearby synapses activated the higher affinity extrasynaptic mGluRs and that that main mossy fiber input to the UBC was not being stimulated. For these reasons, some whole-cell recordings (or perforated patch) would show that when stimulation is confirmed to be monosynaptic and reliable it can produce the same range of spiking responses seen extracellularly and that AMPA receptormediated currents are indeed small or absent in some UBCs.

We appreciate the reviewer’s concerns regarding the reliability of mossy fiber activation, the possibility of glutamate spillover from other synapses, and the possibility of disynaptic activation involving stimulation of MFàUBCàUBC connections. We examined these issues in a previous study (Guo et al., Nat. Commun., 2021).  We did on-cell recordings and followed that up with whole cell voltage clamp recordings from the same cell (Guo et al., Nat. Commun., 2021, Fig. 5), and there was good agreement with the amplitude and timing of spiking and the time course and amplitudes of the synaptic currents.  We also compared responses evoked by focal glutamate uncaging over the brush and MF stimulation (Guo et al., Nat. Commun., 2021, Fig. 4). We found that the time courses and amplitudes of the responses were remarkably similar. This strongly suggests that the responses we observe do not reflect disynaptic activation (MFàUBCàUBC connections). We also showed that the responses were all-or-none: at low intensities no response was evoked, as the intensity of extracellular stimulation was increased a large response was suddenly evoked at a threshold intensity and further increases in intensity did not increase the amplitude of the response (Guo et al., Nat. Commun., 2021, Extended data Fig. 1).  We can be well above threshold and still excite the same response, and as a result we do not see stereotyped indications of an inability to stimulate during prolonged high frequency activation.  We recognize the importance of these issues, so we have  added a section dealing explicitly with these issues (pp. 15-16).  

A discussion of whether the tested glutamate receptors affected the spontaneous firing rates of these cells would be informative as standing currents have been reported in UBCs. It is unclear whether the firing rate was normalized for each stimulation, each drug application, or each cell. It would also be informative to report whether UBCs characterized as responding with Fast, Mid-range, Slow, and OFF responses have different spontaneous firing rates or spontaneous firing patterns (regular vs irregular).

The spontaneous firing of UBCs is indeed an interesting issue that is deserving of further investigation. It is not currently known how spontaneous firing at rest is regulated in UBCs, however, in previous work we have shown that there is great diversity in the rates across the population of UBCs in the dorsal cochlear nucleus (Huson & Regehr, JNeurosci, 2023, Fig. 4). Unfortunately, during the kind of sustained high-frequency stimulation protocols (as used in this study) spontaneous firing rates tend to increase. This is likely an effect of residual receptor activation. As such, our current dataset is not suitable to performing in depth analysis of the effects of the different glutamate receptors on spontaneous firing rates. As this study aims to explore UBC responses to MF inputs we feel that specific experiments to address the issue of spontaneous firing rates are outside of the scope.

As the reviewers points out there are indeed different ways the firing rates can be normalized for display in the heatmaps, and different normalizations have been used in different figures. We have made sure that the method for normalization is clearly indicated in the figure legends for each of the heatmaps on display, specifying the protocol and drug application used for normalization.

Figure 1 shows examples of how Fast, Mid-range, Slow, and OFF UBCs respond to in vivo MF firing patterns, but lacks a summary of how the input is transformed across a population of UBCs. In panel d, it looks as if the phase of firing becomes more delayed across the examples from Fast to OFF UBCs. Quantifying this input/output relationship more thoroughly would strengthen these results.

The UBC responses to in vivo MF firing patterns are intriguing and we agree that there appears to be increasing delays for slower UBCs visible in Figure 1. However, we feel that the true in vivo MF firing patterns are too complex and irregular for rigorous interpretation. Therefore, we only tested simplified burst and smooth pursuit-like input patterns on the full population of UBCs. Here we indeed do see increasingly delayed responses as UBCs get slower (Fig. 4).

Inhibition was pharmacologically blocked in these studies. Golgi cells and other inhibitory interneurons likely contribute to how UBCs transform input signals. Speculation of how GABAergic and glycinergic synaptic inhibition may contribute additional context to help readers understand how a circuit with intact inhibition may behave. 

As indicated in our response to reviewer 1, we have added a section discussing the very important issue of inhibition and UBC responses in vivo.   

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Including recordings without inhibition blocked would strengthen the study and provide a more comprehensive view of the transformations made by UBCs at the input stage of the cerebellar cortex.

See response to public comments.   

(2) The authors claim that a continuum of temporal responses was observed in UBCs, but they also distinguish between fast, mid-range, slow, and OFF UBCs. While some UBCs fire spontaneously, others are activated by MF inputs. A more thorough classification effort would clarify the various response profiles observed under specific MF stimulation regimes. Have the authors considered using machine learning algorithms to aid in classification? 

We fundamentally feel that these response properties do not conform to rigid categories. In our previous work we have shown that UBC population constitutes a continuum in terms of gene expression, and in terms of spontaneous and evoked firing patterns. While in order to answer some questions empirically it may still be useful to apply advanced algorithms to enforce separate groups to be compared, in this work we aimed to present the full range of UBC responses without introducing any additional biases that such methods would produce.

(3) A robust classification could assist in quantifying the temporal shifts observed during smooth pursuit-like MF stimulation, a critical outcome of the study.

As stated above, we prefer to present an unbiased overview of the continuous nature of the UBC population, as we believe that this is fundamentally the most accurate representation. While it is true that this prevents us from providing a quantification in the different temporal shifts, we believe that the range of shifts across the population is sufficiently large and continuously varying the be convincing (see Figure 4d).  

(4) In Figure 5, contrary to what is described on page 10, Cells 10 and 11 (OFF UBCs) appear to behave differently, as mGluR1 does not seem to affect their firing rates. A specific case should be made for OFF UBCs. 

Indeed, cells 10 and 11 do not show clear increases in firing and are not strongly affected by blocking of mGluR1. However, as discussed above and explored in our previous work, we feel that the range of UBC increases in firing is best described as a continuum, including the extreme where increases in firing are no longer clearly observable. As the aim in this work is to describe this continuum of responses for physiologically relevant inputs, we do not feel there is a benefit to creating a specific case for OFF UBCs here. It should be pointed out that the number of “pure” OFF UBCs completely lacking an mGluR1 component is very small.  

(5) A summary diagram should be added at the end of the manuscript to highlight the key temporal features observed in this study. 

This is a great suggestion and we have prepared such a summary diagram (Figure 6).

Reviewer #2 (Recommendations for the authors):

(1) Page 3- "Assed" should be "assessed"

(2) Page 19- "by integrating" is repeated twice

(3) It was not noted whether the data would be made available. It could be useful for those interested in implementing UBCs in models of the cerebellar cortex.

We agree that this data set is invaluable to those interested in implementing UBCs in models of the cerebellar cortex.  We will make the dataset available as described in the text.

Author response:

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

Reviewer #1:

(1) “…Given that the focus in the paper is on tissue-specific immune training, it would be helpful to know whether the ongoing presence of BCG at low levels in the profiled tissue contributes to the trained immunity phenotypes observed.”….“To address point 1, the authors could treat with anti-BCG antibiotics at 2 or 4 weeks post-BCG exposure and profile the impact on trained immunity phenotypes.”

We thank the reviewer for this important comment. The experiment suggested by the reviewer is to treat with abx to remove BCG from the tissue from the first week post challenge for the duration of four weeks. In previous work, Kaufmann et al (PMID: 29328912) showed that after a month of antibiotics, BCG levels are reduced, but residual BCG levels still remains. Accroding to their results, while antibiotic treatment reduces the training phenotype of LKS⁺ HSC expansion in the bone marrow, protection against TB was maintained during ex-vivo challenge of BMDMs.

In our experiments, we are concerned that antibiotic treatment will only change the dynamics of BCG clearance, but residual BCG will remain and will limit our interpretation. Furthermore, examining the transcriptional changes we observed at early timeponts after BCG may not be relavant at 1 month post antibiotics.

As an alternative approach, we refer to our results with an antibody to block early IFNg signaling (1-5 days; Figure S4 K-M). Here, although BCG levels are comparable between treatment and control groups, we were unable to detect any TI-related transcriptional signatures upon early aIFNg treatment. This indicates that that residual BCG is not sufficient for the TI phenotype in the spleen. We now emphasize this point in the revised version of the manuscript (see lines 335-339).

(2) “Related to the point about BCG above, it would be helpful to understand whether this is a specifically time-limited requirement when trained immunity is first induced, or whether ongoing signaling through this axis is required for maintenance of the observed trained immunity phenotypes.”… “To address point 2, authors could treat with the inhibitor at 2 weeks and/or 4 weeks post-BCG and profiling later transcriptional and/or salmonella growth phenotypes.”

We thank the reviewer for his comment, but respectfully claim that this experiment might not be feasible. As IFNg signaling is directly required for control of Salmonella infection,  we are concerned that late IFNg inhibition will also directly affect the response to Salmonella challenge and control. Thus, in our experiments, to ensure that treatment only affects the response to BCG challenge, we were careful to limit aIFNg treatment to the early time points and allowed long resting period before Salmonella challenge.

Furthermore, inhibition of IFNg at late time point was already tested in both Lee et al, and Tran et al. (PMID: 38036767, 38302603). The authors show that late blockage of IFNg signalling (days 14-21) is sufficient to prevent protection during a viral challenge. This would indeed imply that ongoing signalling is necessary in this context to generate protection, specifically also late signalling events. Furthermore, Lee at al., also observed a biphasic activation pattern of cytokines and recruited cells, suggesting that rather than continuous activation, sequential cell activation and signalling may be occurring.

Respectfully, in our experiments we focus on the early time points based on our observations of early recruitment of CM-T cells (Figure S2. C-D). This was our main findings of this paper. We agree with the reviewer that future experiments are required to compare the differences in cell populations that are invovled in the early vs. late trained phenotpe dynamics.

Minor points:

Experimental conditions for the shown data are not consistently clear from the figure legends- would add more detail about the biological conditions.

OK – done

Figure 3E missing units on the legend

OK – done

Figure 4C middle panel missing y-axis label

OK – done

Line 40- remove "both"

OK- done

Line 156- Language could be clearer about what was described previously in contrast to the results shown in this work

We have modified the text accordingly in the revised manuscript

Reviewer #2:

“A significant amount of work has already been performed for this study. The work is rich with data and description.”

We thank the reviewer for acknowledging the importance of our work.

Minor comments for the authors to consider:

“BCG is widely recognised to induce trained immunity. In this study, Salmonella is used as secondary infection event. Why? What is role of Salmonella in this study? Does this study contribute to our understanding of the Salmonella infection process? What does this tell us about Salmonella/vaccines? Is there any evidence that BCG protects against Salmonella infection? “

We thank the reviewer for this important comment. We now added to the introduction and the discussion the relevance of our study to the potential of BCG and trained immunity as an alternative heterologous vaccine approach to traditional vaccines that require strain-specific vaccine for each pathogen (lines 49-55 of the revised manuscript).

“Figure 1E. RPM cannot be detected by scRNAseq?”

The reviewer is correct. we excluded RPMs from the scRNA-seq analysis. As we discuss in the manuscript (lines 94-96), and in our previous publication (PMID: 34788598), RPM activation involves rapid cell death. As we are analyzing by scRNA-seq two weeks after BCG challenge, we only measured scRNA-seq of CD11b+ cells, which exclude RPMs, as we were worried that our transcriptional data would represent transcriptional signatures of dying cells, making interpretation of the data difficult.

“Figures 1H and I. The CM-T macrophages are not represented? Are they contemplated within the CM population? Would be useful to see the contribution of CM-T to the total CM DEGs/pathways.”

The reviewer is correct. CM-T cells are evident only after BCG challenge. Because of this, our analysis of DEGs induced in monocytes by BCG requires analysis of all monocytes together. Thus, we were careful throughout the manuscript to refer to CM when analyzing bulk RNA-seq data.

“Lines 104-117. Can the authors summarise or move the text in this paragraph to discussion? Although it provides important context, it cuts the line of thought and reduces comprehension of this section. “

OK – we moved this section to the discussion in the revised manuscript.

“Line 127. Is it Fig 1I or 1F that the authors are referring to? “

The reviewer is correct, and we changed the text in the revised manuscipt accordingly.

“Figure 1J. x-axis labels CM cells but both text and figure legend refer to this panel as CM-T. If this is the case, please show data for CM and CM-T separately.”

Please see our earlier point above that limits these analyses. As such we have also edited the text and figure legend to reflect this.

“Lines 136-139. Please indicate that this can be found in Fig 1J.”

OK – indicated in the revised manuscript

“Line 152. Please add that STm infection occurred at 14 and 60 days post training.”

OK – added

“Lines 162-163. This is repeated from lines 89-90, maybe the reduction of RPMs can be only highlighted in this section so that the previous section can be just focused on the new CM-T population?”

The reviewer is correct - we removed the mention of RPMs here, and mention them only later in the revised manuscript.

“Line 163. The recruitment is CM or CM-T cells? Since they express CXCL9 (line 165 and Fig1J) could this be used as a marker for the CM-T population at this time point?”

The reviewer is correct, and we thank him for this important comment. We now indicate that CXCL9+ is a marker for the CM-Ts population here and throughout the revised manuscript (lines 153-155 of the revised manuscript).

“Line 173. The loss of CXCL9 at 60 dpi means that CM-T population disappears/reduces or returns to CM only? If the population is reduced, could it be related to the reduced STm infection control at 60 days?”

OK– done. Referred to these cells as CM-Ts and suggested a correlation with protection loss in the text (lines 160-162 of the revised manuscript).

“Figure 2D. Can the authors show if there is variation in the myeloid populations after PBS injection at different time points? Are the percentages shown only at 3 dpi? It is curious that at 30 dpi the transcriptome has a significant change for certain genes.”

There are indeed variations across the PBS time points samples, which we demonstrate in Figure S2B. The percentages shown in the main figure for PBS reflect the mean of all time points, this is now stated in greater clarity in the revised manuscript (lines 151-152). We also noted an increase in the cell cycling genes at D30 for the control mice as well, and while still significant in BCG, we limited interpretation accordingly.

“Line 208. The authors can highlight that the expression of STAT1 follows the same pattern as IFNg. Maybe even present the graphs side by side?”

The reviewer is correct, and we have implemented their suggestion as such in the updated text (lines 192-195) and figure (Fig. 2H).

“Line 213. Authors mention a replenishment of the RPM population - what time point are you referring to? At 60 dpi the population seems to be halved compared to 14 dpi. Later (line 230), authors refer to the replenishment as a repopulation by other cell types - is repopulation more correct than replenishment?”

The reviewer is correct, and we thank the reviewer for this important comment. We now changed replenishment to repopulation (lines 95, 201), which is more accurate given the continued decreased percentage at later time points.

Lines 214-222. It is not clear what is the conclusion from these experiments: is the recruitment of progenitors from the BM or by local signals?

The reviewer is correct, we agree that the wording in the initial manuscript was imprecise. This experiment specifically tests whether trained bone marrow progenitors can sustain the observed TI signatures in a naive environment. By transplanting trained bone marrow into naive hosts, we demonstrate that progenitor programming alone is sufficient to maintain long-term SCA-1 expression in NCMs, without requiring ongoing local tissue signals. We now better clarify this text in the revised manuscript (lines 202-212).

“Line 333-334. Where is the data that shows that upon Fedratinib RPMs have enhanced survival?”

OK – We now indicate the figure in the revised manuscript.

Author response:

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

Reviewer #1:

Chemogenetics validation

Little validation is provided for the chemogenetic manipulations. The authors report that animals were excluded due to lack of expression but do not quantify/document the extent of expression in the animals that were included in the study.

We thank the reviewer for raising this oversight. We have added additional examples of virus expression in sections from included and excluded animals in Figure 1 – Supplement 1. We also added additional comments on the extent of expression we observed in lines 92-95: “Post-experiment histology confirmed overlapping virus expression and TH-positive neurons in putative VTA near the injection site (-5.6 mm AP from bregma), as well as approximately 0.5 mm anterior and posterior (-5 to -6 mm AP).”

There's no independent verification that VTA was actually inhibited by the chemogenetic manipulation besides the experimental effects of interest.

While we did include animals expressing control virus to control for any effect of CNO administration itself, the reviewer is correct that we did not independently verify VTA neurons were inhibited. We have noted this limitation of the current study on lines 513-522 in the Discussion: “We did not directly measure the suppression of VTA neurons after CNO injection. Previous work in other brain areas found hM4Di activation suppressed firing rates to around 60% of baseline (Mahler et al., 2014; Chang et al., 2015), in addition to diminishing synaptic transmission even when spikes occurred (Stachniak et al., 2014). Combined with the incomplete expression of hM4Di in TH-positive neurons in our animals, we expect VTA activity was significantly but not completely suppressed. Because our results depend only on any degree of blunting differences in dopamine release at different reward locations, rather than the total absence of dopamine signaling, measuring the magnitude of suppression was not essential for our conclusions.”

The authors report a range of CNO doses. What determined the dose that each rat received? Was it constant for an individual rat? If not, how was the dose determined? The authors may wish to examine whether any of their CNO effects were dependent on dose.

The reviewer is completely correct that we omitted sufficient information regarding the dosage of CNO used in each animal and each session. We have included more details in the Methods lines 676-694, detailing both the doses and the rationale.

The authors tested the same animal multiple times per day with relatively little time between recording sessions. Can they be certain that the effect of CNO wore off between sessions? Might successive CNO injections in the same day have impacted neural activity in the VTA differently? Could the chemogenetic manipulation have grown stronger with each successive injection (or maybe weaker due to something like receptor desensitization)? The authors could test statistically whether the effects of CNO that they report do not depend on the number of CNO injections a rat received over a short period of time.

We thank the reviewer for bringing up the question of whether the order of sessions had an influence on the efficacy of CNO in inactivating VTA activity. To address this, we split our dataset in Experiment 1 into two based on what number session of the particular day it was: 1st sessions of the day vs. all subsequent sessions (2nd+ session of the day). Then, we examined the difference in sharp-wave ripple rate between the reward ends in Epoch 2, as in Figure 2D of the manuscript. Though the resulting number of sessions in each split of the dataset is too low to draw strong statistical conclusions, particularly for novel sessions, we see little evidence there is any systematic change in the effect of VTA inactivation as a function of session number in the day. We include this in the revised manuscript as Figure 2 – Supplement 3 and in the Results lines 255-258.

Motivational considerations

In a similar vein, running multiple sessions per day raises the possibility that rats' motivation was not constant across all data collection time points. The authors could test whether any measures of motivation (laps completed, running speed) changed across the sessions conducted within the same day.

We thank the reviewer for this suggestion. We examined behavioral measures of motivation across sessions conducted within the same day. First, we calculated how many total laps each animal completed each session as a function of the session number of the day. In individual animals, this ranged from -2.8 to 4.1 laps per additional session number (mean 2.01), with an average total laps per session of 43.2 laps. Second, we calculated the median running velocity per session, across both running directions and all epochs, and checked how it varied across session number of the day. Per additional session in the day, this ranged from -3.6 to 8.6 cm/s difference across animals (mean 2.7 cm/s), with an average running velocity of 34.1 cm/s in total. Taken together, while we found little behavioral evidence of strong motivational changes across session, our animals may have been slightly more motivated in later sessions in the day, which also corresponded to later in the light cycle and closer to the dark cycle. We mention this information in Results lines 255-258, related to Figure 2 – Supplement 3.

This is a particularly tricky issue, because my read of the methods is that saline sessions were only conducted as the first session of any recording day, which means there's a session order/time of day and potential motivational confound in comparing saline to CNO sessions.

We have clarified the ordering of CNO and saline sessions in the Methods lines 697-702. Briefly, we avoided running CNO sessions before saline sessions in the same day, but either could be the first session of a day. That is, saline -> saline, saline -> CNO, and CNO -> CNO were all valid orderings. On days with more than two sessions, any number of repeated saline and CNO sessions was permitted, provided that as soon as a CNO session occurred, any subsequent sessions were also CNO.

More generally, we shared this reviewer’s concern about potential confounds between drug and motivation. For novel sessions in Experiment 1, each animal had equal numbers of saline and CNO 1st and 2nd sessions of the day. For familiar sessions, animals had similar counts for 1st sessions of the day (experimental rats: 20 saline, 16 CNO; control rats: 17 saline, 15 CNO) but more CNO 2nd sessions of the day (experimental rats: 5 saline, 13 CNO; control rats: 5 saline, 10 CNO). There were occasionally 3rd or 4th sessions in a given day for some rats, and these were also approximately equal (experimental rat 2, 3rd sessions: 2 each of saline and CNO, 4th session: 1 saline; experimental rat 3 and 4, 3rd sessions: 1 each of saline and CNO; control rat 2, 3rd session: 1 saline).

Statistics, statistical power, and effect sizes

Throughout the manuscript, the authors employ a mixture of t-tests, ANOVAs, and mixed-effects models. Only the mixed effects models appropriately account for the fact that all of this data involves repeated measurements from the same subject. The t-tests are frequently doubly inappropriate because they both treat repeated measures as independent and are not corrected for multiple comparisons.

We thank the reviewer for pointing out these issues with our statistical analyses in places. We have made the following improvements:

Figure 1F-I, S1, reward end visit durations: We now use a linear mixed-effects model to analyze the difference in stopping period durations between epochs. For each session, we calculated the mean stopping duration for each reward end in each epoch, then modeled the difference between epochs as a function of drug and novelty, with animal-specific intercepts. For example, related to Figure 1F and also described in the Results, we modeled the stopping duration difference at the Unchanged reward end, Epoch 2 – Epoch 1, and found experimental rats had a significant intercept (Epoch 2 stops shorter than Epoch 1) and the drug × novelty interaction, while control rats had a significant intercept and novelty main effect. The other visit duration analysis shown in Figure 1 – Supplement 1 have similarly been updated.

Figure 2D-E, ripple rate difference between reward ends in Epoch 2: We now use a linear mixed-effects model to analyze the difference between ripple rates at the Incr. and Unch. reward ends in Epoch 2. For each session, we calculated the mean ripple rate at each end in Epoch 2, then modeled the difference as a function of drug and novelty, with animal-specific intercepts. With the full stopping periods, for experimental rats, there was a significant intercept (ripple rate at Incr. greater than Unch.) and the model with drug included performed significantly better than the one without it (AIC_nodrug – AIC_full = 5.22). Control rats had a significant intercept and effect of novelty (greater difference with novelty), and the model excluding drug terms performed better (AIC_nodrug – AIC_full = -3.54). Results with the trimmed stopping periods were similar. These analyses are described in Results lines 253-266.   

Figure 3D-E, ripple rate as a function of reward history: We now use a mixed-effects model that incorporates animal-specific intercepts. The results remained similar and have been updated in the text and legend.

Figure 4D-K, replay rates as a function of drug, novelty, and directionality: We now use mixed-effects models that incorporate animal-specific intercepts rather than three-way ANOVA. The results remained similar and have been updated in the text and legend.

The number of animals in these studies is on the lower end for this sort of work, raising questions about whether all of these results are statistically reliable and likely to generalize. This is particularly pronounced in the reward volatility experiment, where the number of rats in the experimental group is halved to just two. The results of this experiment are potentially very exciting, but the sample size makes this feel more like pilot data than a finished product.

We have added additional emphasis in the text that the experimental group results of CNO inactivation in the volatile reward task should be confirmed with future work, in Discussion line 529-533. Because these experiments were performed on familiar tracks, we see them as corroborating/complementing the results from Experiment 1. Although the analysis assumes VTA inactivation had no effect, our pooling of all Experiment 2 data to display in Figure 3 – Supplement 2 maximized our ability to analyze the effects of volatile reward deliveries on sharp-wave ripple rates, lending further support to the main results shown in Figure 3.

The effect sizes of the various manipulations appear to be relatively modest, and I wonder if the authors could help readers by contextualizing the magnitude of these results further. For instance, when VTA inactivation increases mis-localization of SWRs to the unchanged end of the track, roughly how many misplaced sharp-waves are occurring within a session, and what would their consequence be? On this particular behavioral task, it's not clear that the animals are doing worse in any way despite the mislocalization of sharp-waves. And it seems like the absolute number of extra sharp-waves that occur in some of these conditions would be quite small over the course of a session, so it would be helpful if the authors could speculate on how these differences might translate to meaningful changes in processes like consolidation, for instance.

We thank the reviewer for this helpful suggestion to give some context to the difference in sharp-wave ripple numbers and the functional consequence of these changes. We agree completely that this task is almost certainly too simple for animals to show any performance deficit from these changes. We chose this precisely so we could examine the consequences of VTA inactivation to the sharp-wave ripple response to reward changes per se, without any confound of performance or memory changes that could also conceivably alter sharp-wave ripples. We have added both more context about the magnitude and consequence of these sharp-wave ripple changes as well as comments about the choice of this particular task (Discussion lines 522-529).  

How directly is reward affecting sharp-wave rate?

Changes in reward magnitude on the authors' task cause rats to reallocate how much time they spent at each end. Coincident with this behavioral change, the authors identify changes in the sharp-wave rate, and the assumption is that changing reward is altering the sharp-wave rate. But it also seems possible that by inducing longer pauses, increased reward magnitude is affecting the hippocampal network state and creating an occasion for more sharp-waves to occur. It's possible that any manipulation so altering rats' behavior would similarly affect the sharp-wave rate.

For instance, in the volatility experiment, on trials when no reward is given sharp-wave rate looks like it is effectively zero. But this rate is somewhat hard to interpret. If rats hardly stopped moving on trials when no reward was given, and the hippocampus remained in a strong theta network state for the full duration of the rat's visit to the feeder, the lack of sharp-waves might not reflect something about reward processing so much as the fact that the rat's hippocampus didn't have the occasion to emit a sharp-wave. A better way to compute the sharp-wave rate might be to use not the entire visit duration in the denominator, but rather the total amount of time the hippocampus spends in a non-theta state during each visit. Another approach might be to include visit duration as a covariate with reward magnitude in some of the analyses. Increasing reward magnitude seems to increase visit duration, but these probably aren't perfectly correlated, so the authors might gain some leverage by showing that on the rare long visit to a low-reward end sharp-wave rate remains reliably low. This would help exclude the explanation that sharp-wave rate follows increases in reward magnitude simply because longer pauses allow a greater opportunity for the hippocampus to settle into a non-theta state.

We thank the reviewer for these important comments. We have better clarified the analysis of sharp-wave ripple rate in the Results (lines 172-173). To speak to the main concern of the reviewer, we do only consider times during “stopping periods” when the rat is actually stationary. That is, ripple rate for each visit is calculated as (# of ripples / total stationary time), rather than the full duration the rat is at the track end. With respect to including visit duration as a covariate, the Poisson model takes the total stationary time of each visit into account, so that it is effectively predicting the number of events (ripples) per unit of time (seconds) given the particular experimental variables (reward condition, drug condition, etc.). We have added additional clarification of this in the Methods (line 834-836).

The authors seem to acknowledge this issue to some extent, as a few analyses have the moments just after the rat's arrival at a feeder and just before departure trimmed out of consideration. But that assumes these sorts of non-theta states are only occurring at the very beginning and very end of visits when in fact rats might be doing all sorts of other things during visits that could affect the hippocampus network state and the propensity to observe sharp-waves.

We hope that with the clarification provided above, this control analysis helps remove any potential effects of approaching/leaving behavior or differences in movement at the reward end that could alter sharp-wave ripple rates. 

Minor issues

The title/abstract should reflect that only male animals were used in this study.

We have added this important information to the Abstract line 21.

The title refers to hippocampal replay, but for much of the paper the authors are measuring sharp-wave rate and not replay directly, so I would favor a more nuanced title.

We thank the reviewer for this suggestion. In the context of our work, we consider sharp-wave ripples as more-easily-detected markers for the occurrence of replay. Previous work from our lab (Ambrose et al., 2016) showed the effect of reward changes had very similar effects to both sharp-wave ripple rate and replay rate. We try to be explicit about viewing ripples as markers of replay content in both the Introduction and Discussion. Nevertheless, we do also demonstrate the title claim directly – by measuring replay and its spatial localization – therefore we feel comfortable with the title as it is.

Relatedly, the interpretation of the mislocalization of sharp-waves following VTA inactivation suggests that the hippocampus is perhaps representing information inappropriately/incorrectly for consolidation, as the increased rate is observed both for a location that has undergone a change in reward and one that has not. However, the authors are measuring replay rate, not replay content. It's entirely possible that the "mislocalized" replays at the unchanged end are, in fact, replaying information about the changed end of the track. A bit more nuance in the discussion of this effect would be helpful.

While we do show that replay content, in the form of reverse vs. forward replays, is altered with VTA inactivation, we take the reviewers point and completely agree. Especially in the context of the linear track, replays at either end could certainly be updating/consolidating information about both ends. We would argue our results suggest VTA is critical to localizing ripples and replay in more complex environments where this is not the case, but this is a hypothesis. We have added clarification and discussion of this point (Discussion lines 522-529).

However, in response to the reviewer’s comment, we have now also examined non-locally-initiated replays specifically to determine whether the increased ripple rate at the Unch. reward end in novel CNO sessions was likely due to more non-local replay, but found no significant increases in non-local replay at either reward end in either drug condition or novelty condition. We have included this result as Figure 4 – Supplement 3, and note it in the Results lines 487-488.

The authors use decoding accuracy during movement to determine which sessions should be included for decoding of replay direction. Details on cross-validation are omitted and would be appreciated. Also, the authors assume that sessions failed to meet inclusion criteria because of ensemble size, but this information is not reported anywhere directly. More info on the ensemble size of included/excluded sessions would be helpful.

We have added additional information about the run decoding procedure and related session inclusion criteria, as well as about recorded ensemble sizes (lines 417-421). Briefly, mean ensemble sizes were significantly smaller for excluded sessions (cell count, mean±sem; included sessions: 26.1±1.1, excluded sessions: 9.5±1.6; two-sample t-test, t(133)=5.3, p<10^-5). The average field size, defined as the number of spatial bins with greater than 1 hz firing rate, in excluded sessions was also larger (mean±sem, included sessions: 47.7±1.3, excluded sessions: 57.7±5.8; two-sample t-test, t(133)=-2.33, p<0.05), though the difference was less dramatic. Using a mixed effects model to predict position decoding error (as in Figure 4 – Supplement 2A) as a function of drug, novelty, cell count, and mean place field size, in both experimental and control groups cell count and field size were significant predictors: more cells and smaller average field size led to lower error. A similar model that instead predicted the fraction of running bins with correctly decoded running direction (as in Figure 4 – Supplement 2B), in neither group was field size significant, while cell count remained so: more cells led to more bins with running direction correctly classified. We include these analyses in the legend for the figure. With respect to cross validation of run decoding, because both the contribution of spikes in any single time bin to a neuron’s place field is extremely small and because we used run decoding accuracy simply to filter out sessions with poorer decoding, we did not use cross validation here.

For most of the paper, the authors detect sharp-waves using ripple power in the LFP, but for the analysis of replay direction, they use a different detection procedure based on the population firing rate of recorded neurons. Was there a reason for this switch? It's somewhat difficult to compare reported sharpwave/replay rates of the analyses given that different approaches were used.

We have added clarification for this change in detecting candidate events (lines 787-789). Briefly, sharp-wave ripples and spike density events are often but not always overlapping, such that there can be strong ripples with little spiking in the recorded ensemble or weak/absent ripples during vigorous spiking in the recorded ensemble. Because the decoding of replay content relies on spiking, our lab and others often use spike density or population burst events as candidate events. We have confirmed that the main results of Experiment 1 (e.g., Figure 2) remain the same if we use spike density events rather than sharp-wave ripples, but prefer to keep the use of sharp-wave ripples here for better comparison with Experiment 2 and to allow the inclusion of animals and sessions with low cell yield but clear ripples in the LFP.  

Reviewer #2 (Recommendations For The Authors):

Include additional histological data to confirm the extent of viral spread and precise tetrode placements. Providing detailed figures that clearly illustrate these aspects would strengthen the validity of the neural recordings and the specificity of the chemogenetic silencing.

We thank the reviewer for this suggestion and have added additional information regarding virus expression in Figure 1 – Supplement 1. We also added additional comments on the extent of expression we observed in lines 92-95: “Post-experiment histology confirmed overlapping virus expression and TH-positive neurons in putative VTA near the injection site (-5.6 mm AP from bregma), as well as approximately 0.5 mm anterior and posterior (-5 to -6 mm AP).”

While we do not show histological confirmation of hippocampal recording sites, the presence of sharp-wave ripples with upward deflections, presence of place cells, and recording coordinates and depth typical of dorsal CA1 made us confident in our recording location. We have noted these characteristics of our recordings in lines 128-131 in the Results: “Tetrodes were lowered to the pyramidal cell layer of dCA1, using the presence of sharp-wave ripples with upward deflections in the LFP, recording depth characteristic of dCA1, and spatially-restricted firing of place cells to confirm the recording location.”

Address the variability in CNO dosing and timing before recordings. It is recommended to standardize the dose and ensure a consistent timing interval between CNO administration and the start of recordings to minimize variability in the effects observed across different subjects. Instead of collecting new data, the authors could report the data for each animal, indicating the dose and interval between the injection and the recording.

We have further clarified the CNO dosing and timings in lines 676-702.

In Figure 1F, explicitly state whether the data represent averages across multiple sessions and confirm if these observations are primarily from the initial novel sessions. This clarification will help in accurately interpreting the effects of novelty on the measured neural activities.

We have changed the analyses shown in Figure 1F-I and Figure 1 – Supplement 1 thanks to the suggestions of Reviewer #1, but also more clearly spell out the analysis. Briefly, we average the durations for each condition within session (e.g., take the mean Unch. duration in Epoch 1), then perform the analysis across sessions. These data come from all sessions in Experiment 1, as described in lines 141-147, meaning there are around 2-3 times as many familiar sessions as novel sessions.

Reconsider the reporting of marginal p-values (e.g., p=0.055). If the results are borderline significant, either more data should be collected to robustly demonstrate the effects or a statistical discussion should be included to address the implications of these marginal findings.

We have removed the reporting of marginal p-values.

Ensure that the axes and scales are consistent across similar figures (specifically mentioned for Figure 2A) to prevent misinterpretation of the data. Consider showing the average across all animals in 2A, similar to 2B and 2C.

We have adjusted these axes to be consistent across all panels.

Add a legend to the heatmap in Figure 4A to facilitate understanding of the data presented.

We have added a heatmap to the figure and legend.

Provide a detailed examination and discussion of the apparent contradictions observed in control data, particularly where experimental conditions with saline show increased reverse replay in novel environments, which is absent in familiar sessions. See Figures 4E and 4I.

We thank the reviewer for noting that this feature of our data deserved discussion. We confirmed that the lack of an effect of reward on reverse replay rates in familiar sessions in control rats was due to generally low replay rates in these sessions. Replay rates have been observed to decrease as the familiarity of an environment or behavior increases, and the presence of the reward-related modulation of reverse replay in novel sessions in these animals is consistent with this observation. We now report in the Results lines 458-459 and 485-486 the low replay rates in this group in familiar sessions, and the likelihood that this is preventing any reward-related modulation from being detected.

Include a more detailed analysis of place cell properties, such as firing rates and field sizes, especially in novel environments where VTA inactivation appears to alter spatial coding. Decoding error is lower during CNO administration - does this mean place fields are smaller/more accurate? This analysis could offer deeper insights into the mechanisms by which dopamine influences hippocampal neural representations and memory processes.

We thank the reviewer for this helpful suggestion. We have expanded on our analysis of place field properties and decoding accuracy, describing properties of sessions with good enough decoding to be included compared to those that were excluded (lines 417-421). We also directly tested how decoding quality depended on several factors, including drug condition, novelty, number of cells recorded, and the average place field size of recorded cells (see legend for Figure 4 – Supplement 2). We found a small but significant effect of drug in experimental rats, but larger effects of number of recorded cells and average field size, that were also present in control animals.

Correct the typo on line 722 from "In ANOVA" to "An ANOVA".

We reworded this section and have corrected this error.

Reviewer #3 (Recommendations For The Authors):

The manuscript is clear and exciting. As a main criticism, I would have liked to see the effects on ripple duration not just the rate.

We thank the reviewer for this interesting idea. We performed a new analysis, similar to our analysis on SWR rate, probing the effect of our experimental manipulations on SWR duration in experimental rats. We have added the results in Figure 2 – Supplement 4, and note them in the main text lines 195-198: “SWR duration was reduced in novel sessions, consistent with replays becoming longer with increased familiarity  (Berners-Lee et al., 2021), as well as in Epoch 2, but was otherwise unaffected by reward or drug (Figure 2 – Supplement 4).”

I have a few other minor comments:

(1) I find it a little disturbing and counterintuitive that statistical differences are not always depicted in the figure graphs (for example Figures 2A-E). If the authors don't like to use the traditional *, ** or *** they could either just use one symbol to depict significance or simply depict the actual p values.

We thank the reviewer for this suggestion. We struggled with indicating significance values graphically in an intuitive way for interaction terms in the figures. We now added significance indicators in Figures 1F-I, added the significant model coefficients directly into Figure 2B-C, changed the analysis depicted in Figure 2D-E per Reviewer 1’s suggestions, and added significance indicators where previously missing in Figures 3 and 4.

(2) Related to the point above: in the page 7 legend D and E, it would be advantageous for clarity of the experimental results to also perform post-hoc analyses as depicted in the graphs, rather than just describe the p-value of the 3way ANOVA;

We thank the reviewer for this suggestion. Because the figure includes the mean and standard error of each condition, in addition to the significant effects of the mixed-effects model, we prefer the current format as it makes clearer the statistical tests that were performed while still allowing visual appreciation of differences between specific experimental conditions of interest to the reader.

(3) According to Figure 1H, the duration of the reward visits can go up to 15s (or more). Yet in Figure 2A only the first 10sec were analyzed. While I understand the rationale for using the initial 10 seconds where there is a lot more data, the results of graphs of Figures A to C will not have the same data/rate as Figures D-F where I assume the entire duration of the visit is taken into account.

A figure showing what happening to the ripple rate during the visits >10sec would help interpret the results of Figure 2.

We thank the reviewer for these interesting suggestions. We clarify now that all these analyses of Experiment 1 use only the first 10 s of each stopping period in Method line 758-764. However, examining the longer stopping periods is an excellent suggestion, and we re-analyzed the Experiment 1 dataset using up to the first 20 s of each stopping period. The main results (e.g., Figure 2) remain the same:

(1) Related to Figure 2B-C: For experimental rats, a mixed-effects generalized linear model predicting sharp-wave ripple rate as a function of reward end, block, drug, novelty, and interactions, had the following significant terms: drug (p<10^-5), novelty (p<10^-10), reward end × block (p<10^-10), and reward end × block × drug (p<0.05). The same model in control rats had significant terms: reward end (p<0.05), novelty (p<10^-4), reward end × block (p<10^-10).

(2) Related to Figure 2D-E: For experimental rats, we used a mixed-effects generalized linear model predicting the difference in sharp-wave ripple rate between the Incr. and Unch. reward ends in Epoch 2 as a function of novelty, drug, and their interaction. Model comparison found the full model performed better than a model removing the drug terms (AIC_nodrug – AIC_full = 2.94), while a model with only the intercept performed even worse (AIC_intercept – AIC_full = 13.76). For control rats, model comparison found the full model was equivalent to a model with only the intercept (AICintercept – AICfull = -0.36), with both modestly better than a model with no drug terms (AIC_nodrug – AIC_full = 1.38).

We have added a remark that results remain the same using this longer time window in Methods line 758-764.

Author response:

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

Reviewer #2 (Public review):

Summary:

Yamawaki et al., conducted a series of neuroanatomical tracing and whole cell recording experiments to elucidate and characterise a relatively unknown pathway between the endopiriform (EN) and CA1 of the ventral hippocampus (vCA1) and to assess its functional role in social and object recognition using fibre photometry and dual vector chemogenetics. The main findings were that the EN sends robust projections to the vCA1 that collateralise to the prefrontal cortex, lateral entorhinal cortex and piriform cortex, and these EN projection neurons terminate in the stratum lacunosum-moleculare (SLM) layer of distal vCA1, synapsing onto GABAergic neurons that span across the Pyramidal-Stratum Radiatum (SR) and SR-SML borders. It was also demonstrated that EN input disynaptically inhibits vCA1 pyramidal neurons. vCA1 projecting EN neurons receive afferent input from piriform cortex, and from within EN. Finally, fibre photometry experiments revealed that vCA1 projecting EN neurons are most active when mice explore novel objects or conspecifics, and pathway-specific chemogenetic inhibition led to an impairment in the ability to discriminate between novel vs. familiar objects and conspecifics.

The authors have addressed most of my concerns, but a few weaknesses remain :<br /> (1) I expected to see the addition of raw interaction times with objects and conspecifics for each phase of social testing (pre-test, sociability test, social discrimination), as per my comment on including raw data. However, the authors only provided total distance traveled and velocity, and total interaction time in Figure S9, which is less informative.

We apologies for missing the request. We have added the raw interaction times in Fig. S9G.

(2) The authors observed increased activity in vCA1-projecting EN neurons tracking with the preferred object during the pre-test (object-object exploration) phase of the social tests, and the summary schematic (Figure 9A) depicts animals as showing a preference for one object over the other (although they are identical) in both the social and object recognition tests. However, in the chemogenetic experiment, the data (Fig S9B) indicate that animals did not show this preference for one object over another, making the expected baseline for this task unclear. This also raises an important question of whether the lack of effect from chemogenetic inhibition of vCA1-projecting EN neurons could be attributed to the absence of this baseline preference.

We appreciate the comments. In Fig. S9B, although the group median at baseline (pretest) showed no preference for one object, individual subjects displayed a preference for one object (i.e., each data point deviated positively or negatively from 0.5) in saline condition. Therefore, we do not think that a lack of baseline preference accounts for the absence of the inhibition effect in the pretest.

Additionally, the finding that vCA1-projecting EN activity is associated with the preferred object exploration appears to counter the authors' argument that novelty engages this circuit (since both objects are novel in this instance). This discrepancy warrants further discussion.

This is an interesting point. One possibility is that during the pretest, EN activity simply "reports" or "represents" the interaction time without driving exploratory preference. This aligns with our DREADD experiment data, which show that inhibition of EN neurons produced no overall behavioral effect. Innate exploratory behavior has been attributed to various circuits, including the medial preoptic area → PAG circuit (Ryoo et al., 2021, Front. Neuro.) and the Septal → VTA circuit (Mocellin et al., 2024, Neuron). We found no direct projection from these areas to EN (Fig. 6), but such connections could be established di- or polysynaptically. Moreover, these circuits could be driven by common inputs, such as the locus coeruleus or the cholinergic system for arousal, with only specific downstream targets, excluding EN, playing a key role in driving innate exploration and preference.

We have inserted the following sentence in discussion (line 253-255):

“The correlation of ENvCA1-proj. activity with novel object preference in the pretest nevertheless suggests that these neurons 'represent' the innate preference without driving it.”

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Line 209: Please remove the reference to neural activity 'predicting' behavior, as correlation analysis does not imply predictive power.

We now have changed the phrase to “Although EN^vCA1-proj. activity was correlated with the behavior…”

Line 236: It is unclear what is meant by: 'This circuit motif may predict the predominant role of ENvCA1-proj. neurons in social recognition memory'

We have changed the sentence to the following for the clarity:

“Since social odor information is crucial for discriminating conspecifics in rodents, this circuit motif may predict the predominant role of ENvCA1-proj. neurons in social recognition memory, given that social odor can engage multiple olfactory pathways innervating the piriform cortex.”

Fig 7 title: insert 'with' after correlates: 'Activity of ENvCA1-proj. neurons correlates social/object discrimination performance'

Corrected.

Fig S1 title: 'Projecing' typo.

Corrected.

Fig S8: Please rephrase for clarity: 'In pretest, the object was aligned by longer interaction time (preferred object is plotted in right side)'

We now have rephrased the sentence to:

“In the pretest plot, the object that the mice interacted with more is placed on the right side.”

References:

A septal-ventral tegmental area circuit drives exploratory behavior. Mocellin, Petra et al. Neuron, Volume 112, Issue 6, 1020-1032.e7

An inhibitory medial preoptic circuit mediates innate exploration. Ryoo, Jia et al. Front. Neurosci., 23 August 221. Volume 15- 2021

Author response:

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

Public Reviews:  

Reviewer #1 (Public Review): 

Summary: 

The authors use an innovative behavior assay (chamber preference test) and standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. They find a profound effect of TRPM2 elimination in the behavioral assay, whereas elimination of TRPV1 has the largest effect on neuronal responses. These findings are of importance, as there is still substantial discussion in the field regarding the contribution of TRP channels to different aspects of thermosensation. 

Strengths: 

The chamber preference test is an important innovation compared to the standard two-plate test, as it depends on thermal information sampled from the entire skin, as opposed to only the plantar side of the paws. With this assay, and the detailed analysis, the authors provide strong supporting evidence for the role of TRPM2 in warmth avoidance. The conceptual framework using the Drift Diffusion Model provides a first glimpse of how this decision of a mouse to change between temperatures can be interpreted and may form the basis for further analysis of thermosensory behavior. 

Weaknesses: 

The authors juxtapose these behavioral data with calcium imaging data using isolated DRG neurons. Here, there are a few aspects that are less convincing. 

(1) The authors study warmth responses using DRG neurons after three days of culturing. They propose that these "more accurately reflect the functional properties and abundance of warm-responsive sensory neurons that are found in behaving animals." However, the only argument to support this notion is that the fraction of neurons responding to warmth is lower after three days of culture. This could have many reasons, including loss of specific subpopulations of neurons, or any other (artificial?) alterations to the neurons' transcriptome due to the culturing. The isolated DRGs are not selected in any way, so also include neurons innervating viscera not involved in thermosensation. If the authors wish to address actual changes in sensory nerves involved in warmth sensing in TRPM2 or TRPV1 KO mice without disturbing the response profile as a result of the isolation procedure, other approaches would be needed (e.g. skin-nerve recordings or in vivo DRG imaging).  

We agree that there could be several reasons as to why the responses of cultured DRGs are reduced compared to the acute/short-term cultures. It is possible ––and likely–– that transcriptional changes happen over the course of the culturing period. It is also possible that it is a mere coincidence that the 3-day cultures have a response profile more similar to the in vivo situation than the acute cultures. In the revised manuscript, we have therefore toned down the claim that the 3-day cultures mirror the native conditions more appropriately and included the sentence “However, whether 3-day cultures resemble native sensory neurons more closely than acute cultures in terms of their (transcriptional) identity is currently unknown.” (page 5). 

We now also included a section “Limitations of the study” and bring this point up there as well and acknolwedge that longer culturing periods may cause changes in the neurons and may result in a drift away from their native state. 

Nevertheless, our results clearly show that acute cultures have a response profile that is much more similar to damaged/”inflamed” neurons, irrespective of any comparison to the 3 daycultures. Therefore, we believe, it is helpful to include this data to make scientists aware that acute cultures are very different to non-inflamed native/in vivo DRG neurons that many researchers use in their experiments.

(2) The authors state that there is a reduction in warmth-sensitive DRG neurons in the TRPM2 knockout mice based on the data presented in Figure 2D. This is not convincing for the following reasons. First, the authors used t-tests (with FDR correction - yielding borderline significance) whereas three groups are compared here in three repetitive stimuli. This would require different statistics (e.g. ANOVA), and I am not convinced (based on a rapid assessment of the data) that such an analysis would yield any significant difference between WT and TRPM2 KO. Second, there seems to be a discrepancy between the plot and legend regarding the number of LOV analysed (21, 17, and 18 FOV according to the legend, compared to 18, 10, and 12 dots in the plot). Therefore, I would urge the authors to critically assess this part of the study and to reconsider whether the statement (and discussion) that "Trpm2 deletion reduces the proportion of warmth responders" should be maintained or abandoned. . 

Yes, we agree that the statistical tests indicated by the referee are more appropriate/robust for the data shown in Figures 1F, 2D, and 4G.

When we perform 2-way repeated measures ANOVA and subsequent multiple comparison test (with Dunnets correction) against Wildtype, for data shown in Fig. 2D, both the main effect (Genotype) and the interaction term (Stimulus x Genotype) are significant. The multiple comparison yields very similar result as in the current manuscript, with the difference that the TRPM2-KO data for the second stimulus (~36°C) is borderline significant (with a p-value of p=0.050).

Due to the possible dependence of the repeated temperature stimuli and the variability of each stimulus between FOVs (Fig. 2C), it is possible that a mixed-effect model that accounts for these effects is more appropriate. 

Similarly, for plots 1F and 4G, Genotype (either as main effect or as interaction with Time) is significant after a repeated measures two-way ANOVA. The multiple comparisons (with Bonferroni correction) only changed the results marginally at individual timepoints, without affecting the overall conclusions. The exception is Fig. 4G at 38°C, where the interaction of Time and Genotype is significant, but no individual timepoint-comparison is significant after Bonferroni correction.

The main difference between the results presented above and the ones presented in the manuscript is the choice of the multiple comparison correction. We originally opted for the falsediscovery rate (FDR) approach as it is less prone to Type II errors (false negatives) than other methods such as Sidaks or Bonferroni, particularly when correcting for a large number of tests.

However, we are mainly interested in whether the genotypes differ in their behavior in each temperature combination and the significant ANOVA tests for Fig. 1F and 4G support that point. The statistical test and comparison used in the original/previous version of the manuscript, comparing behavior at individual/distinct timepoints, are interesting, but less relevant (and potentially distracting), as we do not go into the details about the behavior at any given/distinct timepoint in the assay.

Therefore, and per suggestion of the reviewer, we have updated the statistics in the revised version of the manuscript. Also, we now report the correct number of FOVs in the legend. The statistical details are now found in the legends of the respective figures.

(3) It remains unclear whether the clear behavioral effect seen in the TRPM2 knockout animals is at all related to TRPM2 functioning as a warmth sensor in sensory neurons. As discussed above, the effects of the TRPM2 KO on the proportion of warmth-sensing neurons are at most very subtle, and the authors did not use any pharmacological tool (in contrast to the use of capsaicin to probe for TRPV1 in Figures S3 and S4) to support a direct involvement of TRPM2 in the neuronal warmth responses. Behavioral experiments on sensory-neuron-specific TRPM2 knockout animals will be required to clarify this important point

As mentioned above, we have toned down the correlation between the cellular and behavioral data. 

In the discussion we now clearly describe three possibilities as to why the Trpm2 knockout animals only show a subtle cellular thermal phenotype but a strong behavioral thermal preference phenotype: (i) permanent deletion of Trpm2 may result in developmental defects and/or compensatory mechanisms; (ii) The DRG population expressing Trpm2 may be more relevant for autonomic thermoregulation rather than behavioral responses to temperature; (iii) Trpm2 expression outside DRGs (possibly in the hypothalamic POA) may account for the altered thermal behavior. 

(4) The authors only use male mice, which is a significant limitation, especially considering known differences in warmth sensing between male and female animals and humans. The authors state "For this study, only male animals were used, as we aimed to compare our results with previous studies which exclusively used male animals (7, 8, 17, 43)." This statement is not correct: all four mentioned papers include behavioral data from both male and female mice! I recommend the authors to either include data from female mice or to clearly state that their study (in comparison with these other studies) only uses male mice.  

This is a valid point -- when our study started 7-8 years ago, we only used male mice (as did many other researchers) and this we would now do differently. We have now newly included a statement concerning this limitation in the “Limitations of this study” section of the manuscript. 

Nevertheless, in the studies by Tan et al. And Vandevauw et al. only male animals were used for the behavioral experiments. Yarmolinsky et al.  And Paricio-Montesinons et al. used both males and females while, as far as we can tell, only Paricio-Montesions et al. Reported that no difference was observed between the sexes. 

Wildtypes are all C57bl/6N from the provider Janvier. Generally, all lines are backcrossed to C57bl/6 mice and additionally inbreeding was altered every 4-6 generations by crossing to C57bl/6. Exactly how many times the Trp channel KOs have been backcrossed to C57bl/6 mice we cannot exactly state.

Reviewer #2 (Public Review): 

Summary: 

The authors of the study use a technically well-thought-out approach to dissect the question of how far TRPV1 and TRPM2 are involved in the perception of warm temperatures in mice. They supplement the experimental data with a drift-diffusion model. They find that TRPM2 is required to trigger the preference for 31{degree sign}C over warmer temperatures while TRPV1 increases the fidelity of afferent temperature information. A lack of either channel leads to a depletion of warm-sensing neurons and in the case of TRPV1 to a deficit in rapid responses to temperature changes. The study demonstrates that mouse phenotyping can only produce trustworthy results if the tools used to test them measure what we believe they are measuring. 

Strengths: 

The authors tackle a central question in physiology to which we have not yet found sufficient answers. They take a pragmatic approach by putting existing experimental methods to the test and refining them significantly. 

Weaknesses: 

It is difficult to find weaknesses. Not only the experimental methods but also the data analysis have been refined meticulously. There is no doubt that the authors achieved their aims and that the results support their conclusions. 

There will certainly be some lasting impact on the future use of DRG cultures with respect to (I) the incubation periods, (II) how these data need to be analyzed, and (III) the numbers of neurons to be looked at. 

As for the CPT assay, the future will have to show if mouse phenotyping results are more accurate with this technique. I'm more fond of full thermal gradient environments. However, behavioural phenotyping is still one of the most difficult fields in somatosensory research.  

We thank the referee and were happy to read that the referee finds our study valuable and insightful. 

Reviewer #3 (Public Review):  

Summary and strengths: 

In the manuscript, Abd El Hay et al investigate the role of thermally sensitive ion channels TRPM2 and TRPV1 in warm preference and their dynamic response features to thermal stimulation. They develop a novel thermal preference task, where both the floor and air temperature are controlled, and conclude that mice likely integrate floor with air temperature to form a thermal preference. They go on to use knockout mice and show that TRPM2-/- mice play a role in the avoidance of warmer temperatures. Using a new approach for culturing DRG neurons they show the involvement of both channels in warm responsiveness and dynamics. This is an interesting study with novel methods that generate important new information on the different roles of TRPV1 and TRPM2 on thermal behavior. 

Open questions and weaknesses: 

(1) Differences in the response features of cells expressing TRPM2 and TRPV1 are central and interesting findings but need further validation (Figures 3 and 4). To show differences in the dynamics and the amplitude of responses across different lines and stimulus amplitudes more clearly, the authors should show the grand average population calcium response from all responsive neurons with error bars for all 3 groups for the different amplitudes of stimuli (as has been presented for the thermal stimuli traces). The authors should also provide a population analysis of the amplitude of the responses in all groups to all stimulus amplitudes. Prior work suggests that thermal detection is supported by an enhancement or suppression of the ongoing activity of sensory fibers innervating the skin. The authors should present any data on cells with ongoing activity. 

We have now included grand average population analysis of the different groups in the revised version, this is found in Figure 2E and F. Based on the referee’s suggestion and the new analysis, we now can report a (subtle) cellular phenotype observed in DRG cultures of Trpm2 deficient animals: when averaging all warmth responses, the new analysis suggests that Trpm2-deficient cultures lack modulation of the response magnitude across the three increasing consecutive warmth stimuli (33°C, 36°C and 39°C).

Concerning the point about ongoing activity: We are not sure if it is possible in neuronal cultures to faithfully recapitulate ongoing activity. Ongoing activity has been mostly recorded in skinnerve preparations (or in older studies in other types of nerve recordings) and there are only very few studies that show ongoing activity in cultured neurons and in those instances the ongoing activity only starts in sensory neuron cultures when cultured for even longer time periods than 3 days (Ref.: doi: 10.1152/jn.00158.2018). We have very few cells that show some spontaneous activity, but these are too few to draw any conclusions. In any case, nerve fibers might be necessary to drive ongoing activity which are absent from our cultures.

(2) The authors should better place their findings in context with the literature and highlight the novelty of their findings. The introduction builds a story of a 'disconnect' or 'contradictory' findings about the role of TRPV1 and TRPM2 in warm detection. While there are some disparate findings in the literature, Tan and McNaughton (2016) show a role for TRPM2 in the avoidance of warmth in a similar task, Paricio et al. (2020) show a significant reduction in warm perception in TRPM2 and TRPV1 knock out lines and Yarmolinksy et al. (2016) show a reduction in warm perception with TRPV1 inactivation. All these papers are therefore in agreement with the authors finding of a role for these channels in warm behavior. The authors should change their introduction and discussion to more correctly discuss the findings of these studies and to better pinpoint the novelty of their own work.  

Paricio-Montesinos et al. argue that TRPM8 is crucial for the detection of warmth, as TRPM8KO animals are incapable of learning the operant task. TRPM2-KO animals and, to a smaller extent TRPV1-KO animals, have reduced sensitivity in the task, but are still capable of learning/performing the task. However, in our chamber preference assay this is reversed: TRPM2-KO animals lose the ability to differentiate warm temperatures while TRPM8 appears to play no major role. A commonality between the two studies is that while TRPV1 affects the detection of warm temperatures in the different assays, this ion channel appears not to be crucial. 

Similarly, Yarmolinsky et al. show that Trpv1-inactivation only increases the error rate in their operant assay (from ~10% to ~30%), without testing TRPM2. And Tan et al. show the importance of TRPM2 in the preference task, without testing for TRPV1. 

More generally, the choice of the assay, being either an operant task (Paricio-Montesinos et al. and Yarmolinsky et al.) or a preference assay without training of the mice (Tan et al. and our data here), might be important and different TRP receptors may be relevant for different types of temperature assays, which we have now included at the end of the discussion section in the revised manuscript. While our results generally agree with the previous studies, they add a different perspective on the analysis of the behavior (with correlation to cellular data). We now edited the manuscript to highlight the advances more clearly. 

Nevertheless, we believe that a discrepancy between cellular and behavioral data in the former studies exists and we kept this in the introduction. We hope that our data and suggestions of more nuanced analysis of cellular and behavioral responses, in particular also differences in their kinetics, may be helping to guide future studies.  

(3) The responses of 60 randomly selected cells are shown in Figure 2B. But, looking at the TRPM2-/- data, warm responses appear more obvious than in WTs and the weaker responders of the WT group appear weaker than the equivalent group in the TRPV1-/- and TRPM2-/- data. This does not necessarily invalidate the results, but it may suggest a problem in the data selection. Because the correct classification of warm-sensitive neurons is central to this part of the study more validation of the classifier should be presented. For example, the authors could state if they trained the classifier using equal amounts of cells, show some randomly selected cells that are warm-insensitive for all genotypes, and show the population average responses of warm-insensitive neurons.  

The classifier was trained on a balanced dataset of 1000 (500 responders and 500 nonresponders), manually labelled traces across all 5 temperature stimuli. The prediction accuracy was 98%. We have now described more clearly how the classifier was trained (See Materials and Methods) and include examples of responders and non-responders, the population averages of each class as well as a confusion matrix of the classification in the revised manuscript (Suppl. Figure 4A and B).

(4) The interpretation of the main behavioral results and justification of the last figure is presented as the result of changes in sensing but differences in this behavior could be due to many factors and this needs clarification and discussion. (i) The authors mention that 'crucially temperature perception is not static' and suggest that there are fluctuating changes in perception over time and conclude that their modelling approach helps show changes in temperature detection. They imply that temperature perceptual threshold changes over time, but the mouse could just as easily have had exactly the same threshold throughout the task but their motivation (or some other cognitive variable) might vary causing them to change chamber. The authors should correct this. (ii) Likewise, from their fascinating and high-profile prior work the authors suggest a model of internal temperature sensing whereby TRPM2 expression in the hypothalamus acts as an internal sensory of body temperature. Given this, and the slow time course of the behavior in chambers with different ambient temperatures, couldn't the reason for the behavioral differences be due to central changes in hypothalamic processing rather than detection by skin temperature? If TRPM2-/- were selectively ablated from the skin or the hypothalamus (these experiments are not necessary for this paper) it might be possible to conclude whether sensation or body temperature is more likely the root cause of these effects but, without further experiments it is tough to conclude either way. (iii) Because the ambient temperature is controlled in this behavior, another hypothesis is that warm avoidance could be due to negative valence associated with breathing warm air, i.e. a result of sensation within the body in internal pathways, rather than sensing from the external skin. Overall, the authors should tone down conclusions about sensation and present a more detailed discussion of these points.  

We are sorry that the statement including the phrase “crucially temperature perception is not static” was ambiguous; We have now deleted this statement and instead included different possibilities as to why mice may switch from one chamber to the other stochastically. 

As the referee mentioned, it is possible that some other variable (motivation etc.) makes the mouse change the chamber; Nevertheless, we hypothesize that this variable (whatever it might be) is still modulated by temperature (at least this would be the likeliest explanation that we see).

As for the aspect of internal/hypothalamic temperature sensing and its dependence on Trpm2: we have included this possibility in the discussion in the manuscript. 

As for the point of negative valence mediated by breathing in warm air: yes, presumably this could also be possible. The aspect of valence is in interesting aspect by itself: would the mice be rather repelled from the (uncomfortable) hot plate or more attracted to the (more comfortable) thermoneutral plate, or both? Something to elucidate in a different study.

(5) It is an excellent idea to present a more in-depth analysis of the behavioral data collected during the preference task, beyond 'the mouse is on one side or the other'. However, the drift-diffusion approach is complex to interpret from the text in the results and the figures. The results text is not completely clear on which behavioral parameters are analyzed and terms like drift, noise, estimate, and evidence are not clearly defined. Currently, this section of the paper slightly confuses and takes the paper away from the central findings about dynamics and behavioral differences. It seems like they could come to similar conclusions with simpler analysis and simpler figures. 

We have now reassessed the description of the drift diffusion model and explain it more clearly, this can be found on page 5 – 8. We have considered whether it will be better to introduce the drift diffusion model at the beginning of the study, subsequent to Figure 1 but we believe this to better suited at the end, because, indeed, the cellular results (and differences in kinetic response parameters observed in DRG cultures of Trpv1 KO mice) prompted us to assess the behavior in this way. Thus, the order of experiments presented here, represents also more the natural path the study took. 

(6) In Figure 2D the % of warm-sensitive neurons are shown for each genotype. Each data point is a field of view, however, reading the figure legend there appear to be more FOVs than data points (eg 10 data points for the TRPV1-/- but 17 FOVs). The authors should check this. 

We have checked and corrected the number of FOVs mentioned in the legend, and the number shown in the Figure 2D and its legend are now in agreement. 

(7) Can the authors comment on why animals with over-expression of TRPV1 spend more time in the warmest chamber to start with at 38C and not at 34C?  

This is an interesting observation that we did not consider before. A closer look at Figure 4H reveals that the majority of the TRPV1-OX animals, have a proportionally long first visit to the 38°C room. We can only speculate why this is the case. We cannot rule out that this a technical shortcoming of the assay and how we conduced it – but we did not observe this for the wildtype mice, thus it is rather unlikely a technical problem. It is possible that this is a type of “freezing-” (or “startle-“) behavior when the animals first encounter the 38°C temperature. Freezing behaviors in mice can be observed when sudden/threatening stimuli are applied. It is possible that, in the TRPV1-overexpressing animals, the initial encounter with 38°C leads to activation of a larger proportion of cells (compared to WT controls), possibly signaling a “threatening” stimulus, and thus leading to this startle effect. However, such a claim would require additional experiments to test such a hypothesis more rigorously.

Author response:

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

eLife Assessment

This study presents valuable findings on the potential of short-movie viewing fMRI protocol to explore the functional and topographical organization of the visual system in awake infants and toddlers. Although the data are compelling given the difficulty of studying this population, the evidence presented is incomplete and would be strengthened by additional analyses to support the authors' claims. This study will be of interest to cognitive neuroscientists and developmental psychologists, especially those interested in using fMRI to investigate brain organisation in pediatric and clinical populations with limited fMRI tolerance.

We are grateful for the thorough and thoughtful reviews. We have provided point-bypoint responses to the reviewers’ comments, but first, we summarize the major revisions here. We believe these revisions have substantially improved the clarity of the writing and impact of the results.

Regarding the framing of the paper, we have made the following major changes in response to the reviews:

(1) We have clarified that our goal in this paper was to show that movie data contains topographic, fine-grained details of the infant visual cortex. In the revision, we now state clearly that our results should not be taken as evidence that movies could replace retinotopy and have reworded parts of the manuscript that could mislead the reader in this regard.

(2) We have added extensive details to the (admittedly) complex methods to make them more approachable. An example of this change is that we have reorganized the figure explaining the Shared Response Modelling methods to divide the analytic steps more clearly.

(3) We have clarified the intermediate products contributing to the results by adding 6 supplementary figures that show the gradients for each IC or SRM movie and each infant participant.

In response to the reviews, we have conducted several major analyses to support our findings further:

(1) To verify that our analyses can identify fine-grained organization, we have manually traced and labeled adult data, and then performed the same analyses on them. The results from this additional dataset validate that these analyses can recover fine-grained organization of the visual cortex from movie data.

(2) To further explore how visual maps derived from movies compare to alternative methods, we performed an anatomical alignment control analysis. We show that high-quality maps can be predicted from other participants using anatomical alignment.

(3) To test the contribution of motion to the homotopy analyses, we regressed out the motion effects in these analyses. We found qualitatively similar results to our main analyses, suggesting motion did not play a substantial role.

(4) To test the contribution of data quantity to the homotopy analyses, we correlated the amount of movie data collected from each participant with the homotopy results. We did not find a relationship between data quantity and the homotopy results. 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Ellis et al. investigated the functional and topographical organization of the visual cortex in infants and toddlers, as evidenced by movie-viewing data. They build directly on prior research that revealed topographic maps in infants who completed a retinotopy task, claiming that even a limited amount of rich, naturalistic movie-viewing data is sufficient to reveal this organization, within and across participants. Generating this evidence required methodological innovations to acquire high-quality fMRI data from awake infants (which have been described by this group, and elsewhere) and analytical creativity. The authors provide evidence for structured functional responses in infant visual cortex at multiple levels of analyses; homotopic brain regions (defined based on a retinotopy task) responded more similarly to one another than to other brain regions in visual cortex during movie-viewing; ICA applied to movie-viewing data revealed components that were identifiable as spatial frequency, and to a lesser degree, meridian maps, and shared response modeling analyses suggested that visual cortex responses were similar across infants/toddlers, as well as across infants/toddlers and adults. These results are suggestive of fairly mature functional response profiles in the visual cortex in infants/toddlers and highlight the potential of movie-viewing data for studying finer-grained aspects of functional brain responses, but further evidence is necessary to support their claims and the study motivation needs refining, in light of prior research.

Strengths:

- This study links the authors' prior evidence for retinotopic organization of visual cortex in human infants (Ellis et al., 2021) and research by others using movie-viewing fMRI experiments with adults to reveal retinotopic organization (Knapen, 2021).

- Awake infant fMRI data are rare, time-consuming, and expensive to collect; they are therefore of high value to the community. The raw and preprocessed fMRI and anatomical data analyzed will be made publicly available.

We are grateful to the reviewer for their clear and thoughtful description of the strengths of the paper, as well as their helpful outlining of areas we could improve.

Weaknesses:

- The Methods are at times difficult to understand and in some cases seem inappropriate for the conclusions drawn. For example, I believe that the movie-defined ICA components were validated using independent data from the retinotopy task, but this was a point of confusion among reviewers. 

We acknowledge the complexity of the methods and wish to clarify them as best as possible for the reviewers and the readers. We have extensively revised the methods and results sections to help avoid potential misunderstandings. For instance, we have revamped the figure and caption describing the SRM pipeline (Figure 5).

To answer the stated confusion directly, the ICA components were derived from the movie data and validated on the (completely independent) retinotopy data. There were no additional tasks. The following text in the paper explains this point:

“To assess the selected component maps, we correlated the gradients (described above) of the task-evoked and component maps. This test uses independent data: the components were defined based on movie data and validated against task-evoked retinotopic maps.” Pg. 11

In either case: more analyses should be done to support the conclusion that the components identified from the movie reproduce retinotopic maps (for example, by comparing the performance of movie-viewing maps to available alternatives (anatomical ROIs, group-defined ROIs). 

Before addressing this suggestion, we want to restate our conclusions: features of the retinotopic organization of infant visual cortex could be predicted from movie data. We did not conclude that movie data could ‘reproduce’ retinotopic maps in the sense that they would be a replacement. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously[23] found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses[27], here we find that functional alignment is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

As per the reviewer’s suggestion and alluded to in the paragraph above, we have created anatomically aligned visual maps, providing an analogous test to the betweenparticipant analyses like SRM. We find that these maps are highly similar to the ground truth. We describe this result in a new section of the results:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Also, the ROIs used for the homotopy analyses were defined based on the retinotopic task rather than based on movie-viewing data alone - leaving it unclear whether movie-viewing data alone can be used to recover functionally distinct regions within the visual cortex.

We agree with the reviewer that our approach does not test whether movie-viewing data alone can be used to recover functionally distinct regions. The goal of the homotopy analyses was to identify whether there was functional differentiation of visual areas in the infant brain while they watch movies. This was a novel question that provides positive evidence that these regions are functionally distinct. In subsequent analyses, we show that when these areas are defined anatomically, rather than functionally, they also show differentiated function (e.g., Figure 2). Nonetheless, our intention was not to use the homotopy analyses to define the regions. We have added text to clarify the goal and novelty of this analysis.

“Although these analyses cannot define visual maps, they test whether visual areas have different functional signatures.” Pg. 6

Additionally, even if the goal were to define areas based on homotopy, we believe the power of that analysis would be questionable. We would need to use a large amount of the movie data to define the areas, leaving a low-powered dataset to test whether their function is differentiated by these movie-based areas.

- The authors previously reported on retinotopic organization of the visual cortex in human infants (Ellis et al., 2021) and suggest that the feasibility of using movie-viewing experiments to recover these topographic maps is still in question. They point out that movies may not fully sample the stimulus parameters necessary for revealing topographic maps/areas in the visual cortex, or the time-resolution constraints of fMRI might limit the use of movie stimuli, or the rich, uncontrolled nature of movies might make them inferior to stimuli that are designed for retinotopic mapping, or might lead to variable attention between participants that makes measuring the structure of visual responses across individuals challenging. This motivation doesn't sufficiently highlight the importance or value of testing this question in infants. Further, it's unclear if/how this motivation takes into account prior research using movie-viewing fMRI experiments to reveal retinotopic organization in adults (e.g., Knapen, 2021). Given the evidence for retinotopic organization in infants and evidence for the use of movie-viewing experiments in adults, an alternative framing of the novel contribution of this study is that it tests whether retinotopic organization is measurable using a limited amount of movie-viewing data (i.e., a methodological stress test). The study motivation and discussion could be strengthened by more attention to relevant work with adults and/or more explanation of the importance of testing this question in infants (is the reason to test this question in infants purely methodological - i.e., as a way to negate the need for retinotopic tasks in subsequent research, given the time constraints of scanning human infants?).

We are grateful to the reviewer for giving us the opportunity to clarify the innovations of this research. We believe that this research contributes to our understanding of how infants process dynamic stimuli, demonstrates the viability and utility of movie experiments in infants, and highlights the potential for new movie-based analyses (e.g., SRM). We have now consolidated these motivations in the introduction to more clearly motivate this work:

“The primary goal of the current study is to investigate whether movie-watching data recapitulates the organization of visual cortex. Movies drive strong and naturalistic responses in sensory regions while minimizing task demands[12, 13, 24] and thus are a proxy for typical experience. In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion[25–27]. Movies have been useful in awake infant fMRI for studying event segmentation[28], functional alignment[29], and brain networks[30]. However, this past work did not address the granularity and specificity of cortical organization that movies evoke. For example, movies evoke similar activity in infants in anatomically aligned visual areas[28], but it remains unclear whether responses to movie content differ between visual areas (e.g., is there more similarity of function within visual areas than between31). Moreover, it is unknown whether structure within visual areas, namely visual maps, contributes substantially to visual evoked activity. Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity – rather than anatomy – and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses[27, 32–34].” Pg. 3-4

Furthermore, the introduction culminates in the following statement on what the analyses will tell us about the nature of movie-driven activity in infants:

“These three analyses assess key indicators of the mature visual system: functional specialization between areas, organization within areas, and consistency between individuals.” Pg. 5

Furthermore, in the discussion we revisit these motivations and elaborate on them further:

[Regarding homotopy:] “This suggests that visual areas are functionally differentiated in infancy and that this function is shared across hemispheres[31].” Pg. 19

[Regarding ICA:] “This means that the retinotopic organization of the infant brain accounts for a detectable amount of variance in visual activity, otherwise components resembling these maps would not be discoverable.” Pg. 19–20

[Regarding SRM:] “This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45].” Pg. 21

Additionally, we have expanded our discussion of relevant work that uses similar methods such as the excellent research from Knapen (2021) and others:

“In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion[25-27].” Pg. 4

“We next explored whether movies can reveal fine-grained organization within visual areas by using independent components analysis (ICA) to propose visual maps in individual infant brains[25,26,35,42,43].” Pg. 9

Reviewer #2 (Public Review):

Summary:

This manuscript shows evidence from a dataset with awake movie-watching in infants, that the infant brain contains areas with distinct functions, consistent with previous studies using resting state and awake task-based infant fMRI. However, substantial new analyses would be required to support the novel claim that movie-watching data in infants can be used to identify retinotopic areas or to capture within-area functional organization.

Strengths:

The authors have collected a unique dataset: the same individual infants both watched naturalistic animations and a specific retinotopy task. These data position the authors to test their novel claim, that movie-watching data in infants can be used to identify retinotopic areas.

Weaknesses:

To claim that movie-watching data can identify retinotopic regions, the authors should provide evidence for two claims:

- Retinotopic areas defined based only on movie-watching data, predict retinotopic responses in independent retinotopy-task-driven data.

- Defining retinotopic areas based on the infant's own movie-watching response is more accurate than alternative approaches that don't require any movie-watching data, like anatomical parcellations or shared response activation from independent groups of participants.

We thank the reviewer for their comments. Before addressing their suggestions, we wish to clarify that we do not claim that movie data can be used to identify retinotopic areas, but instead that movie data captures components of the within and between visual area organization as defined by retinotopic mapping. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously[23] found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses[27], here we find that functional alignment with infants is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

In response to the reviewer’s suggestion, we compare the maps identified by SRM to the averaged, anatomically aligned maps from infants. We find that these maps are highly similar to the task-based ground truth and we describe this result in a new section:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Note that we do not compare the anatomically aligned maps with the ICA maps statistically. This is because these analyses are not comparable: ICA is run withinparticipant whereas anatomical alignment is necessarily between-participant — either infant or adults. Nonetheless, an interested reader can refer to the Table where we report the results of anatomical alignment and see that anatomical alignment outperforms ICA in terms of the correlation between the predicted and task-based maps.

Both of these analyses are possible, using the (valuable!) data that these authors have collected, but these are not the analyses that the authors have done so far. Instead, the authors report the inverse of (1): regions identified by the retinotopy task can be used to predict responses in the movies. The authors report one part of (2), shared responses from other participants can be used to predict individual infants' responses in the movies, but they do not test whether movie data from the same individual infant can be used to make better predictions of the retinotopy task data, than the shared response maps.

So to be clear, to support the claims of this paper, I recommend that the authors use the retinotopic task responses in each individual infant as the independent "Test" data, and compare the accuracy in predicting those responses, based on:

-  The same infant's movie-watching data, analysed with MELODIC, when blind experimenters select components for the SF and meridian boundaries with no access to the ground-truth retinotopy data.

-  Anatomical parcellations in the same infant.

-  Shared response maps from groups of other infants or adults.

-  (If possible, ICA of resting state data, in the same infant, or from independent groups of infants).

Or, possibly, combinations of these techniques.

If the infant's own movie-watching data leads to improved predictions of the infant's retinotopic task-driven response, relative to these existing alternatives that don't require movie-watching data from the same infant, then the authors' main claim will be supported.

These are excellent suggestions for additional analyses to test the suitability for moviebased maps to replace task-based maps. We hope it is now clear that it was never our intention to claim that movie-based data could replace task-based methods. We want to emphasize that the discoveries made in this paper — that movies evoke fine-grained organization in infant visual cortex — do not rely on movie-based maps being better than alternative methods for producing maps, such as the newly added anatomical alignment.

The proposed analysis above solves a critical problem with the analyses presented in the current manuscript: the data used to generate maps is identical to the data used to validate those maps. For the task-evoked maps, the same data are used to draw the lines along gradients and then test for gradient organization. For the component maps, the maps are manually selected to show the clearest gradients among many noisy options, and then the same data are tested for gradient organization. This is a double-dipping error. To fix this problem, the data must be split into independent train and test subsets.

We appreciate the reviewer’s concern; however, we believe it is a result of a miscommunication in our analytic strategy. We have now provided more details on the analyses to clarify how double-dipping was avoided. 

To summarize, a retinotopy task produced visual maps that were used to trace both area boundaries and gradients across the areas. These data were then fixed and unchanged, and we make no claims about the nature of these maps in this paper, other than to treat them as the ground truth to be used as a benchmark in our analyses. The movie data, which are collected independently from the same infant in the session, used the boundaries from the retinotopy task (in the case of homotopy) or were compared with the maps from the retinotopy task (in the case of ICA and SRM). In other words, the statement that “the data used to generate maps is identical to the data used to validate those maps” is incorrect because we generated the maps with a retinotopy task and validated the maps with the movie data. This means no double dipping occurred.

Perhaps a cause of the reviewer’s interpretation is that the gradients used in the analysis are not clearly described. We now provide this additional description:  “Using the same manually traced lines from the retinotopy task, we measured the intensity gradients in each component from the movie-watching data. We can then use the gradients of intensity in the retinotopy task-defined maps as a benchmark for comparison with the ICA-derived maps.” Pg. 10

Regarding the SRM analyses, we take great pains to avoid the possibility of data contamination. To emphasize how independent the SRM analysis is, the prediction of the retinotopic map from the test participant does not use their retinotopy data at all; in fact, the predicted maps could be made before that participant’s retinotopy data were ever collected. To make this prediction for a test participant, we need to learn the inversion of the SRM, but this only uses the movie data of the test participant. Hence, there is no double-dipping in the SRM analyses. We have elaborated on this point in the revision, and we remade the figure and its caption to clarify this point:

We also have updated the description of these results to emphasize how double-dipping was avoided:

“We then mapped the held-out participant's movie data into the learned shared space without changing the shared space (Figure 5c). In other words, the shared response model was learned and frozen before the held-out participant’s data was considered.

This approach has been used and validated in prior SRM studies[45].” Pg. 14

The reviewer suggests that manually choosing components from ICA is double-dipping. Although the reviewer is correct that the manual selection of components in ICA means that the components chosen ought to be good candidates, we are testing whether those choices were good by evaluating those components against the task-based maps that were not used for the ICA. Our statistical analyses evaluate whether the components chosen were better than the components that would have been chosen by random chance. Critically: all decisions about selecting the components happen before the components are compared to the retinotopic maps. Hence there is no double-dipping in the selection of components, as the choice of candidate ICA maps is not informed by the ground-truth retinotopic maps. We now clarify what the goal of this process is in the results:

“Success in this process requires that 1) retinotopic organization accounts for sufficient variance in visual activity to be identified by ICA and 2) experimenters can accurately identify these components.” Pg. 10

The reviewer also alludes to a concern that the researcher selecting the maps was not blind to the ground-truth retinotopic maps from participants and this could have influenced the results. In such a scenario, the researcher could have selected components that have the gradients of activity in the places that the infant has as ground truth. The researcher who made the selection of components (CTE) is one of the researchers who originally traced the areas in the participants approximately a year prior to the identification of ICs. The researcher selecting the components didn’t use the ground-truth retinotopic maps as reference, nor did they pay attention to the participant IDs when sorting the IC components. Indeed, they weren’t trying to find participant specific maps per se, but rather aimed to find good candidate retinotopic maps in general. In the case of the newly added adult analyses, the ICs were selected before the retinotopic mapping was reviewed or traced; hence, no knowledge about the participant-specific ground truth could have influenced the selection of ICs. Even with this process from adults, we find results of comparable strength as we found in infants, as shown below. Nonetheless, there is a possibility that this researcher’s previous experience of tracing the infant maps could have influenced their choice of components at the participant-specific level. If so, it was a small effect since the components the researcher selected were far from the best possible options (i.e., rankings of the selected components averaged in the 64th percentile for spatial frequency maps and the 68th percentile for meridian maps). We believe all reasonable steps were taken to mitigate bias in the selection of ICs.

Reviewer #3 (Public Review):

The manuscript reports data collected in awake toddlers recording BOLD while watching videos. The authors analyse the BOLD time series using two different statistical approaches, both very complex but do not require any a priori determination of the movie features or contents to be associated with regressors. The two main messages are that 1) toddlers have occipital visual areas very similar to adults, given that an SRM model derived from adult BOLD is consistent with the infant brains as well; 2) the retinotopic organization and the spatial frequency selectivity of the occipital maps derived by applying correlation analysis are consistent with the maps obtained by standard and conventional mapping.

Clearly, the data are important, and the author has achieved important and original results. However, the manuscript is totally unclear and very difficult to follow; the figures are not informative; the reader needs to trust the authors because no data to verify the output of the statistical analysis are presented (localization maps with proper statistics) nor so any validation of the statistical analysis provided. Indeed what I think that manuscript means, or better what I understood, may be very far from what the authors want to present, given how obscure the methods and the result presentation are.

In the present form, this reviewer considers that the manuscript needs to be totally rewritten, the results presented each technique with appropriate validation or comparison that the reader can evaluate.

We are grateful to the reviewer for the chance to improve the paper. We have broken their review into three parts: clarification of the methods, validation of the analyses, and enhancing the visualization.

Clarification of the methods

We acknowledge that the methods we employed are complex and uncommon in many fields of neuroimaging. That said, numerous papers have conducted these analyses on adults (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017) and non-human primates (Arcaro & Livingstone, 2017; Moeller et al., 2009). We have redoubled our efforts in the revision to make the methods as clear as possible, expanding on the original text and providing intuitions where possible. These changes have been added throughout and are too vast in number to repeat here, especially without context, but we hope that readers will have an easier time following the analyses now. 

Additionally, we updated Figures 3 and 5 in which the main ICA and SRM analyses are described. For instance, in Figure 3’s caption we now add details about how the gradient analyses were performed on the components: 

“We used the same lines that were manually traced on the task-evoked map to assess the change in the component’s response. We found a monotonic trend within area from medial to lateral, just like we see in the ground truth.” Pg. 11

Regarding Figure 5, we reconsidered the best way to explain the SRM analyses and decided it would be helpful to partition the diagram into steps, reflecting the analytic process. These updates have been added to Figure 5, and the caption has been updated accordingly.

We hope that these changes have improved the clarity of the methods. For readers interested in learning more, we encourage them to either read the methods-focused papers that debut the analyses (e.g., Chen et al., 2015), read the papers applying the methods (e.g., Guntupalli et al., 2016), or read the annotated code we publicly release which implements these pipelines and can be used to replicate the findings.

Validation of the analyses

One of the requests the reviewer makes is to validate our analyses. Our initial approach was to lean on papers that have used these methods in adults or primates (e.g., Arcaro, & Livingstone, 2017; Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Moeller et al., 2009) where the underlying organization and neurophysiology is established. However, we have made changes to these methods that differ from their original usage (e.g., we used SRM rather than hyperalignment, we use meridian mapping rather than traveling wave retinotopy, we use movie-watching data rather than rest). Hence, the specifics of our design and pipeline warrant validation. 

To add further validation, we have rerun the main analyses on an adult sample. We collected 8 adult participants who completed the same retinotopy task and a large subset of the movies that infants saw. These participants were run under maximally similar conditions to infants (i.e., scanned using the same parameters and without the top of the head-coil) and were preprocessed using the same pipeline. Given that the relationship between adult visual maps and movie-driven (or resting-state) analyses has been shown in many studies (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017), these adult data serve as a validation of our analysis pipeline. These adult participants were included in the original manuscript; however, they were previously only used to support the SRM analyses (i.e., can adults be used to predict infant visual maps). The adult results are described before any results with infants, as a way to engender confidence. Moreover, we have provided new supplementary figures of the adult results that we hope will be integrated with the article when viewing it online, such that it will be easy to compare infant and adult results, as per the reviewer’s request. 

As per the figures and captions below, the analyses were all successful with the adult participants: 1) Homotopic correlations are higher than correlations between comparable areas in other streams or areas that are more distant within stream. 2) A multidimensional scaling depiction of the data shows that areas in the dorsal and ventral stream are dissimilar. 3) Using independent components analysis on the movie data, we identified components that are highly correlated with the retinotopy task-based spatial frequency and meridian maps. 4) Using shared response modeling on the movie data, we predicted maps that are highly correlated with the retinotopy task-based spatial frequency and meridian maps.

These supplementary analyses are underpowered for between-group comparisons, so we do not statistically compare the results between infants and adults. Nonetheless, the pattern of adult results is comparable overall to the infant results. 

We believe these adult results provide a useful validation that the infant analyses we performed can recover fine-grained organization.

Enhancing the visualization

The reviewer raises an additional concern about the lack of visualization of the results. We recognize that the plots of the summary statistics do not provide information about the intermediate analyses. Indeed, we think the summary statistics can understate the degree of similarity between the components or predicted visual maps and the ground truth. Hence, we have added 6 new supplementary figures showing the intensity gradients for the following analyses: 1. spatial frequency prediction using ICA, 2. meridian prediction using ICA, 3. spatial frequency prediction using infant SRM, 4. meridian prediction using infant SRM, 5. spatial frequency prediction using adult SRM, and 6. meridian prediction using adult SRM.

We hope that these visualizations are helpful. It is possible that the reviewer wishes us to also visually present the raw maps from the ICA and SRM, akin to what we show in Figure 3A and 3B. We believe this is out of scope of this paper: of the 1140 components that were identified by ICA, we selected 36 for spatial frequency and 17 for meridian maps. We also created 20 predicted maps for spatial frequency and 20 predicted meridian maps using SRM. This would result in the depiction of 93 subfigures, requiring at least 15 new full-page supplementary figures to display with adequate resolution. Instead, we encourage the reader to access this content themselves: we have made the code to recreate the analyses publicly available, as well as both the raw and preprocessed data for these analyses, including the data for each of these selected maps.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) As mentioned in the public review, the authors should consider incorporating relevant adult fMRI research into the Introduction and explain the importance of testing this question in infants.

Our public response describes the several citations to relevant adult research we have added, and have provided further motivation for the project.

(2) The authors should conduct additional analyses to support their conclusion that movie data alone can generate accurate retinotopic maps (i.e., by comparing this approach to other available alternatives).

We have clarified in our public response that we did not wish to conclude that movie data alone can generate accurate retinotopic maps, and have made substantial edits to the text to emphasize this. Thus, because this claim is already not supported by our analyses, we do not think it is necessary to test it further.

(3) The authors should re-do the homotopy analyses using movie-defined ROIs (i.e., by splitting the movie-viewing data into independent folds for functional ROI definition and analyses).

As stated above, defining ROIs based on the movie content is not the intended goal of this project. Even if that were the general goal, we do not believe that it would be appropriate to run this specific analysis with the data we collected. Firstly, halving the data for ROI definition (e.g., using half the movie data to identify and trace areas, and then use those areas in the homotopy analysis to run on the other half of data) would qualitatively change the power of the analyses described here. Secondly, we would be unable to define areas beyond hV4/V3AB with confidence, since our retinotopic mapping only affords specification of early visual cortex. Thus we could not conduct the MDS analyses shown in Figure 2.

(4) If the authors agree that a primary contribution of this study and paper is to showcase what is possible to do with a limited amount of movie-viewing data, then they should make it clearer, sooner, how much usable movie data they have from infants. They could also consider conducting additional analyses to determine the minimum amount of fMRI data necessary to reveal the same detailed characteristics of functional responses in the visual cortex.

We agree it would be good to highlight the amount of movie data used. When the infant data is first introduced in the results section, we now state the durations:

“All available movies from each session were included (Table S2), with an average duration of 540.7s (range: 186--1116s).” Pg. 5

Additionally, we have added a homotopy analysis that describes the contribution of data quantity to the results observed. We compare the amount of data collected with the magnitude of same vs. different stream effect (Figure 1B) and within stream distance effect (Figure 1C). We find no effect of movie duration in the sample we tested, as reported below:

“We found no evidence that the variability in movie duration per participant correlated with this difference [of same stream vs. different stream] (r=0.08, p=.700).” Pg. 6-7

“There was no correlation between movie duration and the effect (Same > Adjacent: r=-0.01, p=.965, Adjacent > Distal: r=-0.09, p=.740).” Pg. 7

(5) If any of the methodological approaches are novel, the authors should make this clear. In particular, has the approach of visually inspecting and categorizing components generated from ICA and movie data been done before, in adults/other contexts?

The methods we employed are similar to others, as described in the public review.

However, changes were necessary to apply them to infant samples. For instance, Guntupalli et al. (2016) used hyperalignment to predict the visual maps of adult participants, whereas we use SRM. SRM and hyperalignment have the same goal — find a maximally aligned representation between participants based on brain function — but their implementation is different. The application of functional alignment to infants is novel, as is their use in movie data that is relatively short by comparison to standard adult data. Indeed, this is the most thorough demonstration that SRM — or any functional alignment procedure — can be usefully applied to infant data, awake or sleeping. We have clarified this point in the discussion.

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45], which may prove especially useful for infant fMRI[52].” Pg. 21

(6) The authors found that meridian maps were less identifiable from ICA and movie data and suggest that this may be because these maps are more susceptible to noise or gaze variability. If this is the case, you might predict that these maps are more identifiable in adult data. The authors could consider running additional analyses with their adult participants to better understand this result.

As described in the manuscript, we hypothesize that meridian maps are more difficult to identify than spatial frequency maps because meridian maps are a less smooth, more fine-grained map than spatial frequency. Indeed, it has previously been reported (Moeller et al., 2009) that similar procedures can result in meridian maps that are constituted by multiple independent components (e.g., a component sensitive to horizontal orientations, and a separate component sensitive to vertical components). Nonetheless, we have now conducted the ICA procedure on adult participants and again find it is easier to identify spatial frequency components compared to meridian maps, as reported in the public review.

Minor corrections:

(1) Typo: Figure 3 title: "Example retintopic task vs. ICA-based spatial frequency maps.".

Fixed

(2) Given the age range of the participants, consider using "infants and toddlers"? (Not to diminish the results at all; on the contrary, I think it is perhaps even more impressive to obtain awake fMRI data from ~1-2-year-olds). Example: Figure 3 legend: "A) Spatial frequency map of a 17.1-monthold infant.".

We agree with the reviewer that there is disagreement about the age range at which a child starts being considered a toddler. We have changed the terms in places where we refer to a toddler in particular (e.g., the figure caption the reviewer highlights) and added the phrase “infants and toddlers” in places where appropriate. Nonetheless, we have kept “infants” in some places, particularly those where we are comparing the sample to adults. Adding “and toddlers” could imply three samples being compared which would confuse the reader.

(3) Figure 6 legend: The following text should be omitted as there is no bar plot in this figure: "The bar plot is the average across participants. The error bar is the standard error across participants.".

Fixed

(4) Table S1 legend: Missing first single quote: Runs'.

Fixed

Reviewer #2 (Recommendations For The Authors):

I request that this paper cite more of the existing literature on the fMRI of human infants and toddlers using task-driven and resting-state data. For example, early studies by (first authors) Biagi, Dehaene-Lambertz, Cusack, and Fransson, and more recent studies by Chen, Cabral, Truzzi, Deen, and Kosakowski.

We have added several new citations of recent task-based and resting state studies to the second sentence of the main text:

“Despite the recent growth in infant fMRI[1-6], one of the most important obstacles facing this research is that infants are unable to maintain focus for long periods of time and struggle to complete traditional cognitive tasks[7].”

Reviewer #3 (Recommendations For The Authors):

In the following, I report some of my main perplexities, but many more may arise when the material is presented more clearly.

The age of the children varies from 5 months to about 2 years. While the developmental literature suggests that between 1 and 2 years children have a visual system nearly adult-like, below that age some areas may be very immature. I would split the sample and perhaps attempt to validate the adult SRM model with the youngest children (and those can be called infants).

We recognize the substantial age variability in our sample, which is why we report participant-specific data in our figures. While splitting up the data into age bins might reveal age effects, we do not think we can perform adequately powered null hypothesis testing of the age trend. In order to investigate the contribution of age, larger samples will be needed. That said, we can see from the data that we have reported that any effect of age is likely small. To elaborate: Figures 4 and 6 report the participant-specific data points and order the participants by age. There are no clear linear trends in these plots, thus there are no strong age effects.

More broadly, we do not think there is a principled way to divide the participants by age. The reviewer suggests that the visual system is immature before the first year of life and mature afterward; however, such claims are the exact motivation for the type of work we are doing here, and the verdict is still out. Indeed, the conclusion of our earlier work reporting retinotopy in infants (Ellis et al., 2021) suggests that the organization of the early visual cortex in infants as young as 5 months — the youngest infant in our sample — is surprisingly adult-like.

The title cannot refer to infants given the age span.

There is disagreement in the field about the age at which it is appropriate to refer to children as infants. In this paper, and in our prior work, we followed the practice of the most attended infant cognition conference and society, the International Congress of Infant Studies (ICIS), which considers infants as those aged between 0-3 years old, for the purposes of their conference. Indeed, we have never received this concern across dozens of prior reviews for previous papers covering a similar age range. That said, we understand the spirit of the reviewer’s comment and now refer to the sample as “infants and toddlers” and to older individuals in our sample as “toddlers” wherever it is appropriate (the younger individuals would fairly be considered “infants” under any definition).

Figure 1 is clear and an interesting approach. Please also show the average correlation maps on the cortical surface.

While we would like to create a figure as requested, we are unsure how to depict an area-by-area correlation map on the cortical surface. One option would be to generate a seed-based map in which we take an area and depict the correlation of that seed (e.g., vV1) with all other voxels. This approach would result in 8 maps for just the task-defined areas, and 17 maps for anatomically-defined areas. Hence, we believe this is out of scope of this paper, but an interested reader could easily generate these maps from the data we have released.

Figure 2 results are not easily interpretable. Ventral and dorsal V1-V3 areas represent upper or lower VF respectively. Higher dorsal and ventral areas represent both upper and lower VF, so we should predict an equal distance between the two streams. Again, how can we verify that it is not a result of some artifacts?

In adults, visual areas differ in their functional response properties along multiple dimensions, including spatial coding. The dorsal/ventral stream hypothesis is derived from the idea that areas in each stream support different functions, independent of spatial coding. The MDS analysis did not attempt to isolate the specific contribution of spatial representations of each area but instead tested the similarity of function that is evoked in naturalistic viewing. Other covariance-based analyses specifically isolate the contribution of spatial representations (Haak et al., 2013); however, they use a much more constrained analysis than what was implemented here. The fact that we find broad differentiation of dorsal and ventral visual areas in infants is consistent with adults (Haak & Beckman, 2018) and neonate non-human primates (Arcaro & Livingstone, 2017). 

Nonetheless, we recognize that we did not mention the differences in visual field properties across areas and what that means. If visual field properties alone drove the functional response then we would expect to see a clustering of areas based on the visual field they represent (e.g., hV4 and V3AB should have similar representations). Since we did not see that, and instead saw organization by visual stream, the result is interesting and thus warrants reporting. We now mention this difference in visual fields in the manuscript to highlight the surprising nature of the result.

“This separation between streams is striking when considering that it happens despite differences in visual field representations across areas: while dorsal V1 and ventral V1 represent the lower and upper visual field, respectively, V3A/B and hV4 both have full visual field maps. These visual field representations can be detected in adults[41]; however, they are often not the primary driver of function[39]. We see that in infants too: hV4 and V3A/B represent the same visual space yet have distinct functional profiles.” Pg. 8

The reviewer raises a concern that the MDS result may be spurious and caused by noise. Below, we present three reasons why we believe these results are not accounted for by artifacts but instead reflect real functional differentiation in the visual cortex. 

(1) Figure 2 is a visualization of the similarity matrix presented in Figure S1. In Figure S1, we report the significance testing we performed to confirm that the patterns differentiating dorsal and ventral streams — as well as adjacent areas from distal areas — are statistically reliable across participants. If an artifact accounted for the result then it would have to be a kind of systematic noise that is consistent across participants.

(2) One of the main sources of noise (both systematic and non-systematic) with infant fMRI is motion. Homotopy is a within-participant analysis that could be biased by motion. To assess whether motion accounts for the results, we took a conservative approach of regressing out the framewise motion (i.e., how much movement there is between fMRI volumes) from the comparisons of the functional activity in regions. Although the correlations numerically decreased with this procedure, they were qualitatively similar to the analysis that does not regress out motion:

“Additionally, if we control for motion in the correlation between areas --- in case motion transients drive consistent activity across areas --- then the effects described here are negligibly different (Figure S5).” Pg. 7

(3) We recognize that despite these analyses, it would be helpful to see what this pattern looks like in adults where we know more about the visual field properties and the function of dorsal and ventral streams. This has been done previously (e.g., Haak & Beckman, 2018), but we have now run those analyses on adults in our sample, as described in the public review. As with infants, there are reliable differences in the homotopy between streams (Figure S1). The MDS results show that the adult data was more complex than the infant data, since it was best described by 3 dimensions rather than 2. Nonetheless, there is a rotation of the MDS such that the structure of the ventral and dorsal streams is also dissociable. 

Figure 3 also raises several alternative interpretations. The spatial frequency component in B has strong activity ONLY at the extreme border of the VF and this is probably the origin of the strong correlation. I understand that it is only one subject, but this brings the need to show all subjects and to report the correlation. Also, it is important to show the putative average ICA for retinotopy and spatial frequencies across subjects and for adults. All methods should be validated on adults where we have clear data for retinotopy and spatial frequency.

The reviewer notes that the component in Figure 3 shows strong negative response in the periphery. It is often the case, as reported elsewhere (Moeller et al., 2009), that ICA extracts portions of visual maps. To make a full visual map would require combining components into a composite (e.g., a component that has a high response in the periphery and another component that has a high response in the fovea). If we were to claim that this component, or others like it, could replace the need for retinotopic mapping, then we would want to produce these composite maps; however, our conclusion in this project is that the topographic information of retinotopic maps manifest in individual components of ICA. For this purpose, the analysis we perform adequately assesses this topography.

Regarding the request to show the results for all subjects, we address this in the public response and repeat it here briefly: we have added 6 new figures to show results akin to Figure 3C and D. It is impractical to show the equivalent of Figure 3A and B for all participants, yet we do release the data necessary to see to visualize these maps easily.

Finally, the reviewer suggests that we validate the analyses on adult participants. As shown in Figure S3 and reported in the public response, we now run these analyses on adult participants and observe qualitatively similar results to infants.

How much was the variation in the presumed spatial frequency map? Is it consistent with the acuity range? 5-month-old infants should have an acuity of around 10c/deg, depending on the mean luminance of the scene.

The reviewer highlights an important weakness of conducting ICA: we cannot put units on the degree of variation we see in components. We now highlight this weakness in the discussion:

“Another limitation is that ICA does not provide a scale to the variation: although we find a correlation between gradients of spatial frequency in the ground truth and the selected component, we cannot use the component alone to infer the spatial frequency selectivity of any part of cortex. In other words, we cannot infer units of spatial frequency sensitivity from the components alone.” Pg. 20

Figure 5 pipeline is totally obscure. I presumed that I understood, but as it is it is useless. All methods should be clearly described, and the intermediate results should be illustrated in figures and appropriately discussed. Using such blind analyses in infants in principle may not be appropriate and this needs to be verified. Overall all these techniques rely on correlation activities that are all biased by head movement, eye movement, and probably the dummy sucking. All those movements need to be estimated and correlated with the variability of the results. It is a strong assumption that the techniques should work in infants, given the presence of movements.

We recognize that the SRM methods are complex. Given this feedback, we remade Figure 5 with explicit steps for the process and updated the caption (as reported in the public review).

Regarding the validation of these methods, we have added SRM analyses from adults and find comparable results. This means that using these methods on adults with comparable amounts of data as what we collected from infants can predict maps that are highly similar to the real maps. Even so, it is not a given that these methods are valid in infants. We present two considerations in this regard. 

First, as part of the SRM analyses reported in the manuscript, we show that control analyses are significantly worse than the real analyses (indicated by the lines on Figure 6). To clarify the control analysis: we break the mapping (i.e., flip the order of the data so that it is backwards) between the test participant and the training participants used to create the SRM. The fact that this control analysis is significantly worse indicates that SRM is learning meaningful representations that matter for retinotopy. 

Second, we believe that this paper is a validation of SRM for infants. Infant fMRI is a nascent field and SRM has the potential to increase the signal quality in this population. We hope that readers will see these analyses as a proof of concept that SRM can be used in their work with infants. We have stated this contribution in the paper now.

“Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity -- rather than anatomy -- and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses[27,32-34].” Pg. 4

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45].” Pg. 21

Regarding the reviewer’s concern that motion may bias the results, we wish to emphasize the nature of the analyses being conducted here: we are using data from a group of participants to predict the neural responses in a held-out participant. For motion to explain consistency between participants, the motion would need to be timelocked across participants. Even if motion was time-locked during movie watching, motion will impair the formation of an adequate model that can contain retinotopic information. Thus, motion should only hurt the ability for a shared response to be found that can be used for predicting retinotopic maps. Hence, the results we observed are despite motion and other sources of noise.

What is M??? is it simply the mean value??? If not, how it is estimated?

M is an abbreviation for mean. We have now expanded the abbreviation the first time we use it.

Figure 6 should be integrated with map activity where the individual area correlation should be illustrated. Probably fitting SMR adult works well for early cortical areas, but not for more ventral and associative, and the correlation should be evaluated for the different masks.

With the addition of plots showing the gradients for each participant and each movie (Figures S10–S13) we hope we have addressed this concern. We additionally want to clarify that the regions we tested in the analysis in Figure 6 are only the early visual areas V1, V2, V3, V3A/B, and hV4. The adult validation analyses show that SRM works well for predicting the visual maps in these areas. Nonetheless, it is an interesting question for future research with more extensive retinotopic mapping in infants to see if SRM can predict maps beyond extrastriate cortex.

Occipital masks have never been described or shown.

The occipital mask is from the MNI probabilistic structural atlas (Mazziotta et al., 2001), as reported in the original version and is shared with the public data release. We have added the additional detail that the probabilistic atlas is thresholded at 0% in order to be liberally inclusive. 

“We used the occipital mask from the MNI structural atlas[63] in standard space -- defined liberally to include any voxel with an above zero probability of being labelled as the occipital lobe -- and used the inverted transform to put it into native functional space.” Pg. 27–28

Methods lack the main explanation of the procedures and software description.

We hope that the additions we have made to address this reviewer’s concerns have provided better explanations for our procedures. Additionally, as part of the data and code release, we thoroughly explain all of the software needed to recreate the results we have observed here.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

My main concern is the use of the 700K SNP dataset. This set of SNPs suffers from a heavy ascertainment bias, which can be seen in the PCA in the supplementary material where all the aurochs cluster in the center within the variation of cattle. Given the coverage of some of the samples, multiple individuals would have less than 10K SNP covered. The majority of these are unlikely to be informative here given that they would just represent fixed positions between taurine and indicine or SNPs mostly variable in milk cattle breeds. The authors would get a much better resolution (i.e. many more SNPs to work with their very low genome coverage data) using the 1000 bull genome project VCF data set:

https://www.ebi.ac.uk/ena/browser/view/PRJEB42783 which based on whole genome resequencing data from many cattle. This will certainly help with improving the resolution of qpAdm and f4 analysis, which have huge confidence intervals in most cases. Right now some individuals have huge confidence intervals ranging from 0 to 80% auroch ancestry...

We thank the reviewer for this suggestion. We repeated our analyses with a SNP panel from Run 6 of the 1000 Bulls project presented in Naval-Sanchez et al 2020. This panel reduced standard errors and narrowed down confidence intervals for the ancient samples. Another consequence is that more single-source qpAdm models can now be rejected highlighting the abundance of hybridization. For our comparison to modern breeds, we still use the 700K dataset as it provides a set of different modern European cattle breeds.

I agree with the authors that qpAdm is likely to give quite a noisy estimate of ancestry here (likely explain part of the issue I mentioned above). Although qpAdm is good for model testing here for ancestry proportion the authors instead could use an explicit f4 ratio - this would allow them to specify a model which would make the result easier to interpret.

We have added ancestry estimates from f4 ratios to the manuscript and display them together with qpAdm and Struct-f4 (as suggested by reviewer #3) in our new Table 1. We decided to keep all three different estimates to illustrate that results are not consistent for all analyses. An additional feature of qpAdm is the possibility that two source models can be rejected and additional ancestries can be identified.

The interpretation of the different levels of allele sharing on X vs autosome being the result of sex-bias admixture is not very convincing. Could these differences simply be due to a low recombination rate on the X chromosome and/or lower effective population size, which would lead to less efficient purifying selection?

Following this comment (and another comment referring to the X chromosome analysis by reviewer #2), we decided to remove sex bias from the title of our study and add more information on the caveats of this analysis. While estimating ancestry on the X chromosome can be difficult, we also add that our patterns are consistent with what has been suggested based on ancient mitochondrial data (Verdugo et al 2019). For Neolithic Anatolia, it has been suggested that the insemination of domestic cows by auroch bulls has been intentional or even ritual (Peters et al 2012). A recent parallel archaeogenomic study also concluded sex-biased introgression from autosomal, X-chromosomal and Y-chromosomal data (Rossi et al 2024). As our results are consistent with these previous studies as well as the lower differentiation of modern breeds on the X chromosome (da Fonseca et al 2019), we still consider the general pattern of our results valid even if the exact extent of sex bias is difficult to assess.

The authors suggest that 2 pop model rejection in some domestic population might be due to indicine ancestry, this seems relatively straightforward to test.

We had already performed this analysis of modeling their ancestry from three sources using qpAdm. The results are shown in Supplementary Table S6 and we now refer to this more explicitly in the text: “The presence of indicine ancestry can be confirmed in a qpAdm analysis using three sources resulting in fitting models for all breeds (Supplementary Table S6).”

The first sentence of the paper is a bit long-winded, also dogs were domesticated before the emergence of farming societies.

We rephrased the first sentence to “Domestication of livestock and crops has been the dominant and most enduring innovation of the transition from a hunter-gathering lifestyle to farming societies.”

It would be good to be specific about the number of genomes and coverage info in the last paragraph of the intro.

This information is included in the first paragraph of the results section and we decided to not duplicate the numbers in the preceding introduction paragraph to retain a flow for the readers.

Reviewer #2 (Public Review):

Summary:

In this paper, the authors investigated the admixture history of domestic cattle since they were introduced into Iberia, by studying genomic data from 24 ancient samples dated to ~2000-8000 years ago and comparing them to modern breeds. They aimed to (1) test for introgression from (local) wild aurochs into domestic cattle; (2) characterize the pattern of admixture (frequency, extent, sex bias, directionality) over time; (3) test for correlation between genetic ancestry and stable isotope levels (which are indicative of ecological niche); and (4) test for the hypothesized higher aurochs ancestry in a modern breed of fighting bulls.

Strengths:

Overall, this study collects valuable new data that are useful for testing interesting hypotheses, such as admixture between domestic and wild populations, and correlation between genome-wide aurochs ancestry and aggressiveness.

Thank you for highlighting the importance of our study and the potential of our dataset.

Weaknesses:

Most conclusions are partially supported by the data presented. The presence of admixed individuals in prehistorical periods supports the hypothesized introgression, although this conclusion needs to be strengthened with an analysis of potential contamination. The frequency, sex-bias, and directionality of admixture remain highly uncertain due to limitations of the data or issues with the analysis. There is considerable overlap in stable isotope values between domestic and wild groups, indicating a shared ecological niche, but variation in classification criteria for domestic vs wild groups and in skeletal elements sampled for measurements significantly weakens this claim. Lastly, the authors presented convincing evidence for relatively constant aurochs ancestry across all modern breeds, including the Lidia breed which has been bred for aggressiveness for centuries. My specific concerns are outlined below.

Contamination is a common concern for all ancient DNA studies. Contamination by modern samples is perhaps unlikely for this specific study of ancient cattle, but there is still the possibility of cross-sample contamination. The authors should estimate and report contamination estimates for each sample (based on coverage of autosomes and sex chromosomes, or heterozygosity of Y or MT DNA). Such contamination estimates are particularly important to support the presence of individuals with admixed ancestry, as a domestic sample contaminated with a wild sample (or vice versa) could appear as an admixed individual.

We thank the reviewer for this suggestion. Due to our low coverage data, we focused on estimating contamination from the mitochondrial data by implementing the approach used by Green et al (2008). We make the code for this step available on Github. While most samples displayed low levels of contamination, we identified one sample (moo013a) with a surprisingly high (~50%) level of contamination which was excluded from further analysis.

A major limitation of this study is uncertainty in the "population identity" for most sampled individuals (i.e., whether an individual belonged to the domesticated or wild herd when they were alive). Based on chronology, morphology, and genetic data, it is clear the Mesolithic samples from the Artusia and Mendandia sites are bona fide aurochs, but the identities of individuals from the other two sites are much less certain. Indeed, archeological and morphological evidence from El Portalon supports the presence of both domestic animals and wild aurochs, which is echoed by the inter-individual heterogeneity in genetic ancestry. Based on results shown in Fig 1C and Fig 2 it seems that individuals moo017, moo020, and possibly moo012a are likely wild aurochs that had been hunted and brought back to the site by humans. Although the presence of individuals (e.g., moo050, moo019) that can only be explained by two-source models strongly supports that interbreeding happened (if cross-contamination is ruled out), it is unclear whether these admixed individuals were raised in the domestic population or lived in the wild population and hunted.

The reviewer is pointing out an important topic, the unknown identity of the studied individuals. We have revised the text making clear that we do not know whether the individuals were hunted or herded. At the same time, their genomic ancestry speaks for itself showing that there was hybridization between wild and domestic and that different individuals carried different degrees of wild ancestry. In the revised version, we have added the unknown identity as well as the fact that our results can be affected by both, changes in human hunting and herding practices over time. Regardless of the exact identity of the individuals, our results can still be seen as (a) evidence for hybridization and (b) changes in human practices (hunting and/or herding) and their relationship to bovids over time.

Such uncertainty in "population identity" limits the authors' ability to make conclusions regarding the frequency, sex bias, and directionality of gene flow between domestic and wild populations. For instance, the wide range of ancestry estimates in Neolithic and Chalcolithic samples could be interpreted as evidence of (1) frequent recent gene flow or (2) mixed practices of herding and hunting and less frequent gene flow. Similarly, the statement about "bidirection introgression" (on pages 8 and 11) is not directly supported by data. As the genomic, morphological, and isotope data cannot confidently classify an individual as belonging to the domesticated or wild population, it seems impossible to conclude the direction of gene flow (if by "bidirection introgression" the authors mean something other than "bidirectional gene flow", they need to clearly explain this before reaching the conclusion.)

We have removed “bidirectional introgression” from the text and replaced it with the more neutral term “hybridization”. Furthermore, we used the revision to mention at several places in the text that it is not clear whether the sequenced individuals were hunted and herded and that the observed pattern likely reflects changes in both hunting and herding practices.

The f4 statistics shown in Fig 3B are insufficient to support the claim regarding sex-biased hybridization, as the f4 statistic values are not directly comparable between the X chromosome and autosomes. Because the effective population size is different for the X chromosome and autosomes (roughly 3:4 for populations with equal numbers of males and females), the expected amount of drift is different, hence the fraction of allele sharing (f4) is expected to be different. In fact, the observation that moo004 whose autosomal genome can be modeled as 100% domestic ancestry still shows a higher f4 value for the X chromosome than autosomes hints at this issue. A more robust metric to test for sex-biased admixture is the admixture proportion itself, which can be estimated by qpAdm or f4-ratio (see Patterson et al 2012). However, even with this method, criticism has been raised (e.g., Lazaridis and Reich 2017; Pfennig and Lachance, 2023). In general, detecting sex-bias admixture is a tough problem.

In response to this comment and another comment by reviewer #1, we decided to remove sex bias from the title. In the revised version of our study, we have now switched this analysis from f4 statistics to comparing f4 ratios between the X chromosome and autosomes (Figure 3). Furthermore, we have added more information on the caveats of this analysis citing the articles mentioned by the reviewer. At the same time, we highlight that our patterns are consistent with what has been suggested based on ancient mitochondrial data (Verdugo et al 2019). Unfortunately, the low coverage data does not allow to call Y chromosomal haplotypes which would also allow an analysis of the paternal lineage. But our results are consistent with additional examples from the literature: For Neolithic Anatolia, it has been suggested that the insemination of domestic cows by auroch bulls has been intentional or even ritual (Peters et al 2012) and there is a lower differentiation of modern breeds on the X chromosome (da Fonseca et al 2019). A recent parallel archaeogenomic study also concluded sex-biased introgression from autosomal, X-chromosomal and Y-chromosomal data (Rossi et al 2024). Similar to the broader hybridization signal, our interpretation does not depend on the estimates for single individuals as we describe the broader pattern. As our results are consistent with previous results based on other types of data, we still consider the general pattern of our results valid even if the exact extent of sex bias is difficult to assess.

In general, the stable isotope analysis seems to be very underpowered, due to the issues of variation in classification criteria and skeletal sampling location discussed by the authors in supplementary material. The authors claimed a significant difference in stable nitrogen isotope between (inconsistently defined) domestic cattle and wild aurochs, but no figures or statistics are presented to support this claim. Please describe the statistical method used and the corresponding p-values. The authors can consider including a figure to better show the stable isotope results.

In combination with updated tables, we have added a supplementary figure showing the stable isotope results (S9). In light of the reanalysis of the genetic data, we have reassessed the genetic models used to assign species in the stable isotope analysis. We have provided more details of the statistical methods used and the p-values are given in the supplementary materials. There is a significant difference in the nitrogen isotope values when comparing B. taurus and B. primigenius (identified on morphology) but no other comparisons are significant at the p = 0.05 threshold. The reviewer highlights what we have mentioned in the supplementary material regarding the varied skeletal elements used for stable isotope analysis and the difficulty of assigning a species identity (as this depends on what criteria are used; morphological or some kind of genetic threshold of ancestry). Indeed, how to identify the species is at the heart of the paper. Given that identity could be defined in many ways, we have used 3 different genetic models to reflect this and the morphological categories, to help explore different possible scenarios. The reviewer is correct to point out that some of this analysis is not helped by the variety of skeletal elements used, but we have been careful not to over-interpret the results. The only samples that have nitrogen values higher than one standard deviation from the mean are domestic cattle, so it is not unreasonable to suggest that only domestic cattle have high nitrogen isotope values.

Reviewer #3 (Public Review):

Summary:

Günther and colleagues leverage ancient DNA data to track the genomic history of one of the most important farm animals (cattle) in Iberia, a region showing peculiarities both in terms of cultural practices as well as a climatic refugium during the LGM, the latter of which could have allowed the survival of endemic lineages. They document interesting trends of hybridisation with wild aurochs over the last 8-9 millennia, including a stabilisation of auroch ancestry ~4000 years ago, at ~20%, a time coincidental with the arrival of domestic horses from the Pontic steppe. Modern breeds such as the iconic Lidia used in bullfighting or bull running retain a comparable level of auroch ancestry.

Strengths:

The generation of ancient DNA data has been proven crucial to unravel the domestication history of traditional livestock, and this is challenging due to the environmental conditions of the Iberian peninsula, less favourable to DNA preservation. The authors leverage samples unearthed from key archaeological sites in Spain, including the karstic system of Atapuerca. Their results provide fresher insights into past management practices, and permit characterisation of significant shifts in hybridization with wild aurochs.

We thank the reviewer for their positive assessment of our work and for highlighting the strength and potential of the study.

Weaknesses:

- Treatment of post-mortem damage: the base quality of nucleotide transitions was recalibrated down to a quality score of 2, but for 5bp from the read termini only. In some specimens (e.g. moo022), the damage seems to extend further. Why not use dedicated tools (e.g. mapDamage), or check the robustness by conditioning on nucleotide transversions?

We agree that using such a non-standard data preparation approach requires some testing. Since our main analyses are all based on f statistics, we compared f4 statistics and f4 ratios of our rescaled base quality data with data only using transversion sites. While estimates are highly correlated, the data set reduced to transversions produces larger confidence intervals in f4 ratios due to the lower number of sites. Consequently, we decided to use the rescaled data for all analyses displayed in main figures. We also prefer not to perform reference based rescaling as implemented in mapDamage as it might be sensitive to mapping bias (Günther & Nettelblad 2019).

- Their more solid analyses are based on qpAdm, but rely on two single-sample donor populations. As the authors openly discuss, it is unclear whether CPC98 is a good proxy for Iberian aurochs despite possibly forming a monophyletic clade (the number of analysed sites is simply too low to assess this monophyly; Supplementary Table S2). Additionally, it is also unclear whether Sub1 was a fully unadmixed domestic specimen, depleted of auroch ancestry. The authors seem to suggest themselves that sex-biased introgression may have already taken place in Anatolia ("suggesting that sex-biased processes already took place prior to the arrival of cattle to Iberia").

We expanded the discussion on this topic but removed the analysis of whether European aurochs form a clade due to the low number of sites. We do highlight that a recent parallel study on aurochs genomes confirmed that Western European aurochs form a clade, probably even originating from an Iberian glacial refugium (Rossi et al 2024). Even if minor structure in the gene pool of European aurochs might affect our quantitative results, it should not drive the qualitative pattern. The same should be the case for Sub1 as our tests would detect additional European aurochs ancestry that was not present in Sub1. The corresponding paragraph now reads:

“A limitation of this analysis is the availability of genomes that can be used as representatives of the source populations as we used German and British aurochs to represent western European aurochs ancestry and a single Anatolian Neolithic to represent the original domestic cattle that was introduced into Europe. Our Mesolithic Iberian aurochs contained too little endogenous DNA to be used as a proxy aurochs reference and all Neolithic and Chalcolithic samples estimated with predominantly aurochs ancestry (including the 2.7x genome of moo014) already carry low (but significant) levels of domestic ancestry. However, the fact that all of these aurochs samples carried P mitochondria strongly suggests that western European aurochs can be considered monophyletic. Furthermore, a recent parallel study also concluded that Western European aurochs all form a clade (27). The Anatolian Sub1 might also not be depleted of any European aurochs ancestry and could not fully represent the original European Neolithic gene pool as also indicated by qpAdm and Struct-f4 identifying small proportions of other Asian ancestries in some Iberian individuals.

While these caveats should affect our quantitative estimates of European aurochs ancestry, they should not drive the qualitative pattern as our tests would still detect any excess European aurochs ancestry that was not present in Neolithic Anatolia.”

Alternatively, I recommend using Struct-f4 as it can model the ancestry of all individuals together based on their f4 permutations, including outgroups and modern data, and without the need to define pure "right" and "left" populations such as CPC98 and Sub1. It should work with low-coverage data, and allows us to do f4-based MDS plots as well as to estimate ancestry proportions (including from ghost populations).

We thank the reviewer for this suggestion. We added Struct-f4 as an analysis but observed that it would not converge in an individual-based analysis due to the low coverage of most of our samples. We added Struct-f4 results for samples with >0.1X to the new Table 1, the results are similar to the results obtained using f4 ratios and (to a lower degree) the qpAdm results.

- In the admixture graph analyses (supplementary results), the authors use population groups based on a single sample. If these samples are pseudohaploidised (or if coverage is insufficient to estimate heterozygosity - and it is at least for moo004 and moo014), f3 values are biased, implying that the fitted graph may be wrong. The graph shown in Fig S7 is in fact hard to interpret. For example, the auroch Gyu2 from Anatolia but not the auroch CPC98 also from Anatolia received 62% of ancestry from North Africa? The Neolithic samples moo004 and moo014 also show the same shocking disparity. I would consider re-doing this analysis with more than a sample per population group

There seems to be some confusion relating to the sample identity in these figures. CPC98 is British and not Anatolian while Gyu2 is from the Caucasus and not Anatolia which would explain why they are different. Furthermore, moo004 is mostly of domestic ancestry while, moo014 is mostly of European aurochs ancestry according to our other analyses, which should explain why they also behave differently in this analysis. To avoid confusion and since this is a supplementary analysis from which we are not drawing any major conclusions, we decided to remove the graphs and the analysis from the study.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Fig 3A: The red regression line is misleading. It seems to show that the average aurochs ancestry fraction has been steadily decreasing since ~8000 years ago, but the "averaging" is not meaningful as not all samples necessarily represent domestic cattle remains and the sample size is rather small. In other words, the samples are just a small, random collection of domestic and wild animals, and the average ancestry is subject to large sampling noise. I would suggest removing the regression line (along with the associated confidence interval) in this figure. It would also be helpful to label the samples with their IDs and morphology in the plot for cross-reference with other figures. Also, it is said in the legend that "Modern Iberian breeds... are added around date 0 with some vertical jitter". Do the authors mean "horizontal jitter" instead?

Thank you for noticing this! We have removed the regression line and corrected the figure legend.

Fig 2 vs Fig 3A: are the error bars the same in these two plots? They seem to be highly similar, if not identical, but the legends read very differently ("95% confidence interval by block-jackknife vs. on standard error"). Please explain.

The figure legends have been corrected.

Fig 3B: What do the error bars in Fig 3B mean? 95% confidence interval or one standard error? Please clarify in the legend.

We have removed this figure and replaced it with a different way of displaying the results (now Figure 3). We ensured that the error bars are displayed consistently across figures.

According to the f4 statistics shown in Fig 1C and Fig 3B, moo012b carries a relatively high amount of domestic ancestry. How is this compatible with the observation in Fig 2 that this individual can be modeled with 100% aurochs (i.e., aurochs as the single source)? Does this simply reflect the low genome coverage?

moo012b is indeed one of the lowest coverage samples in our has at <0.02x sequencing depth. Even in our revised analysis using more sites, there is a discrepancy between the results of f4 statistics and qpAdm (suggesting mostly domestic ancestry) and f4 ratio suggesting mostly aurochs ancestry (Figure 1C and Table 1). We believe that this highlights the sensitivity of different methods to assumptions about the relationships of sources and potential “outgroups” which might not be well resolvable with low coverage data and in the presence of potentially complex admixture. Our general results, however, do not depend on the estimates for single individuals as our interpretations are based on the general pattern.

I don't fully understand the rationale behind the statement "However, at some point, the herding practices must have changed since modern Iberian breeds show approximately 20-25% aurochs ancestry". Can the stable ancestry fraction from 4000 years to the present (relative to the highly variable ancestry before) reflect of discontinuation of hunting rather than changes in herding practices?

We agree that this statement was not justified here, we rephrased the sentence to “In fact, from the Bronze Age onwards, most estimates overlap with the approximately 25% aurochs ancestry in modern Iberian cattle” and generally tried to make the text more nuanced on the issue of herding and hunting practices.

Reviewer #3 (Recommendations For The Authors):

Thanks for this interesting piece of work. The results are clearly presented, and I have no additional concerns other than those reflected in the public report, except perhaps:

(i) trying to use more informative sample names (eg. including the date and location). It may facilitate reading without going back and forth to the table "Sample List".

We have now added a main table listing our post-Mesolithic samples together with their age, site and estimated aurochs ancestry proportions. We hope that his table makes it easier for readers to follow our sample IDs.

(ii) Briefly describe in the main the age of aurochs and Sub1 not generated in this study.

Fixed.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Meissner et al describe an update on the collection of split-GAL4 lines generated by a consortium led by Janelia Research Campus. This follows the same experimental pipeline described before and presents as a significant increment to the present collection. This will strengthen the usefulness and relevance of "splits" as a standard tool for labs that already use this tool and attract more labs and researchers to use it.

Strengths:

This manuscript presents a solid step to establish Split-GAL4 lines as a relevant tool in the powerful Drosophila toolkit. Not only does the raw number of available lines contribute to the relevance of this tool in the "technical landscape" of genetic tools, but additional features of this effort contribute to the successful adoption. These include:

(1) A description of expression patterns in the adult and larvae, expanding the "audience" for these tools

(2) A classification of line combination according to quality levels, which provides a relevant criterion while deciding to use a particular set of "splits".

(3) Discrimination between male and female expression patterns, providing hints regarding the potential role of these gender-specific circuits.

(4) The search engine seems to be user-friendly, facilitating the retrieval of useful information.

Overall, the authors employed a pipeline that maximizes the potential of the Split-GAL4 collection to the scientific community.

Weaknesses:

The following aspects apply:

The use of split-GAL4 lines has improved tremendously the genetic toolkit of Drosophila and this manuscript is another step forward in establishing this tool in the genetic repertoire that laboratories use. Thus, this would be a perfect opportunity for the authors to review the current status of this tool, addressing its caveats and how to effectively implement it into the experimental pipeline.

(1) While the authors do bring up a series of relevant caveats that the community should be aware of while using split-GAL4 lines, the authors should take the opportunity to address some of the genetic issues that frequently arise while using the described genetic tools. This is particularly important for laboratories that lack the experience using split-GAL4 lines and wish to use them. Some of these issues are covertly brought up, but not entirely clarified.

First, why do the authors (wisely) rescreen the lines using UAS-CsChrimson-mVenus? One reason is that using another transgene (such as UAS-GFP) and/or another genomic locus can drive a different expression pattern or intensities. Although this is discussed, this should be made more explicit and the readers should be aware of this.

Second, it would be important to include a discussion regarding the potential of hemidriver lines to suffer from transvection effects whenever there is a genetic element in the same locus. These are serious issues that prevent a more reliable use of split-GAL4 lines that, once again, should be discussed.

We added additional explanatory text to the discussion.

(2) The authors simply mention that the goal of the manuscript is to "summarize the results obtained over the past decade.". A better explanation would be welcomed in order to understand the need of a dedicated manuscript to announce the availability of a new batch of lines when previous publications already described the Split-GAL4 lines. At the extreme, one might question why we need a manuscript for this when a simple footnote on Janelia's website would suffice.

We added an additional mention of the cell type split-GAL4 collection at the relevant section and added more emphasis on the curation process adding value to the final selections. We feel that the manuscript is useful to document the methods used for the contained analysis and datasets and gives a starting point to the reader to go through the many split-GAL4 publications and images.

Reviewer #2 (Public Review):

Summary: This manuscript describes the creation and curation of a collection of genetic driver lines that specifically label small numbers of neurons, often just a single to handful of cell types, in the central nervous system of the fruit fly, Drosophila melanogaster. The authors screened over 77,000 split hemidriver combinations to yield a collection of 3060 lines targeting a range of cell types in the adult Drosophila central nervous system and 1373 lines characterized in third-instar larvae. These genetic driver lines have already contributed to several important publications and will no doubt continue to do so. It is a truly valuable resource that represents the cooperation of several labs throughout the Drosophila community.

Strengths:

The authors have thoughtfully curated and documented the lines that they have created, so that they may be maximally useful to the greater community. This documentation includes confocal images of neurons labeled by each driver line and when possible, a list of cell types labeled by the genetic driver line and their identity in an EM connectome dataset. The authors have also made available some information from the other lines they created and tested but deemed not specific or strong enough to be included as part of the collection. This additional resource will be a valuable aid for those seeking to label cell types that may not be included in the main collection.

Weaknesses:

None, this is a valuable set of tools that took many years of effort by several labs. This collection will continue to facilitate important science for years to come.

We thank the reviewer for their positive feedback.

Reviewer #3 (Public Review):

Summary:

The manuscript by Meissner et al. describes a collection of 3060 Drosophila lines that can be used to genetically target very small numbers of brain cells. The collection is the product of over a decade of work by the FlyLight Project Team at the Janelia Research Campus and their collaborators. This painstaking work has used the intersectional split-Gal4 method to combine pairs of so-called hemidrivers into driver lines capable of highly refined expression, often targeting single cell types. Roughly one-third of the lines have been described and characterized in previous publications and others will be described in manuscripts still in preparation. They are brought together here with many new lines to form one high-quality collection of lines with exceptional selectivity of expression. As detailed in the manuscript, all of the lines described have been made publicly available accompanied by an online database of images and metadata that allow researchers to identify lines containing neurons of interest to them. Collectively, the lines include neurons in most regions of both the adult and larval nervous systems, and the imaging database is intended to eventually permit anatomical searching that can match cell types targeted by the lines to those identified at the EM level in emerging connectomes. In addition, the manuscript introduces a second, freely accessible database of raw imaging data for many lower quality, but still potentially useful, split-Gal4 driver lines made by the FlyLight Project Team.

Strengths:

Both the stock collection and the image databases are substantial and important resources that will be of obvious interest to neuroscientists conducting research in Drosophila. Although many researchers will already be aware of the basic resources generated at Janelia, the comprehensive description provided in this manuscript represents a useful summary of past and recent accomplishments of the FlyLight Team and their collaborators and will be very valuable to newcomers in the field. In addition, the new lines being made available and the effort to collect all lines that have been generated that have highly specific expression patterns is very useful to all.

Weaknesses:

The collection of lines presented here is obviously somewhat redundant in including lines from previously published collections. Potentially confusing is the fact that previously published split-Gal4 collections have also touted lines with highly selective expression, but only a fraction of those lines have been chosen for inclusion in the present manuscript. For example, the collection of Shuai et al. (2023) describes some 800 new lines, many with specificity for neurons with connectivity to the mushroom body, but only 168 of these lines were selected for inclusion here. This is presumably because of the more stringent criteria applied in selecting the lines described in this manuscript, but it would be useful to spell this out and explain what makes this collection different from those previously published (and those forthcoming).

We added more description of how this collection is focused on the best cell-type-specific lines across the CNS. An important requirement for inclusion was this degree of specificity across the CNS, while many prior publications had a greater emphasis on lines with a narrower focus of specificity.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Luckily for us, genetics is for the most part an exact science. However, there's still some "voodoo" in a lot of genetic combinations that the authors should disclose and be as clear as possible in the manuscript. This allows for the potential users to gauge expectations and devise a priori alternative plans.

We attempted to comprehensively cover the caveats inherent in our genetic targeting approach.

Minor points:

(1) The authors mention that fly age should be controlled as expression can vary. Is there any reference to support this claim?

We added a reference describing driver expression changes over development.

(2) There should be a citation for "Flies were typically 1-5 days old at dissection for the cell type collection rescreening, 1-8 days old for other non-MCFO crosses and 3-8 days old for MCFO".

We clarified that these descriptions were of our experimental preparations, not describing other citable work.

Reviewer #3 (Recommendations For The Authors):

General Points:

Overall, the manuscript is very clear, but there are a couple of points where more explicit information would be useful. One of these is with respect to the issue of selectivity of targeting. The cell type specificity of lines is often referred to, but cell types can range from single pairs of neurons to hundreds of indistinguishable neurons with similar morphology and function. It would be useful if the authors explained whether their use of the term "cell type" distinguishes cell type from cell number. It would also be useful if lines that target many neurons of a single cell type were identified.

We added further discussion of cell types vs. cell numbers. Our labeling strategy was not optimized for counting cell numbers labeled by each line. We believe EM studies are best positioned to comprehensively evaluate the number of cells making up each type.

The second point relates to vagueness about the intended schedule for providing resources that will match (or allow matching of) neurons to the connectome. For example, on pp. 5-6 it is stated that: "In the future all of the neurons in these lines will be uniquely identified and linked to neurons reconstructed in the electron microscopy volume of the larva" but no timeline is provided. Similarly, for the adult neurons it is stated on p. 4 that: "Anatomical searching for comparison to other light microscopy (LM) and EM data is being made available." A more explicit statement about what resources are and are not yet available, a timeline for full availability, and an indication of how many lines currently have been matched to EM data would be helpful.

During the review and revision period we have made progress on processing the images in the collection. We updated the text with the current status and anticipated timeline for completion.

Specific Points:

p. 4 "Although the lines used for these comparisons are not a random sample, the areas of greatest difference are in the vicinity of previously described sexual dimorphisms..." In the vicinity of is a very vague statement of localization. A couple of examples of what is meant here would be useful.

We added example images to Figure 3.

p. 5 "...may have specific expression outside our regions of interest." It's not clear what "our regions of interest" refers to here. Please clarify.

We clarified that we were referring to the regions studied in the publications listed in Table 1.

p. 5 "...lines that were sparse in VNC but dirty in the brain or SEZ..." A more quantitative descriptor than "dirty" would be helpful.

We unfortunately did not quantify the extent of undesired brain/SEZ expression, but attempted to clarify the statement.

p. 6 "...the images are being made instantly searchable for LM and EM comparisons at NeuronBridge..." Here again it is hard to know what is meant by "being made instantly searchable." How many have been made searchable and what is the bottleneck in making the rest searchable?

We updated the text as described above. The bottleneck has been available processing capacity for the hundreds of thousands of included images.

Figure 1 Supplemental File 2: The movie is beautiful, but it seems more useful as art than as a reference. Perhaps converting it to a pdf of searchable images for each line would make it more useful.

We replaced the movie with a searchable PDF.

Fig. 2(B) legend: "Other lines may have more than two types." It is not clear what "other lines" are being referred to.

As part of making the quality evaluation more robust, we scored lines for the clear presence of three or more cell types. We updated the text accordingly.

Fig. 2(C): Presumably the image shown is an example of variability in expression rather than weakness, but it is hard to know without a point of comparison. Perhaps show the expression patterns of other samples? Or describe briefly in the legend what other samples looked like?

We added Figure 2 - figure supplement 1 with examples of variable expression in a split-GAL4 line.

Author response:

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

Comments on revised version: 

Overall, I thought the authors addressed my comments well with the possible exception of what is actually new here. This was the most important thing that I thought should be included in the revision. Although the authors rewrote the paragraph describing the lines presented in the paper, I still can't tell exactly which ones haven't been previously published. Their revised paragraph says that 40 lines have been "previously used," but Supplemental Table 1 shows references for over 200 of the lines, which sounds more reasonable based on papers that have come out. 

We have modified the text in line 112-120 as below.

“Supplementary File 1 lists 859 lines (including split-LexA) and their detailed information, such as genotype, expression specificity, matched EM cell type(s), and recommended driver for each cell type. A small subset of 47 lines from this collection have been previously used in studies (Aso et al., 2023; Dolan et al., 2019; Gao et al., 2019; Scaplen et al., 2021; Schretter et al., 2020; Takagi et al., 2017; Xie et al., 2021; Yamada et al., 2023).”

For 842 lines among the 859 lines listed in Supplementary File 1, this study is the primary citation for future papers for the following reason: 

In 2021 December, we deposited the confocal images of new split-GAL4 lines at Janelia Flylight website (http://www.janelia.org/split-gal4) without a publication to describe annotation of expression patterns, and we already started sharing the lines without restrictions. In 2023 September, we released the preprint of this study at bioRxiv (doi: https://doi.org/10.1101/2023.09.15.557808). Up to this point, 47 lines have been used in other studies. In Supplementary File 1, 30 of them attribute the citation credit to both this study and other papers, because this 2023 preprint was cited as the primary citation in those papers. Similarly, the omni paper to summarize all the eWort of generating split-GAL4 lines by Janelia Flylight team (https://doi.org/10.7554/eLife.98405.1) cite many lines from this paper. However, since this summary paper did not provide additional information such as functional characterization by behavioral experiments, we did not include it in Supplementary File 1 to clarify that this study is the primary citation for these lines. The remaining 17 lines were published before 2021. We included them for the convenience of users, and we attributed the primary citation to the already published papers. 

Also, in the revised paragraph they state that "All transgenic lines newly generated in this study are listed in Supplementary File 2" but that table lists only the 36 LexA hemidriver lines! Confusingly, this comment cites the same 8 references as are cited for the 40 line that they say were previously published. I am thus only more confused about how many previously uncharacterized lines are presented in this paper. 

We modified the text as below to clarify that “new lines” indicate LexA or DBD lines but not new combination of already published AD and DBD lines. We removed the 8 citations, which were mistakenly placed in the previous manuscript.

“The newly generated LexA, Gal4DBD and LexADBD lines are listed in Supplementary File 2. “

Author response:

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

Reviewer #1:

(1) All analyses were performed on trial-averaged neural responses that were pooled across mice. Owing to differences between subjects in behavior, experimental preparation quality, and biological variability, it seems important to perform at least some analyses on individual analyses to assess how behavioral training might differently affect each animal.

In order to image at a relatively fast rate (30Hz) appropriate to the experimental conditions, we restricted our imaging to a relatively small field of view (412x412um with 512x512 pixels). This entails a smaller number of ROIs per animal, which can lead to an unbalanced distribution of cells responsive to different stimuli for individual fields-of-view. We used the common approach of pooling across animals (Homann et al., 2021; Kim et al., 2019) to overcome limitations imposed by sampling a smaller number of cells per animal. In response to this comment, we included supplemental analyses (Sup.Fig. 6) showing that representational drift (which was not performed on trial-averaged data) looks substantially the same (albeit nosier) for individual animals as at the population level. Additional analyses (PE ratio, etc.) were difficult since the distribution of cells selective for individual stimuli is unbalanced between individual animals and few mice have multiple cells representing all of the different stimuli.

(2) The correlation analyses presented in Figure 3 (labeled the second Figure 2 in the text) should be conducted on a single-animal basis. Studying population codes constructed by pooling across mice, particularly when there is no behavioral readout to assess whether learning has had similar effects on all animals, appears inappropriate to me. If the results in Figure 3 hold up on single animals, I think that is definitely an interesting result.

We repeated the correlation analysis performed on mice individually and included them in the supplement (Supp. Fig. 6). The overall result generally mirrors the result found by pooling across animals.

(3) On Day 0 and Day 5, the reordered stimuli are presented in trial blocks where each image sequence is shown 100 times. Why wasn't the trial ordering randomized as was done in previous studies (e.g. Gavornik and Bear 2014)? Given this lack of reordering, did neurons show reduced predictive responses because the unexpected sequence was shown so many times in quick succession? This might change the results seen in Figure 2, as well as the decoder results where there is a neural encoding of sequence order (Figure 4). It would be interesting if the Figure 4 decoder stopped working when the higher-order block structure of the task was disrupted.

Our work builds primarily on previous studies (Gavornik & Bear, 2014; Price et al., 2023) that demonstrated clear changes in neural responses over days while employing a similar block structure. Notably, Price et al. found that trial number (within a block) was not a significant factor in the generation of prediction-error responses which strongly suggests short-term plasticity does not play a significant role in shaping responses within the block structure. This finding is consistent with our previous LFP recordings which have not revealed any significant plasticity occurring within a training session, a conclusion bolstered by a collaborative work currently in press (Hosmane et al. 2024, Sleep) revealing the requirement for sleep in sequence plasticity expression.

It is possible that layer 2/3 adapts to sequences more rapidly than layer 4/5. While manual inspection does not reveal an obvious difference between early and late blocks in this dataset, the n for this subset is too small to draw firm conclusions. It is our view that the block structure provides the strongest comparison to previous work, but agree it would be interesting to randomize or fully interleave sequences in future studies to determine what effect, if any, short-term changes might have. 

(4) A primary advantage of using two-photon calcium imaging over other techniques like extracellular electrophysiology is that the same neurons can be tracked over many days. This is a standard approach that can be accomplished by using many software packages-including Suite2P (Pachitariu et al. 2017), which is what the authors already used for the rest of their data preprocessing. The authors of this paper did not appear to do this. Instead, it appears that different neurons were imaged on Day 0 (baseline) and Day 5 (test). This is a significant weakness of the current dataset.

The hypothesis being tested was whether expectation violations, as described in Keller & Mrsic-Flogel 2018, exist under a multi-day sequence learning paradigm. For this, tracking cells across days is not necessary as our PE metric compared responses of individual neurons to multiple stimuli within a single session. Given the speed/FOV tradeoff discussed above, we wanted to consider all cells irrespective of whether they were visible/active or trackable across days, especially since we would expect cells that learn to signal prediction errors to be inactive on day 0 and not selected by our segmentation algorithm. Though we did not compare the responses of single cells before/after training, we did analyze cells from the same field of view on days 0 and 5 (see Supp.Fig. 1) and not distinct populations.

Reviewer #2:

(1) There appears to be some confusion regarding the conceptual framing of predictive coding.

Assuming the mouse learns to expect the sequence ABCD, then ABBD does not probe just for negative prediction errors, and ACBD is not just for positive prediction errors. With ABBD, there is a combination of a negative prediction error for the missing C in the 3rd position, and a positive prediction error for B in the 3rd. Likewise, with ACBD, there is a negative prediction error for the missing B at 2nd and missing C at 3rd, and a positive prediction error for the C in 2nd and B in 3rd. Thus, the authors' experimental design does not have the power to isolate either negative or positive prediction errors. Moreover, looking at the raw data in Figure 2C, this does not look like an "omission" response to C, but more like a stronger response to a longer B. The pitch of the paper as investigating prediction error responses is probably not warranted - we see no way to align the authors' results with this interpretation.

The reviewer has identified a real problem with the framing of “positive” and “negative” prediction errors in context of sensory stimuli where substitution simultaneously introduces unexpected “positive” violation and “negative” omission. Simply put, even if there are separate mechanisms to represent positive and negative errors, there may be no way to isolate the positive response experimentally since an unexpected input always replaces the unseen expected input. For example, had a cell fired solely to ACBD (and not during either ABCD or ABCD), then whether it was signaling the unexpected occurrence of C or the unexpected absence of B would be inherently ambiguous. In either case, such a cell would have been labeled as C-responsive, and its activity would have been elevated compared with ABCD and would have been included in our substitution-type analysis of prediction errors. We accept that there is some ambiguity regarding the description in this particular case, but overall, this cell’s activity pattern would have informed the PE analysis for which the result was essentially null for the substitution-type violation ACBD.

Omission, in which the sensory input does not change, may experimentally isolate the negative response though this is only true if there is a temporal expectation of when the change should have occurred. If A is predicting B in an ordinal sense but there is no expectation of when B will occur with respect to A, changing the duration of A would not be expected to produce an error signal since at any point in time B might still be coming and the expectation is not broken until something other than B occurs. With respect specifically to ABBD in our experiments, it is correct that the learned error responses take the form of stronger, sustained responses to B during the time C was expected. This is still in contrast to day 0 in which activation decays after a transient response to ABBD. The data shows that responses during an omitted element are altered with training and take the form of elevated responses to ABBD on day 5.As we say in our discussion, this is somewhat ambiguous evidence of prediction errors since it does emerges only with training and is generally consistent with the hypothesis being tested though it takes a different form than we expected it to.

(2) Related to the interpretation of the findings, just because something can be described as a prediction error does not mean it is computed in (or even is relevant to) the visual cortex. To the best of our knowledge, it is still unclear where in the visual stream the responses described here are computed. It is possible that this type of computation happens before the signals reach the visual cortex, similar to mechanisms predicting moving stimuli already in the retina (https://pubmed.ncbi.nlm.nih.gov/10192333/). This would also be consistent with the authors' finding (in previous work) that single-cell recordings in V1 exhibit weaker sequence violation responses than the author's earlier work using LFP recordings.

Our work was aimed at testing the specific hypothesis that PE responses, at the very least, exist in L2/3—a hypothesis that is well-supported under different experimental paradigms (often multisensory mismatch). Our aim was to test this idea under a sequence learning paradigm and connect it with previously found PE responses in L4. We don’t claim that it is the only place in which prediction errors may be computed or useful, especially since (as you mentioned), there is evidence for such responses in layer 4. But it is fundamentally important to predictive processing that we determine whether PE responses can be found in layer 2/3 under this passive sequence learning paradigm, whether or not they reflect upstream processes, feedback from higher areas, or entirely local computations. Our aim was to establish some baseline evidence for or against predictive processing accounts of L2/3 activity during passive exposure to visual sequences.

(3) Recording from the same neurons over the course of this paradigm is well within the technical standards of the field, and there is no reason not to do this. Given that the authors chose to record from different neurons, it is difficult to distinguish representational drift from drift in the population of neurons recorded.

Our discussion of drift refers to changes occurring within a population of neurons over the course of a single imaging session. We have added clarifying language to the manuscript to make this clear. Changes to the population-level encoding of stimuli over days are treated separately and with different analytical tools. Re. tracking single across days, please see the response to Reviewer #1, comment 4.

(4) The block paradigm to test for prediction errors appears ill-chosen. Why not interleave oddball stimuli randomly in a sequence of normal stimuli? The concern is related to the question of how many repetitions it takes to learn a sequence. Can the mice not learn ACBD over 100x repetitions? The authors should definitely look at early vs. late responses in the oddball block. Also, the first few presentations after the block transition might be potentially interesting. The authors' analysis in the paper already strongly suggests that the mice learn rather rapidly. The authors conclude: "we expected ABCD would be more-or-less indistinguishable from ABBD and ACBD since A occurs first in each sequence and always preceded by a long (800 ms) gray period.

This was not the case. Most often, the decoder correctly identified which sequence stimulus A came from." This would suggest that whatever learning/drift could happen within one block did indeed happen and responses to different sequences are harder to interpret.

This work builds on previous studies that used a block structure to drive plasticity across days. We previously tested whether there are intra-block effects and found no indication of changes occurring within a block or withing a session (please see the response to Reviewer #1, comment 3 for further discussion). Observed drift does complicate comparison between blocks. There is no indication in our data that this is a learned effect, though future experiments could test this directly.

(5) Throughout the manuscript, many of the claims are not statistically tested, and where they are the tests do not appear to be hierarchical (https://pubmed.ncbi.nlm.nih.gov/24671065/), even though the data are likely nested.

We have modified language throughout the manuscript to be more precise about our claims. We used pooled data between mice and common parametric statistics in line with published literature. The referenced paper offers a broad critique of this approach, arguing that it increases the possibility of type 1 errors, though it is not clear to us that our experimental design carries this risk particularly since most of our results were negative. To address the specific concern, however we performed a non-parametric hierarchical bootstrap analysis (https://pmc.ncbi.nlm.nih.gov/articles/PMC7906290/) that re-confirmed the statistical significance of our positive results, see Supplemental Figure 8.

(6) The manuscript would greatly benefit from thorough proofreading (not just in regard to figure references).

We apologize for the errors in the manuscript. We caught the issue and passed on a corrected draft, but apparently the uncorrected draft was sent for review. The re-written manuscript addresses all identified issues.

(7) With a sequence of stimuli that are 250ms in length each, the use of GCaMP6s appears like a very poor choice.

We started our experiments using GCaMP6f but ultimately switched to GCaMP6s due to its improved sensitivity, brightness, and accuracy in spike detection (Huang et al., 2021). When combined with deconvolution (Pachitariu et al., 2018; Pnevmatikakis et al., 2016), we found GCaMP6s provides the most complete and accurate view of spiking within 40ms time bins. The inherent limitations of calcium imaging are more likely to be addressed using electrophysiology rather than a faster sensor in future studies.

(8) The data shown are unnecessarily selective. E.g. it would probably be interesting to see how the average population response evolves with days. The relevant question for most prediction error interpretations would be whether there are subpopulations of neurons that selectively respond to any of the oddballs. E.g. while the authors state they "did" not identify a separate population of omission-responsive neurons, they provide no evidence for this. However, it is unclear whether the block structure of the experiments allows the authors to analyze this.

We concluded that there is no clear dedicated subpopulation of omission-responding cells by inspecting cells with large PE responses (i.e., ABBD, see supplemental figure 3). Out of the 107 B-responsive cells on day 5, only one appeared to fire exclusively during the omitted stimulus. Average traces for all B-responsive cells are included in the supplement and we have updated the manuscript accordingly. Similarly, a single C-responsive cell was found with an apparently unique substitution error profile (ABCD and ACBD , supplemental figure 4).

Our primary concern was to make sure that days 0 and 5 had the highest quality fields-of-view. In work leading up to this study, there were concerns that imaging on all intermediate days resulted in a degradation of quality due to photobleaching. We agree that an analysis of intermediate days would be interesting, but it was excluded due to these concerns. 

Reviewer #3:

(1) Experimental design using a block structure. The use of a block structure on test days (0 and 5) in which sequences were presented in 100 repetition blocks leads to several potential confounds. First, there is the potential for plasticity within blocks, which could alter the responses and induce learned expectations. The ability of the authors to clearly distinguish blocks 1 and 2 on Day 0 with a decoder suggests this change over time may be meaningful.

Repeating the experiments with fully interleaved sequences on test days would alleviate this concern. With the existing data, the authors should compare responses from the first trials in a block to the last trials in a block.

This block design likely also accounts for the ability of a decoder to readily distinguish stimulus A in ABCD from A in ABBD. As all ABCD sequences were run in a contiguous block separate from ABBD, the recent history of experience is different for A stimuli in ABCD versus ABBD. Running fully interleaved sequences would also address this point, and would also potentially mitigate the impact of drift over blocks (discussed below).

As described in other responses, the block structure was chosen to align more closely with previous studies. We take the overall point though, and future studies will employ the suggested randomized or interleaved structure in addition to block structures to investigate the effects of short-term plasticity.

(2) The computation of prediction error differs significantly for omission as opposed to substitutions, in meaningful ways the authors do not address. For omission errors, PE compares the responses of B1 and B2 within ABBD blocks. These responses are measured from the same trial, within tens of milliseconds of each other. In contrast, substitution PE is computed by comparing C in ABCD to C in ACBD. As noted above, the block structure means that these C responses were recorded in different blocks, when the state of the brain could be different. This may account for the authors' detection of prediction error for omission but not substitution. To address this, the authors should calculate PE for omission using B responses from ABCD.

We performed the suggested analysis (i.e., ABBD vs ABCD) prior to submission but omitted it from the draft for brevity (the effect was the same as with ABBD vs ABBD). We have added the results of standardizing with ABCD as supplementary figure 3.

(3) The behavior of responses to B and C within the trained sequence ABCD differs considerably, yet is not addressed. Responses to B in ABCD potentiate from d0-> d5, yet responses to C in the same sequence go down. This suggests there may be some difference in either the representation of B vs C or position 2 vs 3 in the sequence that may also be contributing to the appearance of prediction errors in ABBD but not ACBD. The authors do not appear to consider this point, which could potentially impact their results. Presenting different stimuli for A,B,C,D across mice would help (in the current paper B is 75 deg and C is 165 deg in all cases). Additionally, other omissions or substitutions at different sequence positions should be tested (eg ABCC or ABDC).

We appreciate the suggestion. Ideally, we could test many different variants, but practical concerns regarding the duration of the imaging sessions prevented us from testing other interesting variations (such as ABCC) in the current study. We are uncertain as to how we should interpret the overall depressed response to element C seen on day 5, but since the effect is shared in both ABCD and ACBD, we don’t think it affected our PE calculations. 

(4) The authors' interpretation of their PCA results is flawed. The authors write "Experience simplifies activity in principal component space". This is untrue based on their data. The variance explained by the first set of PCs does not change with training, indicating that the data is not residing in a lower dimensional ("simpler") space. Instead, the authors show that the first 5 PCs better align with their a priori expectations of the stimulus structure, but that does not mean these PCs necessarily represent more information about the stimulus (and the fact that the authors fail to see an improvement in decoding performance argues against this case). Addressing such a question would be highly interesting, but is lacking in the current manuscript. Without such analysis, referring to the PCs after training as "highly discretized" and "untangled" are largely meaningless descriptions that lack analytical support.

We meant the terms “simpler”, “highly-discretized”, and “untangled” as qualitative descriptions of changes in covariance structure that occurred despite the maintenance of overall dimensionality. As the reviewer notes, the obvious changes in PC space appear to have had practically no effect on decodability or dimensionality, and we found this surprising and worth describing.

(5) The authors report that activity sparsifies, yet provide only the fraction of stimulus-selective cells. Given that cell detection was automated in a manner that takes into account neural activity (using Suite2p), it is difficult to interpret these results as presented. If the authors wish to claim sparsification, they need to provide evidence that the total number of ROIs drawn on each day (the denominator for sparseness in their calculation) is unbiased. Including more (or less) ROIs can dramatically change the calculated sparseness.

The authors mention sparsification as contributing to coding efficiency but do not test this. Training a decoder on variously sized subsets of their data on days 0 and 5 would test whether redundant information is being eliminated in the network over training.

First, we provide evidence for sparseness using a visual responsiveness metric in addition to stimulus-selectivity. Second, it is true that Suite2p’s segmentation is informed by activity and therefore may possibly omit cells with very minimal activity. However, we detected a comparable number of cells on day 5 (n=1500) to day 0 (1368). We reportedly roughly half as many cells are stimulus-selective on day 5 compared with day 0. In order for that to have been a result of biased ROI segmentation, we would have needed to have detected closer to 2600 cells on day 5 rather than 1500.  Therefore, we consider any bias in the segmentation to have had little effect on the main findings.

(6) The authors claim their results show representational drift, but this isn't supported in the data. Rather they show that there is some information in the structure of activity that allows a decoder to learn block ID. But this does not show whether the actual stimulus representations change, and could instead reflect an unrelated artifact that changes over time (responsivity, alertness, bleaching, etc). To actually assess representational drift, the authors should directly compare representations across blocks (one could train a decoder on block 1 and test on blocks 2-5). In the absence of this or other tests of representational drift over blocks, the authors should remove the statement that "These findings suggest that there is a measurable amount of representational drift".

“To actually assess representational drift, the authors should directly compare representations across blocks (one could train a decoder on block 1 and test on blocks 25)”: This is the exact analysis that was performed. Additionally, our analysis of pairwise correlations directly measures representational drift.

“But this does not show whether the actual stimulus representations change, and could instead reflect an unrelated artifact that changes over time (responsivity, alertness, bleaching, etc)”: We have repeated the decoder analysis using normalized population vectors (Supplementary Figure 5) which we believe directly addresses whether the observed drift is due to photobleaching or alertness that would affect the overall magnitudes of response vectors.

Our analysis of block decoding reflects decoders trained on individual stimulus elements, and we show the average over all such decodings (we have clarified this in the text). For example, we trained a decoder on ABCD presentations from block 1 and tested only against ABCD from other blocks, which I believe is the test being suggested by the reviewer. Furthermore, we do show that representational similarity for all stimulus elements reduces gradually and more-or-less monotonically as the time between presentations increases. We believe this is a fairly straightforward test of representational drift as has been reported and used elsewhere (Deitch et al., 2021).

(7) The authors allude to "temporal echoes" in a subheading. This term is never defined, or substantiated with analysis, and should be removed.

We hoped the term ‘temporal echo’ would be understood in the context of rebounding activity during gray periods as supported by analysis in figure 6a. We have eliminated the wording in the updated manuscript.

Author response:

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

Public Reviews:

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors provide a method aiming to accurately reflect the individual deviation of longitudinal/temporal change compared to the normal temporal change characterized based on pre-trained population normative model (i.e., a Bayesian linear regression normative model), which was built based on cross-sectional data. This manuscript aims at solving a recently identified problem of using normative models based on cross-sectional data to make inferences about longitudinal change.

Strengths:

The efforts of this work make a good contribution to addressing an important question of normative modeling. With the greater availability of cross-sectional studies for normative modeling than longitudinal studies, and the inappropriateness of making inferences about longitudinal subject-specific changes using these cross-sectional data-based normative models, it's meaningful to try to address this gap from the aspect of methodological development.

In the 1st revision, the authors added a simulation study to show how the performance of the classification based on z-diff scores relatively changes with different disruptions (and autocorrelation). Unfortunately, in my view this is insufficient as it only shows how the performance of using z-diff score relatively changes in different scenarios. I would suggest adding the comparison of performance to using the naïve difference in two simple z-scores to first show its better performance, which should also further highlight the inappropriate use of simple z-scores in inferring within-subject longitudinal changes.

Thank you for the suggestion for additional comparison, which we have now implemented in the simulated methods comparison, see Figure 2 and the extended text of Section 2.1.4 Simulation study.

Specifically, we have revised the simulation section to not only illustrate the performance of our z-diff method under various scenarios but also to include a direct comparison with a naïve approach that subtracts two z-scores.

The updated results demonstrate that, compared to the naïve method, the z-diff score consistently maintains a fixed false-positive rate, making it a more robust and controllable approach. Additionally, we show that under conditions of high autocorrelation, the z-diff method is significantly more sensitive in detecting smaller changes than the subtraction method. Importantly, our analysis of a sample from our dataset indicates that high autocorrelation is a prevalent characteristic in real-world data, further supporting the utility of the z-diff method.

We believe that these findings strengthen the case for adopting the z-diff method and underscore the limitations of more intuitive approaches, which, while simple, lack mathematical rigour.

Additionally, Figure 1 is hard to read and obtain the actual values of the performance measure. I would suggest reducing it to several 2-dimensional figures. For example, for several fixed values of rho, how the performance changes with different values of the true disruption (and also adding the comparison to the naïve method (difference in two z-scores)).

We believe that the Reviewer meant Figure 2; indeed, the 3-dimensional visualization, while attractive to some, may have been difficult to read, so we have now replaced it with several 2-dimensional figures as requested.

I would also suggest changing the title to reflect that the evaluation of "intra-subject" longitudinal change is the method's focus.

Thanks for the suggestion. We have now implemented it by changing the title to Using normative models pre-trained on cross-sectional data to evaluate intra-individual longitudinal changes in neuroimaging data.

We hope the changes implemented fulfill the expectations of the Reviewer.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This work aims to understand the role of thalamus POm in dorsal lateral striatum (DLS) projection in learning a sensorimotor associative task. The authors first confirm that POm forms "en passant" synapses with some of the DLS neuronal subtypes. They then perform a go/no-go associative task that consists of the mouse learning to discriminate between two different textures and to associate one of them with an action. During this task, they either record the activity of the POm to DLS axons using endoscopy or silence their activity. They report that POm axons in the DLS are activated around the sensory stimulus but that the activity is not modulated by the reward. Last, they showed that silencing the POm axons at the level of DLS slows down learning the task.

The authors show convincing evidence of projections from POm to DLS and that POm inputs to DLS code for whisking whatever the outcome of the task is. However, their results do not allow us to conclude if more neurons are recruited during the learning process or if the already activated fibres get activated more strongly. Last, because POm fibres in the DLS are also projecting to S1, silencing the POm fibres in the DLS could have affected inputs in S1 as well and therefore, the slowdown in acquiring the task is not necessarily specific to the POm to DLS pathway.

We thank the reviewer for these constructive comments. The points are addressed below.  

Strengths:

One of the main strengths of the paper is to go from slice electrophysiology to behaviour to get an in-depth characterization of one pathway. The authors did a comprehensive description of the POm projections to the DLS using transgenic mice to unambiguously identify the DLS neuronal population. They also used a carefully designed sensorimotor association task, and they exploited the results in depth.

It is a very nice effort to have measured the activity of the axons in the DLS not only after the mice have learned the task but throughout the learning process. It shows the progressive increase of activity of POm axons in the DLS, which could imply that there is a progressive strengthening of the pathway. The results show convincingly that POm axons in the DLS are not activated by the outcome of the task but by the whisker activity, and that this activity on average increases with learning.

Weaknesses:

One of the main targets of the striatum from thalamic input are the cholinergic neurons that weren't investigated here, is there information that could be provided?

This is true of the parafascicular (Pf) thalamic nucleus, which has been well studied in this context. However, there is much less known about the striatal projections of other thalamic nuclei, including POm, and their inputs to cholinergic neurons. Anatomical tracing evidence from Klug et al. (2018), which mapped brain-wide inputs to striatal cholinergic (ChAT) interneurons, suggests that Pf provides the majority of thalamic innervation of striatal ChAT neurons compared to other thalamic nuclei. Many other thalamic nuclei, including POm, showed very little of no labeling, suggesting weak innervation of ChAT interneurons. However, it is possible that these thalamic nuclei, including POm, do provide functional innervation of ChAT interneurons that is not sufficiently assessed by anatomical tracing. Understanding the innervation patterns of POm-striatal projections beyond the three cell types we have studied here would be an important area of further study.

It is interesting to know that the POm projects to all neuronal types in the DLS, but this information is not used further down the manuscript so the only take-home message of Figure 1 is that the axons that they image or silence in the DLS are indeed connected to DLS neurons and not just passing fibres. In this line, are these axons the same as the ones projecting to S1? If this is the case, why would we expect a different behaviour of the axon activity at the DLS level compared to S1?

Tracing of single POm axons by Ohno et al. (2012) indicated that POm axons form a branched collateral that innervates striatum, while the main axon continues in the rostral-dorsal direction to innervate cortex. We think it is reasonable, based on the morphology, that our optogenetic suppression experiment restricted the suppression of glutamate release to this branch and avoided the other branches of the axon that project to cortex. However, testing this would require monitoring S1 activity during the POm-striatal axon suppression, which we did not do in this study.

It is a very interesting question whether there could be different axon activity behavior in striatum versus S1. There is surprising evidence that POm synaptic terminals are different sizes in S1 and M1 and show different synaptic physiological properties depending on these cortical projection targets (Casas-Torremocha et al., 2022). Based on this, it is possible that POm-striatal synapses show distinct properties compared to cortex; however, this will need to be tested in future work.

The authors used endoscopy to measure the POm axons in the DLS activity, which makes it impossible to know if the progressive increase of POm response is due to an increase of activity from each individual neuron or if new neurons are progressively recruited in the process.

This is a good point. It would be necessary to perform chronic two-photon imaging of POm neurons (or chronic electrophysiological recordings) to determine whether the activity of individual neurons increased versus whether individual neuron activity levels remained similar but new neurons became active with learning. Even under baseline conditions, it is not known in detail what fraction of the population of POm neurons is active during sensory processing or behavior, highlighting how much is still to be discovered in this exciting area of neuroscience.

The picture presented in Figure 4 of the stimulation site is slightly concerning as there are hardly any fibres in neocortical layer 1 while there seems to be quite a lot of them in layer 4, suggesting that the animal here was injected in the VB. This is especially striking as the implantation and projection sites presented in Figures 1 and 2 are very clean and consistent with POm injection.

Although this image was selected to demonstrate the position of the POm injection site and optical fiber implant above striatal axons, the reviewer is correct that there appears to be mixed labeling of axons in L4 and L5a. In some cases, there was expression slightly outside the border of POm (see Fig. 1B, right), which might explain the cortical innervation pattern in this figure. While cortically bound VPM axons pass through the striatum, they do not form synaptic terminals until reaching the cortex (Hunnicutt et al., 2016). If, as may be the case, inhibitory opsins suppress release of neurotransmitter at synaptic terminals more effectively than action potential propagation in axons, it may be likely that optogenetic suppression of POm-striatal terminals is more effective than suppression of action potentials in off-target-labelled VPM axons of passage. Ideally, we could compare effects of suppression of POm-striatal synapses with POm-cortical synapses and VPM-cortical synapses, but this was outside the bandwidth of the present study.

Reviewer #2 (Public Review):

Summary:

Yonk and colleagues show that the posterior medial thalamus (POm), which is interconnected with sensory and motor systems, projects directly to major categories of neurons in the striatum, including direct and indirect pathway MSNs, and PV interneurons. Activity in POm-striatal neurons during a sensory-based learning task indicates a relationship between reward expectation and arousal. Inhibition of these neurons slows reaction to stimuli and overall learning. This circuit is positioned to feed salient event activation to the striatum to set the stage for effective learning and action selection.

Strengths:

The results are well presented and offer interesting insight into an understudied thalamostriatal circuit. In general, this work is important as part of a general need for an increased understanding of thalamostriatal circuits in complex learning and action selection processes, which have generally received less attention than corticostriatal systems.

Weaknesses:

There could be a stronger connection between the connectivity part of the data - showing that POm neurons context D1, D2, and PV neurons in the striatum but with some different properties - and the functional side of the project. One wonders whether the POm neurons projecting to these subtypes or striatal neurons have unique signaling properties related to learning, or if there is a uniform, bulk signal sent to the striatum. This is not a weakness per se, as it's reasonable for these questions to be answered in future papers.

We are very interested to understand the potentially distinct learning-related synaptic and circuit changes that potentially occur at the POm synapses with D1- and D2-SPNs and PV interneurons, and other striatal cell types. We agree that this would be an important topic for further investigation.

All the in vivo activity-related conclusions stem from data from just 5 mice, which is a relatively small sample set. Optogenetic groups are also on the small side.

We appreciate this point and agree that higher N can be important for observing robust effects. A factor of our experiments that helped reduce the number of animals used was the longitudinal design, with repeated measures in the same subjects. This allowed for the internal control of comparing learning effects in the same subject from naïve to expert stages and therefore increased robustness. Even with relatively small group sizes, results were statistically significant, suggesting that the use of more mice was unnecessary, which we considered consistent with best practice in the use of animals in research. We also note that our group sizes were consistent with other studies in the field.  

Reviewer #3 (Public Review):

Yonk and colleagues investigate the role of the thalamostriatal pathway. Specifically, they studied the interaction of the posterior thalamic nucleus (PO) and the dorsolateral striatum in the mouse. First, they characterize connectivity by recording DLS neurons in in-vitro slices and optogenetically activating PO terminals. PO is observed to establish depressing synapses onto D1 and D2 spiny neurons as well as PV neurons. Second, the image PO axons are imaged by fiber photometry in mice trained to discriminate textures. Initially, no trial-locked activity is observed, but as the mice learn PO develops responses timed to the audio cue that marks the start of the trial and precedes touch. PO does appear to encode the tactile stimulus type or outcome. Optogenetic suppression of PO terminals in striatum slow task acquisition. The authors conclude that PO provides a "behaviorally relevant arousal-related signal" and that this signal "primes" striatal circuitry for sensory processing.

A great strength of this paper is its timeliness. Thalamostriatal processing has received almost no attention in the past, and the field has become very interested in the possible functions of PO. Additionally, the experiments exploit multiple cutting-edge techniques.

There seem to be some technical/analytical weaknesses. The in vitro experiments appear to have some contamination of nearby thalamic nuclei by the virus delivering the opsin, which could change the interpretation. Some of the statistical analyses of these data also appear inappropriate. The correlative analysis of Pom activity in vivo, licking, and pupil could be more convincingly done.

The bigger weakness is conceptual - why should striatal circuitry need "priming" by the thalamus in order to process sensory stimuli? Why would such circuitry even be necessary? Why is a sensory signal from the cortex insufficient? Why should the animal more slowly learn the task? How does this fit with existing ideas of striatal plasticity? It is unclear from the experiments that the thalamostriatal pathway exists for priming sensory processing. In fact, the optogenetic suppression of the thalamostriatal pathway seems to speak against that idea.

We thank the reviewer for these constructive comments. The points are addressed below.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Do POm neurons innervate CINs also? The connection between the PF thalamus and CINs is mentioned in a couple of places - one question is how unique are the input patterns for the POm versus adjacent sensorimotor thalamic regions, including the PF? This isn't a weakness per se but knowing the answer to that question would help in forming a more complete picture of how these different thalamostriatal circuits do or do not contribute uniquely to learning and action selection.

Anatomical tracing evidence from Klug et al. (2018), which mapped brain-wide inputs to striatal cholinergic (ChAT) interneurons, suggests that Pf provides the majority of thalamic innervation of striatal ChAT neurons compared to other thalamic nuclei. Many other thalamic nuclei, including POm, showed very little or no labeling, suggesting weak innervation of ChAT interneurons. However, it is possible that these thalamic nuclei, including POm, do provide functional innervation of ChAT interneurons that is not sufficiently assessed by anatomical tracing.

Another difference between Pf and other thalamic nuclei (likely including POm) comes from anatomical tracing evidence (Smith et al., 2014; PMID: 24523677) which indicates that Pf inputs form the majority of their synapses onto dendritic shafts of SPNs, while other thalamic nuclei form synapses onto dendritic spines. Understanding the innervation patterns of POm-striatal projections beyond the three cell types we have studied here, including ChAT neurons and subcellular localization, would be an important area of further study.

It would be useful to know to what extent these POm-striatum neurons are activated generally during movement, versus this discrimination task specifically.

We agree that distinguishing general movement-related activity from task-specific activity would be very useful. Earlier work (Petty et al., 2021) showed a close relationship between POm neuron activity, spontaneous (task-free) whisker movements, and pupil-indexed arousal in head-restrained mice. Oram et al. (2024; PMID: 39003286) recently recorded VPM and POm in freely moving mice during natural movements, finding that activity of both nuclei correlated with head and whisker movements. These studies indicate that POm is generally coactive with exploratory head and whisker movements.

During task performance, the situation may change with training and attentional effects. For example, Petty and Bruno (2024) (https://elifesciences.org/reviewed-preprints/97188) showed that POm activity correlates more closely with task demands than tactile or visual stimulus modality. Our data indicate that POm axonal signals are increased at trial start during anticipation of tactile stimulus delivery and through the sensory discrimination period, then decrease to baseline levels during licking and water reward collection (Fig. 3). Results of Petty and Bruno (2024) together with ours suggest that POm is particularly active during the context of behaviorally relevant task performance. Thus, we think it is likely that, while pupil dilation indexes general movement and arousal, POm activity is more specific to movement and arousal associated with task engagement and behavioral performance. We have strengthened this point in the Discussion.

Many of the data panels and text for legends/axes are quite small, and the stroke on line art is quite faint - overall figures could be improved from a readability standpoint.

We thank the reviewer for their careful attention to the figures. 

Reviewer #3 (Recommendations For The Authors):

Major

(1) Page 4, the Results regarding PSP and distance from injection site. The r-squared is the wrong thing to look at to test for a relationship. One should look at the p-value on the coefficient corresponding to the slope. The p-value is probably significant given the figures, in which case there may be a relationship contrary to what is stated. All the low r-squared value says is that, if there is a relationship, it does not explain a lot of the PSP variability.

We thank the reviewer for alerting us this oversight. We have included the p value (p = 0.0293) in the figure and legend, and indicated that the relationship is “small but significant”.

(2) Figure 1B suggests that the virus injections extend beyond POm and into other thalamic structures. Do any of the results change if the injections contaminating other nuclei are excluded from the analysis? I am not suggesting the authors change the figures/analyses. I am simply suggesting they double-check.

We selected for injections that were predominantly expressing in POm as determined by post-hoc histological analysis (see Fig. 1, right). As above, we think that axons of passage that do not form striatal synapses are less likely to be suppressed than axons with terminals; however, this would need to be determined in further experiments. Because the preponderance of expression is within POm, we think the results would be similar even with a stricter selection criterion. 

(3) The authors conclude that POm and licking are not correlated (bottom of page 6 pertaining to Figures 3A-F). The danger of these analyses is that they assume that GCaMP8 is a perfect linear reporter of POm spikes. The reliability of GCaMP8 has been quantified in some cell types, but not thalamic neurons, which have relatively higher firing rates.

The reviewer is correct that the relationship between GCaMP8 fluorescence changes and spiking has not been sufficiently characterized in thalamic neurons, and that this would be important to do.

What if the indicator is simply saturated late into the trial (after the average reaction time)? It would look like there is no response and one would conclude no correlation, but there could be a very strong correlation.

While saturation is worthy of concern, the signal dynamics here argue against this possibility. The reason is that the signal increased in the early part of the trial and decreased by the end. If saturation was an issue, this would have been apparent during the initial increase. When the signal decreased in amplitude at the end of the trial, this indicates that the signal is not saturated because it is returning from a point closer to its maximum (and is becoming less saturated).

Also, what happens between trials? Are the correlations the same, stronger, weaker? Ideally, the authors would analyze the data during and between trials.

Between trials the signal did not show further changes in baseline beyond what was displayed at the start and end of behavioral trials. There were no consistent increases or decreases in signals between trials, except perhaps during strong whisking bouts. This is anecdotal because we did not analyze between-trial data. However, it is interesting and important to note that signals increased dramatically in amplitude from naïve, early learning to expert behavioral performance (Fig. 3), highlighting that POm-axonal signals relate to behavioral engagement and performance rather than spontaneous behaviors.  

(4) Axonal activity could also appear more correlated with the pupil than licking because pupil dynamics are slow like the dynamics of calcium indicators. These kernels could artificially inflate the correlation. Ideally, the authors could consider these temporal effects. Perhaps they could deconvolve the temporal profiles of calcium and pupil before correlating? Or equivalently incorporate the profiles into their analysis?

We analyzed the lick probability histograms, which had a temporal profile similar to the calcium signals (Fig. 3D,E), ruling out concerns about effects of temporal effects on correlations. It is also worth noting that we observed changes in correlations between calcium signals and pupil with learning stage (Fig. 3I), even though the temporal profiles (signal dynamics) are not changing. Thus, temporal effects of the signals themselves are not the driver of correlations, but rather the changes in relative timing between calcium signals and pupil, as occur with learning.

(5) The authors conclude that PO provides a "behaviorally relevant arousal-related signal" and that this signal "primes" striatal circuitry for sensory processing. The data here support the first part. It is not clear that the data support the second part, largely because it is vague what "priming" of sensory processing or "a key role in the initial stages of action selection (p.9) even means here. Why would such circuitry even be necessary? Why is a sensory signal from the cortex insufficient? Why should the animal more slowly learn the task? How does this fit with existing ideas of striatal plasticity? Some conceptual proposals from the authors, even if speculative and not offered as a conclusion, would be helpful.

We appreciate these good points and have added further consideration and revision of the concept of priming and potential roles in an extensively revised Discussion section.

(6) The photometry shows that PO turns on about 2 seconds before the texture presentation. PO's activity seems locked to the auditory cue, not the texture (Figure 2). This means that the attempt to suppress the thalamostriatal pathway with JAWS (Figure 4) is rather late, isn't it? Some PO signals surely go through. This seems to contradict the idea of priming above. It would be good if the authors could factor this into their narrative. Perhaps labelling the time of the auditory cue in Figure 4C would also be helpful.

The start of texture presentation (movement of the texture panel toward the mouse) and auditory cue occur at the same time. To clarify this, we added a label “start tone” in Figure 4C and also in Figure 2C.

For optogenetic (JAWS) suppression, we intentionally chose a time window between start tone onset and texture presentation, because our photometry experiments showed that this was when the preponderance of the signal occurred. However, the reviewer is correct that our chosen optogenetic suppression (JAWS) onset occurs shortly after the photometry signal has already started, potentially leaving the early photometry signal un-suppressed. Our motivation for choosing a restricted time window surrounding the texture presentation time was 1) to minimize illumination and potential heating of brain tissue; 2) to target a time window that avoids the auditory cue but covers stimulus presentation. We did not want to extend the duration of the suppression to before the trial started, because this could produce task-non-specific effects, such as distraction or loss of attention before the start of the trial.

Even if some signal were getting through before suppression, we don’t think this contradicts the possibility of ‘priming’, because the process underlying priming would still be disrupted even if not totally suppressed. This would alter the temporal relationship between POm-striatal inputs and further corticostriatal inputs (from S1 and M1 cortex, for example). We have included further consideration of these points and possible relation to the priming concept in the Discussion.

Minor

(1) Page 5, "the sensitivity metric is artificially increased". What do you mean "artificially"? The mice are discriminating better. It is true that either a change in HR or FAR can cause the sensitivity metric to change, but there is nothing artificial or misleading about this.

We removed the word artificial and clarified our definition of behaviorally Expert in this context:

“Mice were considered Expert once they had reached ≥ 0.80 Hit Rate and ≤ 0.30 FA Rate for two consecutive sessions in lieu of a strict sensitivity (d’) threshold; we found this definition more intuitive because d’ is enhanced as Hit Rate and FA Rate approach their extremes (0 or 1)”

(2) Page 7, "Upon segmentation (Figure S4G-J)". Do you mean "segregation by trial outcome"?

Corrected.

(3) Page 9, "POm projections may have discrete target-specific functions, such that POm-striatal inputs may play a distinct role in sensorimotor behavior compared to POm-cortical inputs". Would POm-cortical inputs not also be sensorimotor? The somatosensory cortex contains a lot of corticostriatal cells. It also has various direct and indirect links to the motor cortex as well.

We have clarified the wording here to convey the possibility that POm signals could be received and processed differently by striatal versus cortical circuitry, and have moved this statement to later in the discussion for better elaboration.

(4) The Methods state that male and female mice were used. Why not say how many of each and whether or not there are any sex-specific differences?

We added the following information to the Methods:

The number of male and female mice were as follows, by experiment type: 6 male, 4 female (electrophysiology); 3 male, 2 female (fiber photometry); 4 male, 5 female (optogenetics). Data were not analyzed for sex differences.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this series of studies, Locantore et al. investigated the role of SST-expressing neurons in the entopeduncular nucleus (EPNSst+) in probabilistic switching tasks, a paradigm that requires continued learning to guide future actions. In prior work, this group had demonstrated EPNSst+ neurons co-release both glutamate and GABA and project to the lateral habenula (LHb), and LHb activity is also necessary for outcome evaluation necessary for performance in probabilistic decision-making tasks. Previous slice physiology works have shown that the balance of glutamate/GABA co-release is plastic, altering the net effect of EPN on downstream brain areas and neural circuit function. The authors used a combination of in vivo calcium monitoring with fiber photometry and computational modeling to demonstrate that EPNSst+ neural activity represents movement, choice direction, and reward outcomes in their behavioral task. However, viral-genetic manipulations to synaptically silence these neurons or selectively eliminate glutamate release had no effect on behavioral performance in well-trained animals. The authors conclude that despite their representation of task variables, EPN Sst+ neuron synaptic output is dispensable for task performance.

Strengths and Weaknesses:

Overall, the manuscript is exceptionally scholarly, with a clear articulation of the scientific question and a discussion of the findings and their limitations. The analyses and interpretations are careful and rigorous. This review appreciates the thorough explanation of the behavioral modeling and GLM for deconvolving the photometry signal around behavioral events, and the transparency and thoroughness of the analyses in the supplemental figures. This extra care has the result of increasing the accessibility for non-experts, and bolsters confidence in the results.

(1) To bolster a reader's understanding of results, we suggest it would be interesting to see the same mouse represented across panels (i.e. Figures 1 F-J, Supplementary Figures 1 F, K, etc i.e via the inclusion of faint hash lines connecting individual data points across variables.

Thank you for the suggestion. The same mouse is now represented in Fig 1 and Fig 1—Figure Supplement 1 as a darkened circle so it can be followed across different panels. Photometry from this mouse was used as sample date in Figure 2b and Figure 2—figure supplement 1a-b.

(2) Additionally, Figure 3E demonstrates that eliminating the 'reward' and 'choice and reward' terms from the GLM significantly worsens model performance; to demonstrate the magnitude of this effect, it would be interesting to include a reconstruction of the photometry signal after holding out of both or one of these terms, alongside the 'original' and 'reconstructed' photometry traces in panel D. This would help give context for how the model performance degrades by exclusion of those key terms.

We have now added analyses and reconstructed photometry signals from GLMs excluding important predictors in Figure 3—figure supplement 1 and 2. We use the model where both “Direction and reward” were omitted as predictors for the GLM and showed photometry reconstructions aligned to behavioral events used for the full model (Figure 3—figure supplement 1) and partial model (Figure 3—figure supplement 2) to compare model performance.  

(3) Finally, the authors claimed calcium activity increased following ipsilateral movements. However, Figure 3C clearly shows that both SXcontra and SXipsi increase beta coefficients. Instead, the choice direction may be represented in these neurons, given that beta coefficients increase following CXipsi and before SEipsi, presumably when animals make executive decisions. Could the authors clarify their interpretation on this point?

We observe that calcium activity increases during ipsilateral choices as the animal moves toward the ipsilateral side port (e.g. CX_ipsi to SE_ipsi; Fig 2C and Fig 3C). The animal also makes other ipsiversive movements not during the “choice” phase of a trial such as when it is returning to the center port following a contralateral choice (e.g. SX_Contra to CE; Fig 2—figure supplement 1F and Fig 3C). We also observe an increase in calcium activity during these ipsiversive movements (e.g. SX_Contra to CE), but they are not as large as those observed during the choice phase (Fig 2—figure supplement 1G). Therefore, during the choice phase of a trial, activity contains signals related to ipsilateral movement and additional factors (e.g. executive decision making).    

(4) Also, it is not clear if there is a photometry response related to motor parameters (i.e. head direction or locomotion, licking), which could change the interpretation of the reward outcome if it is related to a motor response; could the authors show photometry signal from representative 'high licking' or 'low licking' reward trials, or from spontaneous periods of high vs. low locomotor speeds (if the sessions are recorded) to otherwise clarify this point?

Unfortunately, neither licks nor locomotion were recorded during the behavioral sessions when photometry was recorded. In Figure 2—figure supplement 1a we now show individual trials sorted by trial duration (time elapsed between CE and SE) to illustrate the dynamics of the photometry signal on fast vs slow trials within a session.  

(5) There are a few limitations with the design and timing of the synaptic manipulations that would improve the manuscript if discussed or clarified. The authors take care to validate the intersectional genetic strategies: Tetanus Toxin virus (which eliminates synaptic vesicle fusion) or CRISPR editing of Slc17a6, which prevents glutamate loading into synaptic vesicles. The magnitude of effect in the slice physiology results is striking. However, this relies on the co-infection of a second AAV to express channelrhodopsin for the purposes of validation, and it is surely the case that there will not be 100% overlap between the proportion of cells infected.

For the Tet-tox experiments in Figure 4 we estimate approximately 70±15% of EP^Sst+ neurons expressed Tet-tox based on our histological counts and published stereological counts in EP (Miyamoto and Fukuda, 2015). It is true that channelrhodopsin expression will not overlap 100% with cells infected by the other virus, indeed our in vitro synaptic physiology shows small residual postsynaptic currents following optogenetic stimulation either from incomplete blockade of synaptic release or neurons that expressed channelrhodopsin but not Tettx (Figure 4—figure supplement 1J-K). The same is shown for CRISPR mediated deletion of Slc17a6 (Fig 5 – Fig supplement 1J-K).  

(6) Alternative means of glutamate packaging (other VGluT isoforms, other transporters, etc) could also compensate for the partial absence of VGluT2, which should be discussed.

While single cell sequencing (Wallace et al, 2017) has shown EP^Sst+ neurons do not express Slc17a7/8 (vGlut1 or vGlut3) it is possible that these genes could be upregulated following CRISPR mediated deletion of Slc17a6, however we do not see evidence of this with our in vitro synaptic physiology (EPSCs are significant suppressed, Figure 5 – Fig supplement 1J-K) and therefore can conclude it is highly unlikely to occur to a significant degree in our experiments. This is now included in the Discussion.

(7) The authors do not perform a complimentary experiment to delete GABA release (i.e. via VGAT editing), which is understandable, given the absence of an effect with the pan-synaptic manipulation. A more significant concern is the timing of these manipulations as the authors acknowledge. The manipulations are all done in well-trained animals, who continue to perform during the length of viral expression. Moreover, after carefully showing that mice use different strategies on the 70/30 version vs the 90/10 version of the task, only performance on the 90/10 version is assessed after the manipulation. Together, the observation that EPNsst activity does not alter performance on a well-learned, 90/10 switching task decreases the impact of the findings, as this population may play a larger role during task acquisition or under more dynamic task conditions. Additional experiments could be done to strengthen the current evidence, although the limitation is transparently discussed by the authors.

As mentioned above, it is possible that a requirement for EP^Sst+ neurons could be revealed if the experiment was conducted with different parameters (either different reward probabilities, fluctuating reward probabilities within a session, or withholding additional training during viral expression). It is difficult to predict which version of the task, if any, would be most likely to reveal a requirement for EP^Sst+ neurons based on our results. We favor testing for EP^Sst+ function using a new behavioral paradigm that allows us to carefully examine task learning following EP manipulations in an independent study.

(8) Finally, intersectional strategies target LHb-projecting neurons, although in the original characterization, it is not entirely clear that the LHb is the only projection target of EPNsst neurons. A projection map would help clarify this point.

In a previous study we confirmed that EP^Sst+ neurons project exclusively to the LHb using cell-type specific rabies infection and examining all reported downstream regions for axon collaterals (Wallace et al 2017, Suppl. Fig 6F-G). When EP^Sst+ neurons were labeled we did not observe axon collaterals in known targets of EP such as ventro-antero lateral thalamus, red nucleus, parafasicular nucleus of the thalamus, or the pedunculopontine tegmental nucleus, only in the LHb. Additionally, using single cell tracing techniques, others have shown EP neurons that exclusively project to the LHb (Parent et al, 2001).

Overall, the authors used a pertinent experimental paradigm and common cell-specific approaches to address a major gap in the field, which is the functional role of glutamate/GABA co-release from the major basal ganglia output nucleus in action selection and evaluation. The study is carefully conducted, their analyses are thorough, and the data are often convincing and thought-provoking. However, the limitations of their synaptic manipulations with respect to the behavioral assays reduce generalizability and to some extent the impact of their findings.

Reviewer #2 (Public Review):

Summary:

This paper aimed to determine the role EP sst+ neurons play in a probabilistic switching task.

Strengths:

The in vivo recording of the EP sst+ neuron activity in the task is one of the strongest parts of this paper. Previous work had recorded from the EP-LHb population in rodents and primates in head-fixed configurations, the recordings of this population in a freely moving context is a valuable addition to these studies and has highlighted more clearly that these neurons respond both at the time of choice and outcome.

The use of a refined intersectional technique to record specifically the EP sst+ neurons is also an important strength of the paper. This is because previous work has shown that there are two genetically different types of glutamatergic EP neurons that project to the LHb. Previous work had not distinguished between these types in their recordings so the current results showing that the bidirectional value signaling is present in the EP sst+ population is valuable.

Weaknesses:

(1) One of the main weaknesses of the paper is to do with how the effect of the EP sst+ neurons on the behavior was assessed.

(a) All the manipulations (blocking synaptic release and blocking glutamatergic transmission) are chronic and more importantly the mice are given weeks of training after the manipulation before the behavioral effect is assessed. This means that as the authors point out in their discussion the mice will have time to adjust to the behavioral manipulation and compensate for the manipulations. The results do show that mice can adapt to these chronic manipulations and that the EP sst+ are not required to perform the task. What is unclear is whether the mice have compensated for the loss of EP sst+ neurons and whether they play a role in the task under normal conditions. Acute manipulations or chronic manipulations without additional training would be needed to assess this.

Unfortunately, when mice are given a three week break from behavioral training (the time required to allow for adequate viral expression) behavioral performance on the task (p(highport), p(switch), trial number, trial time, etc.) is significantly degraded. Animals do eventually recover to previous performance levels, but this takes place during a 4-5 day “relearning” period. Here we sought to examine if EP^Sst+ neurons are required for continued task performance and chose to continue to train the animals following viral injection to avoid the “relearning” period that occurs following an extended break from behavioral training which may have made it difficult to interpret changes in behavioral performance due to the viral manipulation vs relearning.  

Acute manipulations were not used because we planned to compare complete synaptic ablation (Tettx) and single neurotransmitter ablation (CRISPR Slc17a6) over similar time courses and we know of no acute manipulation that could achieve single neurotransmitter ablation. 

(b) Another weakness is that the effect of the manipulations was assessed in the 90/10 contingency version of the task. Under these contingencies, mice integrate past outcomes over fewer trials to determine their choice and animals act closer to a simple win-stay-lose switch strategy. Due to this, it is unclear if the EP sst+ neurons would play a role in the task when they must integrate over a larger number of conditions in the less deterministic 70/30 version of the task.

It is possible that a requirement for EP^Sst+ neurons could be revealed if the experiment was conducted with different parameters (either different reward probabilities, fluctuating reward probabilities within a session, or withholding additional training during viral expression). It is difficult to predict which version of the task, if any, would be most likely to reveal a requirement for EP^Sst+ neurons based on our results. We favor testing for EP^Sst+ function using a new behavioral paradigm that allows us to carefully examine task learning following EP manipulations in an independent study.

The authors show an intriguing result that the EP sst+ neurons are excited when mice make an ipsilateral movement in the task either toward or away from the center port. This is referred to as a choice response, but it could be a movement response or related to the predicted value of a specific action. Recordings while mice perform movement outside the task or well-controlled value manipulations within the session would be needed to really refine what these responses are related to.

If activity of EP^Sst+ neurons included a predicted value component, we would expect to see a change in activity during ipsilateral movements when the previous trial was rewarded vs unrewarded. This is examined in Fig 2—figure suppl. 2C, where we compare EP^Sst+ responses during ipsilateral trials when the previous trials were either rewarded (blue) or unrewarded (gray). We show that EP^Sst+ activity prior to side port entry (SE) is identical in these two trial types indicating that EP^Sst+ neurons do not show evidence of predicted value of an action in this context. Therefore, we conclude that increased EP^Sst+ activity during ipsilateral trials is primarily related to ipsilateral movement following CX (we call this the “choice” phase of the trial). We also show that other ipsiversive movements outside of the “choice” phase of a trial (such as the return to center port following a contralateral trial) show a smaller but significant increase in activity (Figure 2—figure supplement 1F-G). Therefore, whereas the activity observed during ipsilateral choice contains signals related to ipsilateral movement and additional factors, our data suggest that predicted value is not one of those factors. We will clarify this point and our definition of “choice” in the narrative.  

(2) The authors conclude that they do not see any evidence for bidirectional prediction errors. It is not possible to conclude this. First, they see a large response in the EP sst+ neurons to the omission of an expected reward. This is what would be expected of a negative reward prediction error. There are much more specific well-controlled tests for this that are commonplace in head-fixed and freely moving paradigms that could be tested to probe this. The authors do look at the effect of previous trials on the response and do not see strong consistent results, but this is not a strong formal test of what would be expected of a prediction error, either a positive or negative. The other way they assess this is by looking at the size of the responses in different recording sessions with different reward contingencies. They claim that the size of the reward expectation and prediction error should scale with the different reward probabilities. If all the reward probabilities were present in the same session this should be true as lots of others have shown for RPE. Because however this data was taken from different sessions it is not expected that the responses should scale, this is because reward prediction errors have been shown to adaptively scale to cover the range of values on offer (Tobler et al., Science 2005). A better test of positive prediction error would be to give a larger-than-expected reward on a subset of trials. Either way, there is already evidence that responses reflect a negative prediction error in their data and more specific tests would be needed to formally rule in or out prediction error coding especially as previous recordings have shown it is present in previous primate and rodent recordings.

We do not conclude that we see no evidence for RPE and the reviewer is correct in stating that a large increase in EP^Sst+ activity following omission of an expected reward would be expected of a negative reward prediction error. However, this observation alone is not strong enough evidence that EP^Sst+ neurons signal RPE. When we looked for additional evidence of RPE within our experiments we did not find consistent demonstrations of its existence in our data. When performing photometry measurements of dopamine release in the striatum, RPE signals are readily observed with a task identical to ours using trial history to as a modifier of reward prediction (Chantranupong, et al 2023). Of course, there could be a weaker more heterogeneous RPE signal in EP^Sst+ neurons that we cannot detect with our methods. As we state in the discussion, RPE signals may be present in a subset of individual neurons (as observed in Stephenson-Jones et al, 2016 and Hong and Hikosaka, 2008) which are below our detection threshold using fiber photometry. Additionally, Hong and Hikosaka, 2008 show that LHb-projecting GPi neurons show both positive and negative reward modulations which may obscure observation of RPE signals with photometry recordings that arise from population activity of genetically defined neurons.   

(3) There are a lot of variables in the GLM that occur extremely close in time such as the entry and exit of a port. If two variables occur closely in time and are always correlated it will be difficult if not impossible for a regression model to assign weights accurately to each event. This is not a large issue, but it is misleading to have regression kernels for port entry and exits unless the authors can show these are separable due to behavioral jitter or a lack of correlation under specific conditions, which does not seem to be the case.

It is true that two variables that are always correlated are redundant in a GLM. For example, center entry (CE) and center exit (CX) occur in quick succession in most trials and are highly correlated (Figure 1C). For this reason, when only one is removed as a predictor from the model but not the other there is a very small change in the MSE of the fit (Figure 3E, -CE or -CX). However, when both are removed model performance decreases further indicating that center-port nose-pokes do contribute to model performance (Figure 3E, -CE/CX). Due to the presence/absence of reward following side port entry there is substantial behavioral jitter (due to water consumption in rewarded trials) that the SE and SX are not always correlated, therefore the model performs worse when either are omitted alone, but even worse still when both SE/SX are omitted together (Figure 3E, -SE/SX). We will update Figure 3 and the narrative to make this more explicit.

Reviewer #3 (Public Review):

Summary:

The authors find that Sst-EPN neurons, which project to the lateral habenula, encode information about response directionality (left vs right) and outcome (rewarded vs unrewarded). Surprisingly, impairment of vesicular signaling in these neurons onto their LHb targets did not impair probabilistic choice behavior.

Strengths:

Strengths of the current work include extremely detailed and thorough analysis of data at all levels, not only of the physiological data but also an uncommonly thorough analysis of behavioral response patterns.

Weaknesses:

Overall, I saw very few weaknesses, with only two issues, both of which should be possible to address without new experiments:

(1) The authors note that the neural response difference between rewarded and unrewarded trials is not an RPE, as it is not affected by reward probability. However, the authors also show the neural difference is partly driven by the rapid motoric withdrawal from the port. Since there is also a response component that remains different apart from this motoric difference (Figure 2, Supplementary Figure 1E), it seems this is what needs to be analyzed with respect to reward probability, to truly determine whether there is no RPE component. Was this done?

We thank the reviewer for this comment, we believe this is particularly important for unrewarded trials as SE and SX occur in rapid succession. In Figure 2—figure supplement 2A-B we now show the photometry signal from Rewarded and Unrewarded ipsilateral trials aligned to SX for different reward probabilities. We quantify the signals for different reward probabilities during a 500ms window immediately prior to SX but find no differences between groups.  

(2) The current study reaches very different conclusions than a 2016 study by Stephenson-Jones and colleagues despite using a similar behavioral task to study the same Sst-EPN-LHb circuit. This is potentially very interesting, and the new findings likely shed important light on how this circuit really works. Hence, I would have liked to hear more of the authors' thoughts about possible explanations of the differences. I acknowledge that a full answer might not be possible, but in-depth elaboration would help the reader put the current findings in the context of the earlier work, and give a better sense of what work still needs to be done in the future to fully understand this circuit.

For example, the authors suggest that the Sst-EPN-LHb circuit might be involved in initial learning, but play less of a role in well-trained animals, thereby explaining the lack of observed behavioral effect. However, it is my understanding that the probabilistic switching task forces animals to continually update learned contingencies, rendering this explanation somewhat less persuasive, at least not without further elaboration (e.g. maybe the authors think it plays a role before the animals learn to switch?).

Also, as I understand it, the 2016 study used manipulations that likely impaired phasic activity patterns, e.g. precisely timed optogenetic activation/inhibition, and/or deletion of GABA/glutamate receptors. In contrast, the current study's manipulations - blockade of vesicle release using tetanus toxin or deletion of VGlut2, would likely have blocked both phasic and tonic activity patterns. Do the authors think this factor, or any others they are aware of, could be relevant?

We have added further discussion of the Stephenson-Jones, et al 2016 study as well as the Lazaridis, et al 2019 study which shows no effect of phasic stimulation of EP when specifically manipulating EP^Sst+ (vGat+/vGlut2+) neurons rather than vGlut2+ neurons as in the Stephenson-Jones study.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In some places, there seems to be a mismatch between referenced figures and texts. For example:

(1) The authors described that 'This increase in activity was seen for all three reward probabilities tested (90/10, 80/20, and 70/30) and occurred while the animal was engaged in ipsiversive movements as similar increases were observed following side exit (SX) on contralateral trials as the animal was moving from the contralateral side port back to the center port (Figure 2-Figure Supplement 1c)', but supplement 1c is not about calcium dynamics around the SX event. I presume they mean Figure 2-Figure Supplement 1d.

Yes, this will be corrected in the revised manuscript.

(2) The authors explained that increased EPSst+ neuronal activity following an unrewarded outcome was partially due to the rapid withdrawal of the animal's snout following an unrewarded outcome however, differences in rewarded and unrewarded trials were still distinguishable when signals were aligned to side port exit indicating that these increases in EPSst+ neuronal activity on unrewarded trials were a combination of outcome evaluation (unrewarded) and side port withdrawal occurring in quick succession (SX, Figure 2 - Figure Supplement 1d). I presume that they mean Figure 2 - Figure Supplement 1e.

Yes, this will be corrected in the revised manuscript.

Minor suggestions related to specific figure presentation are below:

Figure 2 and supplement figures:

(1) Figure 2B: the authors may consider presenting outcome-related signals recorded from all trials, including both ipsilateral and contralateral events, and align signals to SE when reward consumption presumably begins, rather than aligning to CE.

We have added sample recordings from ipsilateral and contralateral trials and sorted them by trial duration to allow for clearer presentation of activity following CE and SE (Figure 2—figure supplement 1a-b).

(2) The authors described that 'This increase in activity was seen for all three reward probabilities tested (90/10, 80/20, and 70/30) and occurred while the animal was engaged in ipsiversive movements as similar increases were observed following side exit (SX) on contralateral trials as the animal was moving from the contralateral side port back to the center port (Figure 2-Figure Supplement 1c)', but supplement 1c is not about calcium dynamics around the SX event. I presume they mean Figure 2-Figure Supplement 1d.

Yes, this will be corrected in the revised manuscript.

(3) The authors explained that increased EPSst+ neuronal activity following an unrewarded outcome was partially due to the rapid withdrawal of the animal's snout following an unrewarded outcome however, differences in rewarded and unrewarded trials were still distinguishable when signals were aligned to side port exit indicating that these increases in EPSst+ neuronal activity on unrewarded trials were a combination of outcome evaluation (unrewarded) and side port withdrawal occurring in quick succession (SX, Figure 2 -Figure Supplement 1d). I presume that they mean Figure 2 -Figure Supplement 1e.

Yes, this will be corrected in the revised manuscript.

Figure 3 and supplement figures:

(1) Figure 3C-F: it is hard to compare the amplitude of calcium signals between different behaviour events without a uniform y-axis.

The scale for the y-axis on Figure 3C-D is uniform for all panels. Figure 3E is also uniform for all boxplots. The reviewer may be referring to Figure 2C-F, but the y-axis for all of the photometry data is uniform for all panels and the horizontal line represents zero. The y-axis for the quantification on the right of each panel is scaled to the max/min for each comparison.

(2) Figure 3E is difficult to follow. The authors explained that the 'SE' variable is generated by collapsing the ipsilateral and contralateral port entries, and hence the variable has no choice of direction information. I assumed that the 'SX', 'CE', and 'CX' variables are generated similarly. It is not clear if this is the case for the 'side', 'centre' and 'choice' variables. The authors explained that 'omitting center port entry/exit together or individually also resulted in decreased GLM performance but to a smaller degree than the omission of choice direction (Figure 3e, "-Center")'. My understanding is that they created the Centre variable by collapsing ipsilateral and contralateral centre port entry/exit together. The Centre variable should have no choice of direction information. How is the Center variable generated differently from omitting centre port entry/exit together? I would ask the authors to explain the model and different variables a bit more thoroughly in the text.

We apologize for the confusion. All ten variables used to train the full GLM are listed in Fig. 3C. In Figure 3E variable(s) were omitted to test how they contributed to GLM performance (data labeled “None” is the full model with all variables). Omitted variables are now defined as follows: -Rew = Rew+Unrew removed, -Direction = Ipsi/Contra designation removed and collapsed into CE, CX, SE, SX, -Direction & Rew = Ipsi/Contra info removed from all variables + Rew/Unrew removed, -CE/CX = Ipsi/Contra CE and CX removed, -CE = Ipsi/contra CE removed, -CX = Ipsi/contra CX removed, -SE/SX = Ipsi/Contra SE and SX removed, -SE = Ipsi/contra SE removed, -SX = Ipsi/contra SX removed. This clarification has also been added to the Generalized Linear Model section of Materials and Methods.

Figure 5 and supplement figures:

There are no representative and summary figures show the specificity and efficiency of oChief-tdTomato or Tetx-GFP expression. Body weight changes following virus injection are not well described.

A representative image of Tettx GFP expression are shown in Fig. 4A and percent of infected EP^Sst+ neurons is described in the text (70±15.1% (mean±SD), 1070±230 neurons/animal, n=6 mice). Most oChief-tdTom animals were used for post-hoc electrophysiology experiments and careful quantification of viral expression was not possible. However, Slc17a6 deletion was confirmed in these animals (Fig. 5 – Fig supplement 1J-K) to confirm the manipulation was effective in the experimental group. A representative image of oChief-tdTom expression is shown in Fig. 5A.

We now mention the body weight changes observed following Tettx injection in the narrative.

Reviewer #2 (Recommendations For The Authors):

(1) In the RFLR section you state that "this variable decays...", a variable can't decay only the value of a variable can change. Also, it is not mentioned what variable is being discussed. There are lots of variables in the model so this should be made clear.

We now state, “This variable (β) changes over trials and is updated with new evidence from each new trial’s choice and outcome with an additional bias towards or away from its most recent choice (Figure 1-figure supplement 2A-C).”

(2) I couldn't find in the results section, or the methods section the details for the Tet tx experiments, were mice trained and tested on 90/10 only? Were they trained while the virus was expressing etc? This should be added.

In the methods section we state, ”For experiments where we manipulated synaptic release in EP^Sst+ neurons (Figures 4-5) we trained mice (reward probabilities 90/10, no transparent barrier present) to the following criteria for the 5 days prior to virus injection: 1) p(highport) per session was greater than or equal to 0.80 with a variance less than 0.003, 2) p(switch) per session was less than or equal to 0.15 with a variance less than 0.001, 3) the p(left port) was between 0.45-0.55 with a variance less than 0.005, and 4) the animal performed at least 200 trials in a session. The mean and variance for these measurements was calculated across the five session immediately preceding surgery. The criterion were determined by comparing performance profiles in separate animals and chosen based on when animals first showed stable and plateaued behavioral performance. Following surgery, mice were allowed to recover for 3 days and then continued to train for 3 weeks during viral expression. Data collected during the 5 day pre-surgery period was then compared to data collected for 10 sessions following the 3 weeks allotted for viral expression (i.e. days 22-31 post-surgery).”

Reviewer #3 (Recommendations For The Authors):

(1) The kernel in Figure 3C shows an activation prior to CE on "contra" trials that is not apparent in Figure 2C which shows no activation prior to CE on either contra or ipsi trials. Given that movement directionality prior to CE is dictated by the choice on the PREVIOUS trial, is the "contra" condition in 3C actually based on the previous trial? If so, this should be clarified.

On most “contra” trials the animal is making an ipsiversive movement just prior to CE as it returns to the center from the contralateral side-port (as most trials are no “switch” trials). Therefore, an increase in activity is expected and shown most clearly following SX for contralateral trials in Fig 2 –Fig suppl 1F. A significant increase in activity prior to CE on contra trials compared to ipsi trials can also be seen in Fig 2C, its just not as large a change as the increase observed following CE for ipsi. trials. The comparison between activity observed during the two types of ipsiversive movements is now shown directly in Figure 2—figure supplement 1G.

(2) Paragraph 7 of the discussion uses a phrase "by-in-large", which probably should be "by and large".

Thank you for the correction.

Editor's note:

Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

Readers would also benefit from coding individual data points by sex and noting N/sex.

Sex breakdown has been added to figure legends for each experiment, full statistical reporting is now also include in the figure legends.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Bell et. al. describes an analysis of the effects of removing one of two mutually exclusive splice exons at two distinct sites in the Drosophila CaV2 calcium channel Cacophony (Cac). The authors perform imaging and electrophysiology, along with some behavioral analysis of larval locomotion, to determine whether these alternatively spliced variants have the potential to diversify Cac function in presynaptic output at larval neuromuscular junctions. The author provided valuable insights into how alternative splicing at two sites in the calcium channel alters its function.

Strengths:

The authors find that both of the second alternatively spliced exons (I-IIA and I-IIB) that are found in the intracellular loop between the 1st and second set of transmembrane domains can support Cac function. However, loss of the I-IIB isoform (predicted to alter potential beta subunit interactions) results in 50% fewer channels at active zones and a decrease in neurotransmitter release and the ability to support presynaptic homeostatic potentiation. Overall, the study provides new insights into Cac diversity at two alternatively spliced sites within the protein, adding to our understanding of how regulation of presynaptic calcium channel function can be regulated by splicing.

Weaknesses:

The authors find that one splice isoform (IS4B) in the first S4 voltage sensor is essential for the protein's function in promoting neurotransmitter release, while the other isoform (IS4A) is dispensable. The authors conclude that IS4B is required to localize Cac channels to active zones. However, I find it more likely that IS4B is required for channel stability and leads to the protein being degraded, rather than any effect on active zone localization. More analysis would be required to establish that as the mechanism for the unique requirement for IS4B.

(1) We thank the reviewer for this important point. In fact, all three reviewers raised the same question, and the reviewing editor pointed out that caution or additional experiments were required to distinguish between IS4 splicing being important for cac channel localization versus channel stability/degradation. We provide multiple sets of experiments as well as text and figure revisions to strengthen our claim that the IS4B exon is required for cacophony channels to enter motoneuron presynaptic boutons and localize to active zones.

a. If IS4B was indeed required for cac channel stability (and not for localization to active zones) IS4A channels should be instable wherever they are. This is not the case because we have recorded somatodendritic cacophony currents from IS4A expressing adult motoneurons that were devoid of cac channels with the IS4B exon. Therefore, IS4A cac channels are not instable but underlie somatodendritic voltage dependent calcium currents in these motoneurons. These new data are now shown in the revised figure 3C and referred to in the text on page 7, line 42 to page 8 line 9.

b. Similarly, if IS4B was required for channel stability, it should not be present anywhere in the nervous system. We tested this by immunohistochemistry for GFP tagged IS4A channels in the larval CNS. Although IS4A channels are sparsely expressed, which is consistent with low expression levels seen in the Western blots (Fig. 1E), there are always defined and reproducible patterns of IS4A label in the larval brain lobes as well as in the anterior part of the VNC. This again shows that the absence of IS4A from presynaptic active zones is not caused by channel instability, because the channel is expressed in other parts of the nervous system. These data are shown in the new supplementary figure 1 and referred to in the text on page 15, lines 3 to 8.

c. As suggested in a similar context by reviewers 1 and 2, we now show enlargements of the presence of IS4B channels in presynaptic active zones as well as enlargements of the absence of IS4A channels in presynaptic active zones in the revised figures 2A-C and 3A. In these images, no IS4A label is detectable in active zones or anywhere else throughout the axon terminals, thus indicating that IS4B is required for expressing cac channels in the axon terminal boutons and localizing it to active zones. Text and figure legends have been adjusted accordingly.

d. Related to this, reviewer 1 also recommended to quantify the IS4A and ISB4 channel intensity and co-localization with the active zone marker brp (recommendation for authors). After following the reviewers’ suggestion to adjust the background values in IS4A and IS4B immunolabels to identical (revised Figs. 2A-C), it becomes obvious that IS4A channel are not detectable above background in presynaptic terminals or active zones, thus intensity is close to zero. We still calculated the Pearsons co-localization coefficient for both IS4 variants with the active zone marker brp. For IS4B channels the Pearson’s correlation coefficient is control like, just above 0.6, whereas for IS4A channels we do not find colocalization with brp (Pearson’s below 0.25). These new analyses are now shown in the revised figure 2D and referred to on page 6, lines 33 to 38.

e. Consistent with our finding that IS4B is required for cac channel localization to presynaptic active zones, upon removal of IS4B we find no evoked synaptic transmission (Fig. 2 in initial submission, now Fig. 3B).

Together these data are in line with a unique requirement of IS4B at presynaptic active zones (not excluding additional functions of IS4B), whereas IS4A containing cac isoforms are not found in presynaptic active zones and mediate different functions.

Reviewer #2 (Public Review):

This study by Bell et al. focuses on understanding the roles of two alternatively spliced exons in the single Drosophila Cav2 gene cac. The authors generate a series of cac alleles in which one or the other mutually exclusive exons are deleted to determine the functional consequences at the neuromuscular junction. They find alternative splicing at one exon encoding part of the voltage sensor impacts the activation voltage as well as localization to the active zone. In contrast, splicing at the second exon pair does not impact Cav2 channel localization, but it appears to determine the abundance of the channel at active zones.

Together, the authors propose that alternative splicing at the Cac locus enables diversity in Cav2 function generated through isoform diversity generated at the single Cav2 alpha subunit gene encoded in Drosophila.

Overall this is an excellent, rigorously validated study that defines unanticipated functions for alternative splicing in Cav2 channels. The authors have generated an important toolkit of mutually exclusive Cac splice isoforms that will be of broad utility for the field, and show convincing evidence for distinct consequences of alternative splicing of this single Cav2 channel at synapses. Importantly, the authors use electrophysiology and quantitative live sptPALM imaging to determine the impacts of Cac alternative splicing on synaptic function. There are some outstanding questions regarding the mechanisms underlying the changes in Cac localization and function, and some additional suggestions are listed below for the authors to consider in strengthening this study. Nonetheless, this is a compelling investigation of alternative splicing in Cav2 channels that should be of interest to many researchers.

(2) We believe that the additional data on cac IS4A isoform localization and function as detailed above (response to public review 1) has strengthened the manuscript and answered some of the remaining questions the reviewer refers to. We are also grateful for the specific additional reviewer suggestions which we have addressed point-by-point and refer to below (section recommendations for authors).

Reviewer #3 (Public Review):

Summary:

Bell and colleagues studied how different splice isoforms of voltage-gated CaV2 calcium channels affect channel expression, localization, function, synaptic transmission, and locomotor behavior at the larval Drosophila neuromuscular junction. They reveal that one mutually exclusive exon located in the fourth transmembrane domain encoding the voltage sensor is essential for calcium channel expression, function, active zone localization, and synaptic transmission. Furthermore, a second mutually exclusive exon residing in an intracellular loop containing the binding sites for Caβ and G-protein βγ subunits promotes the expression and synaptic localization of around ~50% of CaV2 channels, thereby contributing to ~50% of synaptic transmission. This isoform enhances release probability, as evident from increased short-term depression, is vital for homeostatic potentiation of neurotransmitter release induced by glutamate receptor impairment, and promotes locomotion. The roles of the two other tested isoforms remain less clear.

Strengths:

The study is based on solid data that was obtained with a diverse set of approaches. Moreover, it generated valuable transgenic flies that will facilitate future research on the role of calcium channel splice isoforms in neural function.

Weaknesses:

(1) Based on the data shown in Figures 2A-C, and 2H, it is difficult to judge the localization of the cac isoforms. Could they analyze cac localization with regard to Brp localization (similar to Figure 3; the term "co-localization" should be avoided for confocal data), as well as cac and Brp fluorescence intensity in the different genotypes for the experiments shown in Figure 2 and 3 (Brp intensity appears lower in the dI-IIA example shown in Figure 3G)? Furthermore, heterozygous dIS4B imaging data (Figure 2C) should be quantified and compared to heterozygous cacsfGFP/+.

According to the reviewer’s suggestion, we have quantified cac localization relative to brp localization by computing the Pearson’s correlation coefficient for controls and IS4A as well as IS4B animals. These new data are shown in the revised Fig. 2D and referred to on page 6, lines 33-38. Furthermore, we now confirm control-like Pearson’s correlation coefficients for all exon out variants except ΔIS4B and show Pearson’s correlation coefficients for all genotypes side-by-side in the revised Fig. 4D (legend has been adjusted accordingly). In addition, in response to the recommendations to authors, we now provide selective enlargements for the co-labeling of Brp and each exon out variant in the revised figures 2-4. We have also adjusted the background in Fig. 2C (ΔIS4B) to match that in Figs. 2A and B (control and ΔIS4A). This allows a fair comparison of cac intensities following excision of IS4B versus excision of IS4A and control (see also Fig 3). Together, this demonstrates the absence of IS4A label in presynaptic active zones much clearer. As suggested, we have also quantified brp puncta intensity on m6/7 across homozygous exon excision mutants and found no differences (this is now stated for IS4A/IS4B in the results text on page 6, lines 37/38 and for I-IIA/I-IIB on page 8, lines 42-44.). We did not quantify the intensity of cacophony puncta upon excision of IS4B because the label revealed no significant difference from background (which can be seen much better in the images now), but the brp intensities remained control-like even upon excision of IS4B.

(2) They conclude that I-II splicing is not required for cac localization (p. 13). However, cac channel number is reduced in dI-IIB. Could the channels be mis-localized (e.g., in the soma/axon)? What is their definition of localization? Could cac be also mis-localized in dIS4B? Furthermore, the Western Blots indicate a prominent decrease in cac levels in dIS4B/+ and dI-IIB (Figure 1D). How do the decreased protein levels seen in both genotypes fit to a "localization" defect? Could decreased cac expression levels explain the phenotypes alone?

We have now precisely defined what we mean by cac localization, namely the selective label of cac channels in presynaptic active zones that are defined as brp puncta, but no cac label elsewhere in the presynaptic bouton (page 6, lines 18 to 20). On the level of CLSM microscopy this corresponds to overlapping cac puncta and brp puncta, but no cac label elsewhere in the bouton. Based on the additional analysis and data sets outlined in our response 1 (see above) we conclude that excision of IS4B does not cause channel mislocalization because we find reproducible expression patterns elsewhere in the nervous system as well as somatodendritic cac current in ΔIS4B (for detail see above). Therefore, the isoforms containing the mutually exclusive IS4A exon are expressed and mediate other functions, but cannot substitute IS4B containing isoforms at the presynaptic AZ. In fact, our Western blots are in line with reduced cac expression if all isoforms that mediate evoked release are missing, again indicating that the presynapse specific cac isoforms cannot be replaced by other cac isoforms. This is also in line with the sparse expression of IS4A throughout the CNS as seen in the new supplementary figure 1 (for detail see above).

(3) Cac-IS4B is required for Cav2 expression, active zone localization, and synaptic transmission. Similarly, loss of cac-I-IIB reduces calcium channel expression and number. Hence, the major phenotype of the tested splice isoforms is the loss of/a reduction in Cav2 channel number. What is the physiological role of these isoforms? Is the idea that channel numbers can be regulated by splicing? Is there any data from other systems relating channel number regulation to splicing (vs. transcription or post-transcriptional regulation)?

Our data are not consistent with the idea that splicing regulates channel numbers. Rather, splicing can be used to generate channels with specific properties that match the demand at the site of expression. For the IS4 exon pair we find differences in activation voltage between IS4A and IS4B channels (revised Fig. 3C), with IS4B being required for sustained HVA current. IS4A does not localize to presynaptic active zones at the NMJ and is only sparsely expressed elsewhere in the NS (new supplementary Fig. 1). By contrast, IS4B is abundantly expressed in many neuropils. Therefore, taking out IS4B takes out the more abundant IS4 isoform. This is consistent with different expression levels for IS4 isoforms that have different functions, but we do not find evidence for splicing regulating expression levels per se.

Similarly, the I-II mutually exclusive exon pair differs markedly in the presence or absence of G-protein βγ binding sites that play a role in acute channel regulation as well the conservation of the sequence for β-subunit binding (see page 5, lines 9-17). Channel number reduction in active zones occurs specifically if expression of the cac channels with the G_βγ-binding site as well as the more conserved β-subunit binding is prohibited by excision of the I-IIB exon (see Fig. 5F). Vice versa, excision of I-IIA does not result in reduced channel numbers. This scenario is consistent with the hypothesis that conserved β-subunit binding affects channel number in the active zone (see page 17, lines 3 to 6 and lines 33-36), but we have no evidence that I-II splicing per se affects channel number.

(4) Although not supported by statistics, and as appreciated by the authors (p. 14), there is a slight increase in PSC amplitude in dIS4A mutants (Figure 2). Similarly, PSC amplitudes appear slightly larger (Figure 3J), and cac fluorescence intensity is slightly higher (Figure 3H) in dI-IIA mutants. Furthermore, cac intensity and PSC amplitude distributions appear larger in dI-IIA mutants (Figures 3H, J), suggesting a correlation between cac levels and release. Can they exclude that IS4A and/or I-IIA negatively regulate release? I suggest increasing the sample size for Canton S to assess whether dIS4A mutant PSCs differ from controls (Figure 2E). Experiments at lower extracellular calcium may help reveal potential increases in PSC amplitude in the two genotypes (but are not required). A potential increase in PSC amplitude in either isoform would be very interesting because it would suggest that cac splicing could negatively regulate release.

There are several possibilities to explain this, but as none of the effects is statistically significant, we prefer to not investigate this in further depth. However, given that we cannot find IS4A in presynaptic active zones (revised figures 2C and 3A plus the new enlargements 2Ci and 3Ai, revised text page 6, lines 22 to 24 and 29 to 31, and page 7, second paragraph, same as public response 1D) IS4A channels cannot have a direct negative effect on release probability. Nonetheless, given that IS4A containing cac isoforms mediate functions in other neuronal compartments (see revised Fig. 3C) it may regulate release indirectly by affecting e.g. action potential shape. Moreover, in response to the more detailed suggestions to authors we provide new data that give additional insight.

(5) They provide compelling evidence that IS4A is required for the amplitude of somatic sustained HVA calcium currents. However, the evidence for effects on biophysical properties and activation voltage (p. 13) is less convincing. Is the phenotype confined to the sustained phase, or are other aspects of the current also affected (Figure 2J)? Could they also show the quantification of further parameters, such as CaV2 peak current density, charge density, as well as inactivation kinetics for the two genotypes? I also suggest plotting peaknormalized HVA current density and conductance (G/Gmax) as a function of Vm. Could a decrease in current density due to decreased channel expression be the only phenotype? How would changes in the sustained phase translate into altered synaptic transmission in response to AP stimulation?

Most importantly, sustained HVA current is abolished upon excision of IS4B (not IS4A, we think the reviewer accidentally mixed up the genotype) and presynaptic active zones at the NMJ contain only cac isoforms with the IS4B exon. This indicates that the cac isoforms that mediate evoked release encode HVA channels. The somatodendritic currents shown in the revised figure 3C (previously 2J) that remain upon excision of IS4B are mediated by IS4A containing cac isoforms. Please note that these never localize to the presynaptic active zone, and thus do not contribute to evoked release. Therefore, the interpretation is that specifically sustained HVA current encoded by IS4B cac isoforms is required for synaptic transmission. Reduced cac current density due to decreased channel expression is not the cause for impaired evoked release upon IS4B excision, but instead, the cause is the absence of any cac channels in active zones. IS4B-containing cac isoforms encode sustained HVA current, and we speculate that this might be a well suited current to minimize cacophony channel inactivation in the presynaptic active zone. Given that HVA current shows fast voltage dependent activation and fast inactivation upon repolarization, it is useful at large intraburst firing frequencies as observed during crawling (Kadas et al., 2017) without excessive cac inactivation (see page 15, Kadas, lines 16 to 20).

However, we agree with the reviewer that a deeper electrophysiological analysis of splice isoform specific cac currents will be instructive. We have now added traces of control and ΔIS4B from a holding potential of -90 mv (revised Fig. 3C, bottom traces and revised text on page 7, line 43 to page 8, lines 1 to 10), and these are also consistent with IS4B mediating sustained HVA cac current. However, further analysis of activation and inactivation voltages and kinetics suffers form space clamp issues in recordings from the somata of such complex neurons (DLM motoneurons of the adult fly contain roughly 6000 µm of dendrites with over 4000 branches, Ryglewski et al., 2017, Neuron 93(3):632-645). Therefore, we will analyze the currents in a heterologous expression system and present these data to the scientific community as a separate study at a later time point.

(6) Why was the STED data analysis confined to the same optical section, and not to max. intensity z-projections? How many and which optical sections were considered for each active zone? What were the criteria for choosing the optical sections? Was synapse orientation considered for the nearest neighbor Cac - Brp cluster distance analysis? How do the nearest-neighbor distances compare between "planar" and "side-view" Brp puncta?

Maximum intensity z-projections would be imprecise because they can artificially suggest close proximity of label that is close by in x and y but far away in z. Therefore, the analysis was executed in xy-direction of various planes of entire 3D image stacks. We considered active zones of different orientations (Figs. 5C, D) to account for all planes. In fact, we searched the entire z-stacks until we found active zones of all orientations within the same boutons, as shown in figures 5C1-C6. The same active zone orientations were analyzed for all exon-out mutants with cac localization in active zones. The distance between cac and brp did not change if viewed from the side or any other orientation. We now explain this in more clarity in the results text on page 9, lines 23/24.

(7) Cac clusters localize to the Brp center (e.g., Liu et al., 2011). They conclude that Cav2 localization within Brp is not affected in the cac variants (p. 8). However, their analysis is not informative regarding a potential offset between the central cac cluster and the Brp "ring". Did they/could they analyze cac localization with regard to Brp ring center localization of planar synapses, as well as Brp-ring dimensions?

In the top views (planar) we did not find any clear offset in cac orientation to brp between genotypes. In such planar synapses (top views, Fig. 5D, left row) we did not find any difference in Brp ring dimensions. We did not quantify brp ring dimensions rigorously, because this study focusses on cac splice isoform-specific localization and function. Possible effects of different cac isoforms on brp-ring dimensions or other aspects of scaffold structure are not central to our study, in particular given that brp puncta are clearly present even if cac is absent from the synapse (Fig. 3A), indicating that cac is not instructive for the formation of the brp scaffold.

(8) Given the accelerated PSC decay/ decreased half width in dI-IIA (Fig. 5Q), I recommend reporting PSC charge in Figure 3, and PPR charge in Figures 5A-D. The charge-based PPRs of dI-IIA mutants likely resemble WT more closely than the amplitude-based PPR. In addition, miniature PSC decay kinetics should be reported, as they may contribute to altered decay kinetics. How could faster cac inactivation kinetics in response to single AP stimulation result in a decreased PSC half-width? Is there any evidence for an effect of calcium current inactivation on PSC kinetics? On a similar note, is there any evidence that AP waveform changes accelerate PSC kinetics? PSC decay kinetics are mainly determined by GluR decay kinetics/desensitization. The arguments supporting the role of cac splice isoforms in PSC kinetics outlined in the discussion section are not convincing and should be revised.

We agree that reporting charge in figure 3 is informative and do so in the revised text. Since the result (no significant difference in the PSCs between between CS, cac^GFP, ^ΔI-IIA, and transheterozygous I-IIA/I-IIB, but significantly smaller values in ΔI-IIB) remained unchanged no matter whether charge or amplitude were analyzed, we decided to leave the figure as is and report the additional analysis in the text (page 8, lines 40 to 42). This way, both types of analysis are reported. Please note that EPSC amplitude is slightly but not significantly increased upon excision of I-IIA (Fig. 4J), whereas EPSC half amplitude width is significantly smaller (Fig. 5Q, now revised Fig 6R). Together, a tendency of increased EPSC amplitudes and smaller half amplitude width result in statistically insignificant changes in EPSC in ∆I-IIA (now discussed on page 15, lines 37 to 40). We also understand the reviewer’s concern attributing altered EPSC kinetics to presynaptic cac channel properties. We have toned down our interpretation in the discussion and list possible alterations in presynaptic AP shape or cac channel kinetics as alternative explanations (not conclusions; see revised discussion on page 15, line 40 to page 16, line 2). Moreover, we have quantified postsynaptic GluRIIA abundance to test whether altered PSC kinetics are caused by altered GluRIIA expression. In our opinion, the latter is more instructive than mini decay kinetic analysis because this depends strongly on the distance of the recording electrode to the actual site of transmission in these large muscle cells. Although we find no difference in GluRIIA expression levels we now clearly state that we cannot exclude other changes in GluR receptor fields, which of course, could also explain altered PSC kinetics. We have updated the discussion on page 16, lines 2/3 accordingly.

(9) Paired-pulse ratios (PPRs): On how many sweeps are the PPRs based? In which sequence were the intervals applied? Are PPR values based on the average of the second over the first PSC amplitudes of all sweeps, or on the PPRs of each sweep and then averaged? The latter calculation may result in spurious facilitation, and thus to the large PPRs seen in dI-IIB mutants (Kim & Alger, 2001; doi: 10.1523/JNEUROSCI.21-2409608.2001).

We agree that the PP protocol and analyses had to be described more precisely in the methods and have done so on page 23, lines 31 to 37 in the methods. Mean PPR values are based on the PPRs of each sweep and then averaged. We are aware of the study of Kim and Alger 2001 and have re-analyzed the PP data in both ways outlined by the reviewer. We get identical results with either analyses method. Spurious facilitation is thus not an issue in our data. We now explain this in the methods section along with the PPR protocol. The large spread seen in dI-IIB is indeed caused by reduced calcium influx into active zones with fewer channels, as anticipated by the reviewer (see next point).

(10) Could the dI-IIB phenotype be simply explained by a decrease in channel number/ release probability? To test this, I propose investigating PPRs and short-term dynamics during train stimulation at lower extracellular Ca2+ concentration in WT. The Ca2+ concentration could be titrated such that the first PSC amplitude is similar between WT and dI-IIB mutants. This experiment would test if the increased PPR/depression variability is a secondary consequence of a decrease in Ca2+ influx, or specific to the splice isoform.

In fact, the interpretation that decreased PSC amplitude upon I-IIB excision is caused mainly by reduced channel number is precisely our interpretation (see discussion page 14, last paragraph to page 15, first paragraph in the original submission, now page 16, second paragraph paragraph). In addition, we are grateful for the reviewer’s suggestion to triturate the external calcium such that the first PSC amplitude in matches in ∆I-IIB and control. This experiment tests whether altered short term plasticity is solely a function of altered channel number or whether additional causes, such as altered channel properties, also play into this. We triturated the first pulse amplitude in ∆I-IIB to match control and find that paired pulse ratio and the variance thereof are not different anymore. Therefore, the differences observed in identical external calcium can be fully explained by altered channel numbers. This additional dataset is shown in the revised figures 6D and E and referred to in the results section on page 10, lines 14 to 25 and the discussion on page16, lines 36 to 38.

(11) How were the depression kinetics analyzed? How many trains were used for each cell, and how do the tau values depend on the first PSC amplitude? Time constants in the range of a few (5-10) milliseconds are not informative for train stimulations with a frequency of 1 or 10 Hz (the unit is missing in Figure 5H). Also, the data shown in Figures 5E-K suggest slower time constants than 5-10 ms. Together, are the data indeed consistent with the idea that dIIIB does not only affect cac channel number, but also PPR/depression variability (p. 9)?

For each animal the amplitudes of all subsequent PSCs in each train were plotted over time and fitted with a single exponential. For depression at 1 and 10 Hz, we used one train per animal, and 5-6 animals per genotype (as reflected in the data points in Figs. 6I, M). This is now explained in more detail in the revised methods section (page 23, lines 39 to 41). The tau values are not affected by the amplitude of the first PSC. First, we carefully re-fitted new and previously presented depression data and find that the taus for depression at low stimulation frequencies (1 and 10Hz) are not affected by exon excisions at the I-II site. We thank the reviewer for detecting our error in units and tau values in the previous figure panels 5H and L (this has now been corrected in the revised figure panels 6I and M). Given that PSC amplitude upon I-IIB excision is significantly smaller than in controls and following I-IIA excision, we suspected that the time course of depression at low stimulation frequency is not significantly affected by the amount of calcium influx during the first PSC. To further test this, we followed the reviewer ’s suggestion and re-measured depression at 1 and 10 Hz for cac-GFP controls and for delta I-IIB in a higher external calcium concentration (1.8 mM), so that the first PSC was increased in amplitude in both genotypes (1.8 mM external calcium triturates the PSC amplitude in delta I-IIB to match that of controls measured in 0.5 mM external calcium, see revised Figs. 6H, L). Neither in control, nor in delta I-IIB did this affect the time course of synaptic depression (see revised Figs. 6I, M). This indicates that at low stimulation frequencies (1 and 10Hz) the time course of depression is not affected by mean quantal content. This is consistent with the paired pulse ratio at 100 ms interpulse interval shown in figures 6A-D. However, for synaptic depression at 1 Hz stimulation the variability of the data is higher for delta I-IIB (independent of external calcium concentration, see rev. Fig. 6I), which might also be due to reduced channel number in this genotype. Taken together, the data are in line with the idea that altered cac channel numbers in active zones are sufficient to explain all effects that we observe upon I-IIB excision on PPRs and synaptic depression at low stimulation frequencies. This is now clarified in the revised text on page 12, lines 3 to 7.

(12) The GFP-tagged I-IIA and mEOS4b-tagged I-IIB cac puncta shown in Figure 6N appear larger than the Brp puncta. Endogenously tagged cac puncta are typically smaller than Brp puncta (Gratz et al., 2019). Also, the I-IIA and I-IIB fluorescence sometimes appear to be partially non-overlapping. First, I suggest adding panels that show all three channels merged. Second, could they analyze the area and area overlap of I-IIA and I-IIB with regard to each other and to Brp, and compare it to cac-GFP? Any speculation as to how the different tags could affect localization? Finally, I recommend moving the dI-IIA and dI-IIB localization data shown in Figure 6N to an earlier figure (Figure 1 or Figure 3).

We now show panels with the two I-II cac isoforms merged in the revised figure 7H (previously 6N). We also tested merging all three labels as suggested, but found this not instructive for the reader. We thank the reviewer for pointing out that the Brp puncta appeared smaller than the cac puncta in some panels. We carefully went through the data and found that the Brp puncta are not systematically smaller than the cac puncta. Please note that punctum size can appear quite differently, depending on different staining qualities as well as different laser intensities and different point spread in different imaging channels. The purpose of this figure was not to analyze punctum size and labeling intensity, but instead, to demonstrate that I-IIA and I-IIB are both present in most active zones, but some active zones show only I-IIB labeling, as quantified in figure 7I. We did not follow the suggestion to conduct additional co-localization analyses and compare it with cac-GFP controls, because Pearson co-localization coefficients for cac-GFP and all exon-out variants analyzed, including delta I-IIA and delta I-IIB are presented in the revised figure 4D. Moreover, delta I-IIA and delta I-IIB show similar Manders 1 and 2 co-localization coefficients with Brp (see Figs. 4E, F). We do not want to speculate whether the different tags have any effect on localization precision. Artificial differences in localization precision can also be suggested by different antibodies, but we know from our STED analyses with identical tags and antibodies for all isoforms that I-IIA and I-IIB co-localize identically with Brp (see Figs. 5A-E). Finally, we prefer to not move the figure because we believe it is informative to show our finding that active zones usually contain both splice I-II variants together with the finding that only I-IIB is required for PHP.

Recommendations for the authors:

Reviewing Editor Comments:

We thank you for your submission. All three reviewers urge caution in interpreting the S4 splice variant playing a role specifically in Cac localization, as opposed to just leading to instability and degradation. There are other issues with the electrophysiological experiments, a need for improved imaging and analyses, and some areas of interpretation detailed in the reviews.

We agree that additional data was required to conclude that IS4 splicing plays a specific role in cac channel localization and is not just leading to channel instability and degradation. As outlined in detail in our response to reviewer 1, comment 1, we conducted several sets of experiments to support our interpretation. First, electrophysiological experiments show that upon removal of IS4B, which eliminates synaptic transmission at the larval NMJ and cac positive label in presynaptic active zones, somatodendritic cac current is reliably recorded (new data in revised figure 3C). This is not in line with a channel instability or degradation effect, but instead with IS4B containing isoforms being required and sufficient for evoked release from NMJ motor terminals, whereas IS4A isoforms are not sufficient for evoked release from axon terminals, but IS4A isoforms alone can mediate a distinct component of somatodendritic calcium current. Second, immunohostochemical analyses reveal that IS4A, which is not present in NMJ presynaptic active zones, is expressed sparsely, but in reproducible patterns in the larval brain lobes and in specific regions of the anterior VNC parts (new supplementary figure 1). Again, the absence of a IS4A-containing cac isoform from presynaptic active zones but their simultaneous presence in other parts of the nervous system is in accord with isoform specific localization, but not with general channel isoform instability. Third, enlargements of NMJ boutons with brp positive presynaptic active zones confirm the absence of IS4A and the presence of IS4B in active zones (these enlargements are now shown in the revised figures 2A-C, 3A, and 4A-C). Fourth, as suggested we have quantified the Pearson co-localization of IS4 isoforms with Brp in presynaptic active zones (revised Fig. 2D). This confirms quantitatively similar co-localization of IS4B and control with Brp, but no co-localization of IS4A with Brp. In fact, the labeling intensity of IS4A in presynaptic active zones is quantitatively not significantly different from background, no IS4A label is detected anywhere in the axon terminals at the NMJ, but we find IS4 label in the CNS. Together, these data strongly support our interpretation that the IS4 splice site plays a distinct role in cac channel localization. Figure legends as well as results and discussion section have been modified accordingly (the respective page and line numbers are listed in our-point-by-point responses).

In addition, we have carefully addressed all other public comments as well as all other recommendations for authors by providing multiple new data sets, new image analyses, and revising text. Addressing the insightful comments of all three reviewers and the reviewing editor has greatly helped to make the manuscript better.

Reviewer #1 (Recommendations For The Authors):

The conclusion that the IS4B exon controls Cac localization to active zones versus simply being required for channel abundance is not well supported. The authors need to either mention both possibilities or provide stronger support for the active zone localization model if they want to emphasize this point.

We agree and have included several additional data sets as outlined in our response to point 1 of reviewer 1 and to the reviewing editor (see above). These new data strongly support our interpretation that the IS4B exon controls Cac localization to active zones and is not simply required for channel abundance. The additions to the figures and accompanying text (including the respective figure panel, page, and line numbers) are listed in the point-bypoint responses to the reviewers’ public suggestions.

Figure 2C staining for Cac localization in the delta 4B line is difficult to compare to the others, as the background staining is so high (muscles are green for example). As such, it is hard to determine whether the arrows in C are just background.

We had over-emphasized the green label to show that there really is no cacophony label in active zones. However, we agree that this hampered image interpretation. Thus, we have adjusted brightness such that it matches the other genotypes (see new figure panel 2C, and figure 3A, bottom). Revising the figure as suggested by the reviewer shows much more clearly that IS4B puncta are detected exclusively in presynaptic active zones, whereas IS4A channels are not detectable in active zones or anywhere else in the axon terminal boutons. Quantification of IS4A label in brp positive active zones confirms that labeling intensity is not significantly above background (page 6, lines 29 to 31 and page 7, lines 19 to 21). Therefore, IS4A is not detectable in active zones at the NMJ.

It seems more likely that the removal of the 4B exon simply destabilizes the protein and causes it to be degraded (as suggested by the Western), rather than mislocalizing it away from active zones. It's hard to imagine how some residue changes in the S4 voltage sensor would control active zone localization to begin with. The authors should note that the alternative explanation is that the protein is just degraded when the 4B exon is removed.

Based on additional data and analyses, we disagree with the interpretation that removal of IS4B disrupts protein integrity and present multiple lines of evidence that support sparse expression of IS4A channels (ΔIS4B). As outlined in our response to reviewer 1 and to the reviewing editor, we show (1) in new immunohistochemical stainings (new supplementary figure 1) that upon removal of IS4B, sparse label is detectable in the VNC and the brain lobes (for detail see above). (2) In our new figure 3C, we show cacophony-mediated somatodendritic calcium currents recorded from adult flight motoneurons in a control situation and upon removal of IS4B that leaves only IS4A channels. This clearly demonstrates that IS4A underlies a substantial component of the HVA somatodendritic calcium current, although it is absence from axon terminals. This is in line with isoform specific functions at different locations, but not with IS4A instability/degradation. (3) We do not agree with the reviewer’s interpretation of the Western Blot data in figure 1E (formerly figure 1D). Together with our immunohistochemical data that show sparse cacophony IS4A expression, we think that the faint band upon removal of IS4B in a heterozygous background (that reduces labeled channels even further) reflects the sparseness of IS4A expression. This sparseness is not due to channel instability, but to IS4A functions that are less abundant than the ubiquitously expressed cac^IS4B channels at presynaptic active zones of fast chemical synapses (see page 15, lines 24 to 29).

If they really want to claim the 4B exon governs active zone localization, much higher quality imaging is required (with enlarged views of individual boutons and their AZs, rather than the low-quality full NMJ imaging provided). Similarly, higher resolution imaging of Cac localization at Muscle 12 (Figure 2H) boutons would be very useful, as the current images are blurry and hard to interpret. Figure 6N shows beautiful high-resolution Cac and Brp imaging in single boutons for the I-II exon manipulations - the authors should do the same for the 4B line. For all immuno in Figure 2, it is important to quantify Cac intensity as well. There is no quantification provided, just a sample image. The authors should provide quantification as they do for the delta I-II exons in Figure 3.

We did as suggested and added figure panels to figure 2A-C and to new figures 3A (formerly part of figure 2 and 4A-C (formerly figure 3) showing magnified label at the NMJ AZs to better judge on cacophony expression after exon excision. These data are now referred to in the results section on page 6, lines 22 to 24, page 7, lines 18 to 21 and page 8, lines 17/18.

As suggested, we now also provide quantification of co-localization with brp puncta as Pearson’s correlation coefficient for control, IS4B, and IS4A in the new figure panel 2D (text on page 6, lines 34 to 38). This further underscores control-like active zone localization of IS4B but no significant active zone localization of IS4A. As suggested, we quantified now also the intensity of IS4B label in active zones, and it was not different from control (see revised figure 4H and text on page 8, lines 38/39). We did not quantify the intensity of IS4A label, because it was not over background (text, page 6, lines 30/31).

Reviewer #2 (Recommendations For The Authors):

(1a) Questions about the engineered Cac splice isoform alleles:

The authors using CRISPR gene editing to selectively remove the entire alternatively spliced exons of interest. Do the authors know what happens to the cac transcript with the deleted exon? Is the deleted exon just skipped and spliced to the next exon? Or does the transcript instead undergo nonsense-mediated decay?

We do not believe that there is nonsense mediated mRNA decay, because for all exon excisions the respective mRNA and protein are made. Protein has been detected on the level of Western blotting and immunocytochemistry. Therefore, we are certain that the mRNA is viable for each exon excision (and we have confirmed this for low abundance cac protein isoforms by rt-PCR), but only subsets of cac isoforms can be made from mRNAs that are lacking specific exons. However, we can not make any statements as to whether the lack of specific protein isoforms exerts feedback on mRNA stability, the rate of transcription and translation, or other unknown effects.

(1b) While it is clear that the IS4 exons encode part of the voltage sensor in the first repeat, are there studies in Drosophila to support the putative Ca-beta and G-protein beta-gamma binding sites in the I-II loop? Or are these inferred from Mammalian studies?

To the best of our knowledge, there are no studies in Drosophila that unambiguously show Caβ and Gβγ binding sites in the I-II loop of cacophony. However, sequence analysis strongly suggests that I-IIB contains both, a Caβ as well as a Gβγ binding site (AID: α-interacting domain) because the binding motif QXXER is present. In mouse Cav2.1 and Ca_v2.2 channels the sequence is QQIER, while in Drosophila cacophony I-IIB it is QQLER. In the alternative IIIA, this motif is not present, strongly suggesting that G_βγ subunits cannot interact at the AID. However, as already suggested by Smith et al. (1998), based on sequence analysis, Ca_β should still be able to bind, although possibly with a lower affinity. We agree that this information should be given to the reader and have revised the text accordingly on page 5, lines 9 to 17.

(1c) The authors assert that splicing of Cav2/cac in flies is a means to encode diversity, as mammals obviously have 4 Cav2 genes vs 1 in flies. However, as the authors likely know, mammalian Cav2 channels also have various splice isoforms encoded in each of the 4 Cav2 genes. The authors should discuss in more detail what is known about the splicing of individual mammalian Cav2 channels and whether there are any homologous properties in mammalian channels controlled by alternative splicing.

We agree and now provide a more comprehensive discussion of vertebrate Ca_v2 splicing and its impact on channel function. In line to what we report in Drosophila, properties like G_βγ binding and activation voltage can also be affected by alternative splicing in vertebrate Ca_v2 channel, through the exon patterns are quite different from Drosophila. We integrated this part on page 14, first paragraph) in the revised discussion. The respective text is below for the reviewer’s convenience:

“However, alternative splicing increases functional diversity also in mammalian Ca_v2 channels. Although the mutually exclusive splice site in the S4 segment of the first homologous repeat (IS4) is not present in vertebrate Cav channels, alternative splicing in the extracellular linker region between S3 and S4 is at a position to potentially change voltage sensor properties (Bezanilla 2002). Alternative splice sites in rat Ca_v2.1 exon 24 (homologous repeat III) and in exon 31 (homologous repeat IV) within the S3-S4 loop modulate channel pharmacology, such as differences in the sensitivity of Ca_v2.1 to Agatoxin. Alternative splicing is thus a potential cause for the different pharmacological profiles of P- and Q-channels (both Ca_v2.1; Bourinet et al. 1999). Moreover, the intracellular loop connecting homologous repeats I and II is encoded by 3-5 exons and provides strong interaction with G_βγ-subunits (Herlitze et al. 1996). In Ca_v2.1 channels, binding to G_βγ subunits is potentially modulated by alternative splicing of exon 10 (Bourinet et al. 1999). Moreover, whole cell currents of splice forms α1A-a (no Valine at position 421) and α1A-b (with Valine) represent alternative variants for the I-II intracellular loop in rat Ca_v2.1 and Ca_v2.2 channels. While α1A-a exhibits fast inactivation and more negative activation, α1A-b has delayed inactivation and a positive shift in the IV-curve (Bourinet et al. 1999). This is phenotypically similar to what we find for the mutually exclusive exons at the IS4 site, in which IS4B mediates high voltage activated cacophony currents while IS4A channels activate at more negative potentials and show transient current (Fig. 3; see also Ryglewski et al. 2012). Furthermore, altered Ca_β interaction have been shown for splice isoforms in loop III (Bourinet et al. 1999), similar to what we suspect for the I-II site in cacophony. Finally, in mammalian VGCCs, the C-terminus presents a large splicing hub affecting channel function as well as coupling distance to other proteins. Taken together, Ca_v2  channel diversity is greatly enhanced by alternative splicing also in vertebrates, but the specific two mutually exclusive exon pairs investigated here are not present in vertebrate Ca_v2 genes.”

(1d) In Figure 1, it would be helpful to see the entire cac genomic locus with all introns/exons and the 4 specific exons targeted for deletion.

We agree and have changed figure 1 accordingly.

(2a) Cav2.IS4B deletion alleles:

More work is necessary to explain the localization of Cac controlled by the IS4B exon. First, can the authors determine whether actual Cac channels are present at NMJ boutons? The authors seem to indicate that in the IS4B deletion mutants, some Cac (GFP) signal remains in a diffuse pattern across NMJ boutons. However, from the imaging of wild-type Cac-GFP (and previous studies), there is no Cac signal outside of active zones defined by the BRP signal. It would benefit the study to a) take additional, higher resolution images of the remaining Cac signal at NMJs in IS4B deletion mutants, and b) comment on whether the apparent remaining signal in these mutants is only observed in the absence of IS4Bcontaining Cac channels, or if the IS4A-positive channels are normally observed (but perhaps mis-localized?).

We have conducted additional analyses to show convincingly that IS4A channels (that remain upon IS4B deletion) are absent from presynaptic active zone. Please see also responses to reviewers 1 and 3. By adjusting the background values in of CLSM images to identical values in control, delta IS4A, and delta IS4B, as well as by providing selective enlargements as suggested, the figure panels 2C, Ci and 3A now show much clearer, that upon deletion of IS4B no cac label remains in active zones or anywhere else in the axon terminal boutons (see text on page 6, lines 22 to 24). This is further confirmed by quantification showing the in IS4B mutants cac labeling intensity in active zones is not above background (see text on page 6, lines 27 to 31). We never intended to indicate that there was cac signal outside of active zones defined by the brp signal, and we now carefully went through the text to not indicate this possibility unintentionally anywhere in the manuscript.

(2b) Do the authors know whether any presynaptic Ca2+ influx is contributed by IS4Apositive Cac channels at boutons, given the potential diffuse localization? There are various approaches for doing presynaptic Ca2+ imaging that could provide insight into this question.

We agree that this is an interesting question. However, based on the revisions made, we now show with more clarity that IS4A channels are absent from the presynaptic terminal at the NMJ. IS4A labeling intensities within active zones and anywhere else in the axon terminals are not different from background (see text on page 6, lines 27 to 31 and revised Figs. 2C, Ci, and 3A with new selective enlargements in response to comments of both other reviewers). This is in line with our finding that evoked synaptic transmission from NMJ axon terminals to muscle cells is mostly absent upon excision of IS4B (see Fig. 3B). The very small amplitude EPSC (below 5 % of the normal amplitude of evoked EPSCs) that can still be recorded in the absence of IS4B is similar to what is observed in cac null mutant junctions and is mediated by calcium influx through another voltage gated calcium channels, a Ca_v1 homolog named Dmca1D, as we have previously published (Krick et al., 2021, PNAS 118(28):e2106621118. Gathering additional support for the absence of IS4A from presynaptic terminals by calcium imaging experiments would suffer significantly from the presence of additional types of VGCCs in presynaptic terminals (for sure Dmca1D (Krick et al., 2021) and potentially also the Ca_v3 homolog DmαG or Dm-α1T). Such experiments would require mosaic null mutants for cac and DmαG channels in a mosaic IS4B excision mutant, which, if feasible at all, would be very hard and time consuming to generate. In the light of the additional clarification that IS4A is not located in NMJ axon terminal boutons, as shown by additional labeling intensity analysis, revised figures with selective enlargement, and revised text, we feel confident to state that IS4A is not sufficient for evoked SV release.

(2c) Mechanistically, how are amino acid changes in one of the voltage sensing domains in Cac related to trafficking/stabilization/localization of Cac to AZs?

This is an exciting question that has occupied our discussions a lot. Some sorting mechanism must exist that recognizes the correct protein isoforms, just as sorting and transport mechanisms exist that transport other synaptic proteins to the synapse. We do not think that the few amino acid changes in the voltage sensor are directly involved in protein targeting. We rather believe that the cacophony variants that happen to contain this specific voltage sensor are selected for transport out to the synapse. There are possibilities to achieve this cell biological, but we have not further addressed potential mechanisms because we do not want enter the realms of speculation.

(3) How are auxiliary subunits impacted in the Cac isoform mutants?

Recent work by Kate O'Connor-Giles has shown that both Stj and Ca-Beta subunits localize to active zones along with Cac at the Drosophila NMJ. Endogenously tagged Stj and CaBeta alleles are now available, so it would be of interest to determine if Stj and particular Cabeta levels or localization change in the various Cac isoform alleles. This would be particularly interesting given the putative binding site for Ca-beta encoded in the I-II linker.

We agree that the synthesis of the work of Kate O'Connor-Giles group and our study open up new avenues to explore exciting hypotheses about differential coupling of specific cacophony splice isoforms with distinct accessory proteins such as Caβ and α₂δ subunits. However, this requires numerous full sets of additional experiments and is beyond the scope of this study.

(4a) Interpretation of short-term plasticity in the I-IIB exon deletion:

The changes in short-term plasticity presented in Figure 5 are interpreted as an additional phenotype due to the loss of the I-IIB exon, but it seems this might be entirely explained simply due to the reduced Cac levels. Reduced Cac levels at active zones will obviously reduce Ca2+ influx and neurotransmitter release. This may be really the only phenotype/function of the I-IIB exon. Hence, to determine whether loss of the I-IIB exon encodes any functions in short-term plasticity, separate from reduced Cac levels, the authors should compare short-term plasticity in I-IIB loss alleles compared to wild type with starting EPSC amplitudes are equal (for example by reducing extracellular Ca2+ levels in wild type to achieve the same levels at in Cac I-IIB exon deleted alleles). Reduced release probability, simply by reduced Ca2+ influx (either by reduced Cac abundance or extracellular Ca2+) should result in more variability in transmission, so I am not sure there is any particular function of the I-IIB exon in maintaining transmission variability beyond controlling Cac abundance at active zones.

For two reasons we are particularly grateful for this comment. First, it shows us that we needed to explain much clearer that our interpretation is that changes in paired pulse ratios (PPRs) and in depression at low stimulation frequencies are a causal consequence of lower channel numbers upon I-IIB exon deletion, precisely as pointed out by the reviewer. We have carefully revised the text accordingly on page 10, lines 14-25, page 11, lines 3-7 and 22-28; page 16, lines 36-38. Second, the experiment suggested by the reviewer is superb to provide additional evidence that the cause of altered PPRs is in fact reduced channel number, but not altered channel properties. Accordingly, we have conducted additional TEVC recordings in elevated external calcium (1.8 mM) so that the single PSC amplitudes in I-IIB excision animals match those of controls in 0.5 mM extracellular calcium. This makes the amplitudes and the variance of PPR for all interpulse intervals tested control-like (see revised Figs. 6D, E). This strongly indicates that differences observed in PPRs as well as the variance thereof were caused by the amount of calcium influx during the first EPSC, and thus by different channel numbers in active zones.

(4b) Another point about the data in Figure 5: If "behaviorally relevant" motor neuron stimulation and recordings are the goal, the authors should also record under physiological Ca2+ conditions (1.8 mM), rather than the highly reduced Ca2+ levels (0.5 mM) they are using in their protocols.

Although we doubt that the effective extracellular calcium concentration that determines the electromotoric force for calcium to enter the ensheathed motoneuron terminals in vivo during crawling is known, we followed the reviewer’s suggestion partly and have repeated the high frequency stimulation trains for ΔI-IIB in 1.8 mM calcium. As for short-term plasticity this brings the charge conducted to values as observed in control and in ΔI-IIA in 0.5 mM calcium. Therefore, all difference observed in previous figure 5 (now revised figure 6) can be accounted to different channel numbers in presynaptic active zones. This is now explained on page 11, lines 19-28. For controls recordings at high frequency stimulation in higher external calcium (e.g. 2 mM) have previously been published and show significant synaptic depression (e.g. Krick et al., 2021, PNAS). Given that in the exon out variants we do not expect any differences except from those caused by different channel numbers, we did not repeat these experiments for control and ΔI-IIA.

(5a) Mechanism of Cac's role in PHP :

As the authors likely know, mutations in Cac were previously reported to disrupt PHP expression (see Frank et al., 2006 Neuron). Inexplicably, this finding and publication were not cited anywhere in this manuscript (this paper should also be cited when introducing PhTx, as it was the first to characterize PhTx as a means of acutely inducing PHP). In the Frank et al. paper (and in several subsequent studies), PHP was shown to be blocked in mutations in Cac, namely the CacS allele. This allele, like the I-IIB excision allele, reduces baseline transmission presumably due to reduced Ca2+ influx through Cac. The authors should at a minimum discuss these previous findings and how they relate to what they find in Figure 6 regarding the block in PHP in the Cac I-IIB excision allele.

We thank the reviewer for pointing this out and apologize for this oversight. We agree that it is imperative to cite the 2006 paper by Frank et al. when introducing PhTx mediated PHP as well as when discussing cac the effects of cac mutants on PHP together with other published work. We have revised the text accordingly on page 12, lines 9-11 and 21-23 and on page 17, lines 29-33.

In terms of data presentation in Fig. 6, as is typical in the field, the authors should normalize their mEPSC/QC data as a percentage of baseline (+PhTx/-PhTx). This makes it easier to see the reduction in mEPSC values (the "homeostatic pressure" on the system) and then the homeostatic enhancement in QC. Similarly, in Fig. 6M, the authors should show both mEPSC and QC as a percentage of baseline (wild type or non-GluRIIA mutant background).

We agree and have changed figure presentation accordingly. Figure 7 (formerly figure 6) was updated as was the accompanying results text on page 12, lines 23-40.

(6) Cac I-IIA and I-IIB excision allele colocalization at AZs:

These are very nice and important experiments shown in Figures 6N and O, which I suggest the authors consider analyzing in further detail. Most significantly:

(6i) The authors nicely show that most AZs have a mix of both Cac IIA and IIB isoforms. Using simple intensity analysis, can the authors say anything about whether there is a consistent stoichiometric ratio of IIA vs IIB at single AZs? It is difficult to extract actual numbers of IIA vs IIB at individual AZs without having both isoforms labeled mEOS4b, but as a rough estimate can the authors say whether the immunofluorescence intensity of IIA:IIB is similar across each AZ? Or is there broad heterogeneity, with some AZs having low vs high ratios of each isoform (as the authors suggest across proximal to distal NMJ AZs)?

We agree and have conducted experiments and analyses to provide these data. We measured the cac puncta fluorescence intensities for heterozygous cac^sfGFP/cac, cacIIIA^sfGFP/cacI-IIB, and cacI-IIB^sfGFP/cacI-IIA animals. We preferred this strategy, because intensity was always measured from cac puncta with the same GFP tag. Next, we normalized all values to the intensities obtained in active zones from heterozygous cac^sfGFP/cac controls and then plotted the intensities of I-IIA versus I-IIB containing active zones side by side. Across junctions and animals, we find a consistent ratio 2:1 in the relative intensities of I-IIB and I-IIA, thus indicating on average roughly twice as many I-IIB as compared to I-IIA channels across active zones. This is consistent with the counts in our STED analysis (see Fig. 5F). These new data are shown in the new figure panel 7J and referred to on page 13, lines 10-16 in the revised text.

(6ii) Intensity analysis of Cac IIA vs IIB after PHP: Previous studies have shown Cac abundance increases at NMJ AZs after PHP. Can the authors determine whether both Cac IIA vs IIB isoforms increase after PHP or whether just one isoform is targeted for this enhancement?

We already show that PHP is not possible in the absence of I-IIB channels (see figure 7). However, we agree that it is an interesting question to test whether I-IIA channel are added in the presence of I-IIB channels during PHP, but we consider this a detail beyond the scope of this study.

Minor points:

(1) Including line numbers in the manuscript would help to make reviewing easier.

We agree and now provide line numbers.

(2) Several typos (abstract "The By contrast", etc).

We carefully double checked for typos.

(3) Throughout the manuscript, the authors refer to Cac alleles and channels as "Cav2", which is unconventional in the field. Unless there is a compelling reason to deviate, I suggest the authors stick to referring to "Cac" (i.e. cacdIS4B, etc) rather than Cav2. The authors make clear in the introduction that Cac is the sole fly Cav2 channel, so there shouldn't be a need to constantly reinforce that cac=Cav2.

We agree and have changed all fly Ca_v2 reference to cac.

(4) In some figures/text the authors use "PSC" to refer to "postsynaptic current", while in others (i.e. Figure 6) they switch to the more conventional terms of mEPSC or EPSC. I suggest the authors stick to a common convention (mEPSC and EPSC).

We have changed PSC to EPSC throughout.

Reviewer #3 (Recommendations For The Authors):

(1) The abstract could focus more on the results at the expense of the background.

We agree and have deleted the second introductory background sentence and added information on PPRs and depression during low frequency stimulation.

(2) What does "strict" active zone localization refer to? Could they please define the term strict?

Strict active zone localization means that cac puncta are detected in active zones but no cac label above background is found anywhere else throughout the presynaptic terminal, now defined on page 6, lines 27-29.

(3) Single boutons/zoomed versions of the confocal images shown in Figures 2A-C, 2H, and 3A-C would be very helpful.

We have provided these panels as suggested (see above and revised figures 2-4). Figure 3 is now figure 4.

(4) The authors cite Ghelani et al. (2023) for increased cac levels during homeostatic plasticity. I recommend citing earlier work making similar observations (Gratz et al., 2019; DOI: 10.1523/JNEUROSCI.3068-18.2019), and linking them to increased presynaptic calcium influx (Müller & Davis, 2012; DOI: 10.1016/j.cub.2012.04.018).

We agree and have added Gratz et al. 2019 and Davis and Müller 2012 to the results section on page 12, lines 17/18 and lines 21-23, in the discussion on page 17, lines 29-33.

(5) The data shown in Figure 3 does not directly support the conclusion of altered release probability in dI-IIB. I therefore suggest changing the legend's title.

We have reworded to “Excisions at the I-II exon do not affect active zone cacophony localization but can alter cacsfGFP label intensity in active zones and PSC amplitude” as this is reflecting the data shown in the figure panels more directly.

(6) It would be helpful to specify "adult flight muscle" in Figure 2J.

We agree that it is helpful to specify in the figure (now revised figure 3C) that the voltage clamp recordings of somatodendritic calcium current were conducted in adult flight motoneurons and have revised the headline of figure panel 3C and the legend accordingly. Please note, these are not muscle cells but central neurons.

(7) Do dIS4B/Cav2null MNs indeed show an inward or outward current at -90 to -70 mV/-40 and -50 mV, or is this an analysis artifact?

No, this is due to baseline fluctuations as typical for voltage clamp in central neurons with more than 6000 µm dendritic length and more than 4000 dendritic branches.

(8) Loss of several presynaptic proteins, including Brp (Kittel et al., 2006), and RBP (Liu et al., 2011), induce changes in GluR field size (without apparent changes in miniature amplitude). The statement regarding the Cav2 isoform and possible effects on GluR number (p. 8) should be revised accordingly.

We understand and have done two things. First, we measured the intensity of GluRIIA immunolabel in ΔI-IIA, ΔI-IIB, and controls and found no differences. Second, we reworded the statement. It now reads on page 9, lines 1-6: “It seems unlikely that presynaptic cac channel isoform type affects glutamate receptor types or numbers, because the amplitude of spontaneous miniature postsynaptic currents (mEPSCs, Fig. 4K) and the labeling intensity of postsynaptic GluRIIA receptors are not significantly different between controls, I-IIA, and I-IIB junctions (see suppl. Fig. 2, p = 0.48, ordinary one-way ANOVA, mean and SD intensity values are 61.0 ± 6.9 (control), 55.8 ± 8.5 (∆I-IIA), 61.1 ± 17.3 (∆I-IIB)). However, we cannot exclude altered GluRIIB numbers and have not quantified GluR receptor field sizes.”

(9) The statement relating miniature frequency to RRP size is unclear (p. 8). Is there any evidence for a correlation between miniature frequency to RRP size? Could the authors please clarify?

We agree that this statement requires caution. Although there is some published evidence for a correlation of RRP size and mini frequency (Neuron, 2009 61(3):412-24. doi: 10.1016/j.neuron.2008.12.029 and Journal of Neuroscience 44 (18) e1253232024; doi: 10.1523/JNEUROSCI.1253-23.2024), which we now refer to on page 9, it is not clear whether this is true for all synapses and how linear such a relationship may be. Therefore, we have revised the text on page 9, lines 6-9. It now reads: “Similarly, the frequency of miniature postsynaptic currents (mEPSCs) remains unaltered. Since mEPSCs frequency has been related to RRP size at some synapses (Pan et al., 2009; Ralowicz et al., 2024) this indicates unaltered RRP size upon I-IIB excision, but we have not directly measured RRP size.”

(10) Please define the "strict top view" of synapses (p. 8).

Top view is what this reviewer referred to as “planar view” in the public review points 6 and 7. In our responses to these public review points we now also define “strict top view”, see page 9, lines 17-19.

(11) Two papers are cited regarding a linear relationship between calcium channel number and release probability (p. 15). Many more papers could be cited to demonstrate a supralinear relationship (e.g., Dodge & Rahaminoff, 1967; Weyhersmüller et al., 2011 doi: 10.1523/JNEUROSCI.6698-10.2011). The data of the present study were collected at an extracellular calcium concentration of 0.5 mM, whereas Meideiros et al. (2023) used 1.5 mM. The relationship between calcium and release is supra-linear around 0.5 mM extracellular calcium (Weyhersmüller et al. 2011). This should be discussed/the statements be revised. Also, the reference to Meideiros et al. (2023) should be included in the reference list.

We have now updated the Medeiros reference (updated version of that paper appeared in eLife in 2024) in the text and reference list. We agree that the relationship of the calcium concentration and P_r can also be non-linear and refer to this on page 16, lines 26-32, but the point we want to make is to relate defined changes in calcium channel number (not calcium influx) as assessed by multiple methods (CLSM intensity measures and sptPALM channel counting) to release probability. We now also clearly state that we measured at 0.5 mM external calcium (page 16, lines 27/28) whereas Medeiros et al. 2024 measured at 1.5 mM calcium (page 16, lines 31/32).

(12) Figure 6: Quantal content does not have any units - please remove "n vesicles".

We have revised this figure in response to reviewer 2 (comment 5) and quantal content is now expressed as percent baseline, thus without units (see revised figure 7).

(13) Figure 6C should be auto-scaled from zero.

This has been fixed by revising that figure in response to reviewer 2 (comment 5)

(14) The data supporting the statement on impaired motor behavior and reduced vitality of adult IS4A should be either shown, or the statement should be removed (p. 13). Any hypotheses as to why IS4A is important for behavior and or viability?

As suggested, we have removed that statement.

(15) They do not provide any data supporting the statement that changes in PSC decay kinetics "counteract" the increase in PSC amplitude (p. 14). The sentence should be changed accordingly.

We agree and have down toned. It now reads on page 16, lines 7-9: “During repetitive firing, the median increase of PSC amplitude by ~10 % is potentially counteracted by the significant decrease in PSC half amplitude width by ~25 %...”.

(16) How do they explain the net locomotion speed increase in dI    -IIA larvae? Although the overall charge transfer is not affected during the stimulus protocols used, could the accelerated PSC decay affect PSP summation (I would actually expect a decrease in summation/slower speed)? Independent of the voltage-clamp data, is muscle input resistance changed in dI-IIA mutants?

Muscle input resistance is not altered in I-II mutants. We refer to potential causes of the locomotion effects of I-IIA excision in the discussion. On page 16, lines 12 to 21 it reads: “there is no difference in charge transfer from the motoneuron axon terminal to the postsynaptic muscle cell between ∆I-IIA and control. Surprisingly, crawling is significantly affected by the removal of I-IIA, in that the animals show a significantly increased mean crawling speed but no significant change in the number of stops. Given that the presynaptic function at the NMJ is not strongly altered upon I-IIA excision, and that I-IIA likely mediates also Ca_v2 functions outside presynaptic AZs (see above) and in other neuron types than motoneurons, and that the muscle calcium current is mediated by Ca_v1>/i> and Ca_v3, the effects of I-IIA excision of increasing crawling speed is unlikely caused by altered pre- or postsynaptic function at the NMJ. We judge it more likely that excision of I-IIA has multiple effects on sensory and pre-motor processing, but identification of these functions is beyond the scope of this study.”

Author response:

Provisional Responses to Review #1's comments:

We thank the reviewer for the comments, which highlight both strengths and weaknesses.

We acknowledge that the optimized parameter values are somewhat specific to Plasmodium, as demographic and mutation/recombination rates can vary across species. However, we would like to emphasize that our simulation and benchmarking framework, along with associated tools like the efficient ibdutils, should be broadly applicable to many species, such as Apicomplexan parasites and other high-recombining eukaryotes, especially when their demographic and evolutionary parameters can be provided or estimated. We will update relevant paragraphs in the disucssion to highlight this point.

Results related to Refined IBD may not seem unexpected, but our work demonstrates that its direct application to malaria parasites without species-specific optimization can be suboptimal, as has previously occurred in malaria research with their validity not formally evaluated. We believe it is crucial for the research community focusing on non-standard model organisms to validate assumptions made in methods developed for standard models, such as humans, before they are applided to new species.

Although standard deviations (SDs) are not provided for many analyses, we argue that simulating 14 chromosomes independently serves as repeats (data were shown as means over chromosomes), particularly when assessing the accuracy of IBD segments or scanning for selection signals. For analyses that aggregate information across chromosomes, we are planning to conduct additional repeated simulations or analyses to quantify the uncertainty of estimates. In the upcoming revised version, we will provide SDs where appropriate and explanations when repeated simulation are not necessary given a large number of data points have well captured their empirical distributions.

Provisional response to review #2's comment:

Thank you to the reviewer for the suggestions. We agree with the comments, and addressing the mentioned weakness will improve the manuscript's clarity and impact. We plan to enhance the introduction by highlighting the significance of studying malaria and specifically focusing on P. falciparum in this work. We will also update the discussion to reinforce the connection between our findings and malaria research and control and further emphasize the broader implications for the field.

Author response:

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

(1) Reviewer 3: Moreover, the conclusion that preBötC NMBR and GRPR activations are unnecessary for sighing is not fully supported by the current experimental design. While the study shows that sighing can still be induced despite pharmacological inhibition of NMBR and GRPR, this does not conclusively prove that these receptors are not required under natural conditions. 

We concluded that “NMBR and GRPR receptors are not necessary for sigh generation”. We acknowledge that under normal conditions these receptors almost certainly play a role; in fact, microinjection of saporin conjugated to bombesin, which presumably ablates NMBR⁺ and GRPR⁺ preBötC neurons, completely eliminated endogenous sighing activity in awake mice (Li et al., Nature, 2015). However, that study did not establish that the receptors per se are essential in this context, since the protocol ablated not just the receptors but also the preBötC neurons that happened to express these receptors. Here, we show that we could evoke sighs AFTER complete pharmacological blockade of NMBRs and GRPRs. Also, we show that sighs can be elicited by stimulation of a distinct subpopulation of preBötC neurons expressing the peptide somatostatin (SST⁺). These results demonstrate that sighs can be evoked in absence of activation of NMBRs and/or GRPRs, leading to the conclusion that NMBRs and/or GRPRs are not required for sighs but rather contribute to periodic sigh generation under normal conditions.

(2) Reviewer 1: To make such a novel (and quite surprising) claim requires many more studies and the conclusion is dependent on how the authors have defined a sigh. Moreover, some data within the paper conflicts with this idea.

Our definition of sighs was carefully chosen so that it applied across different experimental conditions, including in vitro slices, anesthetized or awake in vivo. We defined sighs as transient changes in minute ventilation on a time scale slower than eupneic breathing period, to avoid classifying breathing after vagotomy or under isoflurane anesthesia as “all-sigh breathing”. This is why induction of persistent large amplitude breaths (such as in Figures 5-6) were not counted as sighs.

(3) Reviewer 2: Several key technical aspects of the study require further clarification to aid in interpreting the experimental results, including issues relating to the validation of the transgenic mouse lines and virally transduced expressions of proteins utilized for optogenetic and chemogenetic experiments, as well as justifying the optogenetic photostimulation paradigms used to evoke sighs.

The rationale for using SPP and LPP stems from our published observations of the effects of optogenetic stimulation of various preBötC neuronal subpopulations. Thus, SPP and LPP evoke the same responses in GlyT2 (Sherman et al., 2015) and Dbx1 (Cui et al., 2016) neurons, while for other subpopulations, e.g., SST (Cui et al., 2015), the effects of SPP are markedly different from LPP. Hence, in this study we examined both. As effects of SPP and LPP of SST neurons were examined previously (Cui et al., 2016), these protocols were not repeated except for evoking sighs after blockade of NMBR/GRPRs. SPP of pF NMB or GRP did not evoke any respiratory responses and hence were not presented in any figures (see Results, section “Activation of Nmb- or Grp-expressing pF neurons induces sighs”).

(4) Reviewer 3: however, the rationale and experimental details require further explanation, and their impacts on the conclusion require clarification. For instance, how and why the variability in optogenetic activation conditions could impact the experimental outcomes. 

Refractory periods reported here for pF NMB, pF GRP, preBötC NMBR and preBötC GRPR were all obtained using the same intensity LPP. We acknowledge the possibility, even the likelihood that higher intensity LPP would shorten refractory periods. In line with this, we observed that ectopic sighs were evoked earlier during the LPP as the sigh phase progressed. As described in RESULTS, such effects were observed for pF NMB, pF GRP, preBötC NMBR and preBötC GRPR only and not for preBötC SST, which might suggest that timing of intrinsically generated sighs depends on the NMB-GRP signaling pathway, yet sigh production depends on the SST pathway.

Author response:

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

Reviewer #1 (Public Review):

This is an elegant didactic exposition showing how dendritic plateau potentials can enable neurons to perform reliable 'binary' computations in the face of realistic spike time jitter in cortical networks. The authors make many good arguments, and the general concept underlying the paper is sound. A strength is their systematic progression from biophiysical to simplified models of single neurons, and their parallel investigation of spiking and binary neural networks, with training happening in the binary neural network.

Reviewer #2 (Public Review):

Summary:

Artificial intelligence (AI) could be useful in some applications and could help humankind. Some forms of AI work on the platform of artificial neural networks (ANN). ANNs are inspired by real brains and real neurons. Therefore understanding the repertoire and logic of real neurons could potentially improve AANs. Cell bodies of real neurons, and axons of real neurons, fire nerve impulses (nerve impulses are very brief ~2 ms, and very tall ~100 mV). Dendrites, which comprise ~80% of the total neuronal membrane (80% of the total neuronal apparatus) typically generate smaller (~50 mV amplitude) but much longer (~100 ms duration) electrical transients, called glutamate-mediated dendritic plateau potentials. The authors have built artificial neurons capable of generating such dendritic plateau potentials, and through computer simulations the authors concluded that long-lasting dendritic signals

(plateau potentials) reduce negative impact of temporal jitter occurring in real brain, or in

AANs. The authors showed that in AANs equipped with neurons whose dendrites are capable of generating local dendritic plateau potentials, the sparse, yet reliable spiking computations may not require precisely synchronized inputs. That means, the real world can impose notable fluctuations in the network activity and yet neurons could still recognize and pair the related network events. In the AANs equipped with dendritic plateaus, the computations are very robust even when inputs are only partially synchronized. In summary, dendritic plateau potentials endow neurons with ability to hold information longer and connect two events which did not happen at the same moment of time. Dendritic plateaus circumvent the negative impact, which the short membrane time constants arduously inflict on the action potential generation (in both real neurons and model neurons). Interestingly, one of the indirect conclusions of the current study is that neurons equipped with dendritic plateau potentials may reduce the total number of cells (nodes, units) required to perform robust computations.

Strengths:

The majority of published studies are descriptive in nature. Researchers report what they see or measure. A smaller number of studies embark on a more difficult task, which is to explain the logic and rationale of a particular natural design. The current study falls into that second category. The authors first recognize that conduction delays and noise make asynchrony unavoidable in communication between circuits in the real brain. This poses a fundamental problem for the integration of related inputs in real (noisy) world. Neurons with short membrane time constants can only integrate coincident inputs that arrive simultaneously within 2-3 ms of one another. Then the authors considered the role for dendritic plateau potentials. Glutamate-mediated depolarization events within individual dendritic branches, can remedy the situation by widening the integration time window of neurons. In summary, the authors recognized that one important feature of neurons, their dendrites, are built-in to solve the major problems of rapid signal processing: [1] temporal jitter, [2] variation, [3] stochasticity, and [4] reliability of computation. In one word, the dendritic plateau potentials have evolved in the central nervous systems to make rapid CNS computations robust.

Weaknesses:

The authors made some unsupported statements, which should either be deleted, or thoroughly defended in the manuscript. But first of all, the authors failed to bring this study to the readers who are not experts in computational modeling or Artificial Neural Networks. Critical terms (syntax) and ideas have not been explained. For example: [1] binary feature space? [2] 13 dimensions binary vectors? [3] the binary network could still cope with the loss of information due to the binarization of the continuous coordinates? [4] accurate summation?

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

However, I have a number of specific points, listed below, that should be addressed. Most of them are relatively minor, but the authors should especially address point 10, which is a major point, by redoing the simulations affected by the erroneous value of the time constant, and by remaking the relevant figures based on the new simulations.

Specific comments:

(1) 7f "This feature is conspicuous because it is an order of magnitude longer than unitary synaptic inputs and axonal spikes.": — It is an order of magnitude longer than AMPA receptor-mediated synaptic currents (EPSCs), but more similar in time course to synaptic potentials (EPSPs) whose decay is governed by the passive membrane time constant (about 10 to 20 ms in pyramidal neurons in vivo) and which determines the lifetime of the 'memory' of the neuron for synaptic inputs under conditions of subthreshold, non-spiking dendritic integration. The quoted sentence should be rewritten accordingly.

Following this suggestion, we have rewritten the sentence (l. 7) to: "This timescale is conspicuous, being many times longer than the fastest signalling processes in the nervous systems, including Excitatory Post-Synaptic Potentials (EPSPs) and axonal spikes."

(2) 16ff "This is especially relevant to integration of inputs during high conductance states that are prevalent in-vivo. In these states the effective time constant of the neuronal membrane is extremely short and varies substantially depending on synaptic drive [13, 34, 49].": — The time-averaged synaptic conductance driven by sensory input in vivo is much less high than implied by this statement (e.g. see Fig. 4 of Haider et al. 2013 https://www.nature.com/articles/nature11665 ), and reduces the passive membrane time constant only by a small percentage. The energy cost of a high prevalence of highconductance states and extremely short membrane time constants would also exceed the energy budget of the brain (ref. 4). I would therefore suggest dropping this sentence.

We have clarified this sentence thanks to the reviewer's suggestion. We meant that the instantaneous, rather than the time-averaged, conductance can be very big. To clarify this we have rewritten this section (l. 15): This is especially relevant to integration of inputs during high conductance states that are prevalent in vivo, where a typical neuron receives significant synaptic drive. In these states, the effective membrane time constant can be extremely short, and varies substantially depending on synaptic input.

(3) l. 17f "As a consequence, computations that rely on passive summation of multiple inputs place punishing constraints on spike timing precision.": — Again, the passive membrane time constant is on the order of 10 ms and I would tone down this statement accordingly, removing the word 'punishing' for example.

Following the suggestion, we have rewritten the sentence to (l. 18): "As a consequence, computations that rely on passive summation of multiple inputs would place strong constraints on spike timing precision."

(4) l. 18ff "Dendritic action potentials, by contrast, have a consistently long duration that is ensured by the kinetic properties of voltage gated ion channels and NMDA receptors [54, 47, 10, 3]. These properties are largely determined by the amino acid sequence of receptor and channel proteins that are specifically expressed in dendrites [45, 44, 40]. This suggests dendritic properties are specifically tuned to produce localised, suprathreshold events that outlive rapid membrane fluctuations.": — Yes, but see also Attwell & Gibb 2005 ( https://www.nature.com/articles/nrn1784 ), especially the last two of their key points. The slow NMDA receptor decay kinetics (and therefore their high affinity for binding glutamate) may also be the consequence of a design goal to set the temporal coherence window for NMDA receptor-mediated synaptic plasticity such as STDP to be on the order of tens of milliseconds, somewhat longer than the membrane time constant.

The reviewer is correct; other functions (e.g. synaptic plasticity) are also part of the dendrite's repertoire. To acknowledge this, we added a section (l. 34) where we mention that our idea does not conflict with, for example, synaptic plasticity.

(5) l. 32f "Numerous studies point out that nonlinear summation in dendrites can make neurons computationally equivalent to entire networks of simplified point models, or 'units' in a traditional neural network [9, 21, 38, 40, 45, 48, 50, 51].": — See also Beniaguev et al. 2021 ( https://www.cell.com/neuron/pdf/S0896-6273(21)00501-8.pdf ), which also speaks to the next sentence.

We thank the reviewer for the suggestion; the citation has been added.

(6) Fig. 2E and F: the top of panel F corresponds to the top of panel E, but the bottom ofpanel F does not correspond to the bottom of panel E - it corresponds to a dendritic neuron with passive dendrites, not a point neuron. Panel E should be changed to reflect this fact.

We have followed the suggestion to change the figure.

(7) l. 49f "Despite these dendritic spikes being initiated at different times, they still sum in the soma, leading to a sodium spike there (Figure 2E).": — You probably mean Fig. 2D, and instead of a sodium spike (which could be misunderstood as local and dendritic) you triggered a sodium action potential. Likewise, Fig. 2B (right) shows the timescale of sodium action potentials at the soma (cf. l. 46).

The error in the referencing to the figure has been corrected. The phrasing has also been changed to "a sodium action potential" (l. 56), following the reviewer's suggestion.

(8) Please check the scale bars in Fig. 2D. Do they also apply to panel F below? If yes thatshould be stated.

The scale bars are indeed the same; I have repeated them in the figure to avoid any confusion.

(9) l. 68 "This time constant is consistent with the high-conductance state of pyramidalneurons in the cortex [6]":

You do not need to invoke a high-conductance state to justify this time constant, which is indeed typical for the membrane time constant of pyramidal neurons in vivo.

On a related note, Fig. 3B and its legend seem to assume that tau = 1 ms, and calls that one EPSP duration in the legend. An EPSC may have a decay time constant of 1 ms, but an EPSP will have a decay time constant of about 10 ms, similar to the membrane time constant. Fig. 3B (and therefore also the rest of Figure 3) seems to have been constructed with a value of tau that is too small by a factor of 10, and this should be corrected by remaking the figure. If tau = 1 ms was used also in Figure 4 then this figure also needs to be remade.

Section 3.3 and Table 1 also use tau = 1 ms. This is unrealistic and needs to be changed an appropriate value of tau = 10 ms is given by the authors themselves in line 67. The incorrect value of tau in Table 1 causes other entries of the Table to be terribly wrong; a leak conductance of 1 µS would imply an input resistance of the neuron of 1 MOhm, but somatic input resistances of pyramidal neurons in vivo are on the order of 20 to 50 MOhm. The total capacitance of 1 nF is slightly too large, and should be adjusted to yield a membrane time constant of 10 ms given an appropriate leak conductance leading to an input resistance of about 20 to 50 MOhm. These are key numbers to get right for both Figures 3 and 4, especially if you want to be able to say "We have been careful to respect the essence of basic physiological facts while trying to build an abstraction of how elementary spiking computations might occur." (l. 215f).

We thank the reviewer for catching this. We had actually already used tau = 10 ms, but had not yet updated the paper. Moreover, the somatic input resistance was indeed off. To rectify this, we have used the values: $Cm = 0.5 nF$, $\taum = 10 ms$, $Rm = 20 M \Ohm$, $gl = 0.05 \mu S$. Figure 3 was remade using these values, and Table 1 updated accordingly.

(10) l. 158ff "The assumption that each neuron connects to one dendrite of an upstream neuron is actually grounded in physiology, although it may appear like a strong assumption at first glance: related inputs arrive at local clusters of spines synchronously [60].": — You probably mean "each neuron connects to one dendrite of a downstream neuron." And I would add "But see Beniaguev et al. 2022 https://www.biorxiv.org/content/10.1101/2022.01.28.478132v2.abstract " - your restrictive arrangement of inputs is probably not really needed, especially if postsynaptic neurons have more dendrites.

The suggested wording was correct, and has been now incorporated (l. 166). I have also added the suggested citation.

(11) I note that the plateaus in Fig. 4D are much shorter than those in Fig. 2D and F, but thisis a good thing: The experimental and simulation results in Fig. 2 are based on ref. 18, which used microiontophoresis of glutamate, leading to much slower glutamate concentration time courses at the dendritic NMDA receptors than synaptic release of glutamate would. The time courses of plateaus in Fig. 4 are much more in line with the NMDA plateau durations shown in ref. 21, especially their Figure 2B. These faster NMDA plateaus (or NMDA spikes as they are called in ref. 21) are based on synaptic release of glutamate in vivo, and on the faster NMDA receptor kinetics at physiological temperature compared to the old models with room temperature kinetics used in ref. 18.

Here are two additional references that the authors might find interesting:

Fisek et al. 2023 https://www.nature.com/articles/s41586-023-06007-6 Dudai et al. 2022 https://www.jneurosci.org/content/42/7/1184.full

We thank the reviewer for the suggested references. The first has been added to the references in the introduction, on l. 28. The second has been added on l. 78.

Reviewer #2 (Recommendations For The Authors):

(1) In Fig. 3A, we observed some animal pictures, which were never explained in the figurecaption, or text of the manuscript. These pictures were probably explained at the lab meeting, so it is unnecessary to waste effort on these pictures in the manuscript draft.

We agree with the reviewer; the figures have been removed.

(2) Figure 1 has not been referenced anywhere in the manuscript text!

Indeed, this had to be corrected, figure is now references on l. 9.

(3) Line 45. "[18] triggered two NMDA spikes by glutamate uncaging at the indicated (red,blue) sites". [18] triggered one NMDA spike while recording at three locations simultaneously (two locations in dendrite and one location in the soma).

The reviewer is correct here. The sentence has now been rephrased to "(ref.) triggered an NMDA spike by glutamate microiontophoresis while recording at the soma and the indicated (red, blue) sites in the dendrite." (l. 49)

(4) Fig. 2B. The two labels, "Dendrite 2" and "Dendrite 1" incorrectly suggest that two traceswere recorded in two dendrites. These two traces were recorded in the same dendrite.

We agree with the reviewer; labels have now been changed to "Dendrite site".

(5) Line 45. "[18] triggered two NMDA spikes by glutamate uncaging at the indicated (red,blue) sites". - - One NMDA spike by "glutamate microiontophoresis".

This is correct, the phrasing on (l. 50) has been changed accordingly.

(6) Line 47. "... simulated glutamate releases 50 ms apart in the three dendritic sites indicatedin Figure 2C, thereby triggering three NMDA spikes at those sites. Despite these dendritic spikes being initiated at different times, they still sum in the soma, leading to a sodium spike there (Figure 2E)". A similar experiment has been performed in real cortical neurons (KD Oikonomu et al., 2012, PMID: 22934081), and could potentially be cited here. Briefly, Oikonomou et al. generated two dendritic plateau potentials in two dendritic branches and monitored the summation of these dendritic plateau potentials in the cell body.

The reference has been added, on l. 54

(7) Line 63. "We compared the behaviour of our simplified model with that of the full, detailedbiophysical model". Which detailed biophysical model? Please cite here the detailed biophysical model that you used for comparisons with your simplified abstract model.

The reference to the paper has been added.

(8) Line 65. "Figure 2F shows that spikes arriving at different times are summed in anintegrate and hold-like manner". In Fig. 2F, I am unable to see that spikes arriving at different times are summed in an integrate and hold-like manner. Which feature of Fig. 2F refers to the "hold-like manner"? Please explain in the manuscript.

To clarify we have added "Figure 2F, top" in the text (l. 71).

(9) Figure 2 caption. "(F) The voltage traces of the abstract model, with and without plateaus.Because of the extended time duration of the plateau potentials, they sum accurately to produce a somatic spike". I am unable to understand what an "accurate summation" in Fig. 2 is. Could the authors provide an illustrative example of a situation in which the neuronal potentials DID NOT sum accurately?

To address this confusion, we have changed the wording to "...they are summed to reach threshold."

(10) Line 75. "This is an important issue we intend to return to in future work". The authorspersonal plans should not be in the text discussing scientific results.

We believe it is entirely reasonable to discuss scientific plans that are part of ongoing work, and this is quite common throughout the literature. Nonetheless, we have now reworded this to "This is an important issue for future work." (l. 81)

(11) In Fig. 4F, the full-line and the dashed-line have not been identified! The readers are leftto guess.

This has now been addressed both with text inserts in the figure, and specification in the figure caption.

(12) Line 247. "would amount to scaling up the number of cells in a network to performcomputations that could, in principle, be performed by more robust single units". Did the authors mean to say: "would amount to scaling up the number of cells in a network to perform computations that could, in principle, be performed by a fewer (but more robust) single units"?

We have replaced the sentence with the reviewer's suggestion (l. 259)

(13) In the abstract, the authors repeat sentences: "the timescale of dendritic potentialsallows reliable integration of asynchronous inputs" and "nonlinear dendritic plateau potentials allow reliable integration of asynchronous spikes". Besides this being a bad writing style, the authors cannot decide if inputs to the model neuron are asynchronous, or spiking of the model neuron is asynchronous. Are these asynchronous spikes occurring in the neuron experiencing dendritic plateau potentials, or these asynchronous spikes occur in the neuronal network? This confusion of terms and ideas must be removed from the abstract.

We have rewritten the second sentence, which now reads: "Using this model, we show that long-lived, nonlinear dendritic plateau potentials allow neurons to spike reliably when confronted with asynchronous input spikes."

(14) In the abstract, the authors claim: "Our results provide empirically testable hypothesesfor the role of dendritic action potentials in cortical function". With great anticipation, I read throughout the manuscript, but I was unable to find one single experimental design that could support the authors' bald statement. In the text of the manuscript, the authors must carefully reveal the precise experimental outline that would test their specific hypothesis, or delete the untrue statement.

We respectfully challenge the rather critical tone of the reviewer. The central hypothesis that plateaus enable robust summation, and that circuit level computations rely on this is an experimentally testable hypothesis. The precise experimental design of how to test such a hypothesis is always best left to an experimentalist to determine, as there are many possible means of doing this and each will depend on the preparation and methodology at hand. At the same time, we understand that there is an increasing culture of expecting explicit "testable hypotheses" spelled out to the reader. To satisfy this expectation while avoiding overly prescriptive ideas for how future work should proceed, we have now added more explicit descriptions of possible experimental tests in l. 231 and onwards.

(15) Fig. 2F was submitted for review without a time scale, while at the same time the authorsheavily discuss specific numerical values for time intervals. Namely, the authors instruct readers to pay attention to a 10 ms time constant and 2-3 ms input decay (Fig. 2F), but they do not show the time scale in Fig. 2F.

"We compared this to a situation where all inputs arrive at a soma with standard LIF dynamics and a 10 ms membrane time constant. This time constant is consistent with the high-conductance state of pyramidal neurons in the cortex [6]: Inputs decay after 2-3 ms, and fail to sum to spike threshold (Figure 2F, lower)".

The time (and voltage) bars have now been added to Fig. 2F.

(16) Line 75. "In the scope of what remains here we want to ask if integrate-and-hold isminimally feasible". This reviewer is unable to understand the meaning of the syntaxes "integrate-and-hold" and "minimally feasible" in the context of dendritic integration. This reviewer is worried that the majority of the journal readers would feel exactly the same. To alleviate this problem, the authors should explain both terms right here, in line 77.

Integrate-and-hold is defined on line 57 (to be exact we write: "We refer to this behavior as “Leaky Integrate-and-Hold” (LIH)." To be more clear we could reuse the acronym LIH here, to emphasise that we are referring to the same thing. By 'minimally feasible' we mean biologically plausible given assumptions that are not strong. Can use another term, e.g. "biologically plausible under lenient assumptions".

To address this point, we have rephrased the sentence as "In the scope of what remains here we want to ask if Leaky-Integrate-and-Hold (LIH) can easily and plausibly facilitate network computations with spikes." (l. 81), repeating the LIH definition.

(17) Line 91. "Spikes arriving even slightly out of sync with each other introduces noise in themembrane potential ..." Introduce.

The sentence has been fixed using the reviewer's correction.

(18) The caption of the Fig. 3B was submitted for review without any explanation of thenormalization procedure used. Also, in the caption of the same figure, one cannot find explanation of the light-gray area surrounding the black curves. Also, the readers are left to wonder how the results of a simulation could possibly be greater than 1 in some simulation trials.

We have added a description of the normalization and the shaded area to the caption of Fig. 3B.

(19) Line 117. "We assumed that inputs to a network arrive at the dendrites within some timewindow, and their combined depolarisations are either sufficient to either elicit a dendritic spike or not, as shown in Figure 3". We could potentially compact the current text by deleting one instance of "either".

We agree this is better writing; one of the occurrences of 'either' has been removed.

(20) Line 127. "where incoming connections can be represented with a 1 (a spike arrives)..."Did you mean "a presynaptic spike arrives"?

The sentence has been rewritten following the suggestion.

(21) Line 134. "with each unit only having ..." Dendrite can be a unit. Dendritic spine can be aunit. Did you mean "with each unit (i.e. neuron) having ..."

We have incorporated the suggestion.

(22) Fig. 4, Caption. "Each point is a 2D input vector x, the colors represent the differentclasses". An effort was made to introduce 3 different classes. But then, no mention of "classes" thereafter. The three input vectors, mentioned in Line 170, perhaps represent the remnants of the class concept mentioned in the previous paragraph.

We have now rewritten the sentence beginning with "These three input vectors ..." on l. 182 to emphasise that a correct answer means a correct classification.

(23) Line 152. "The 2D input points were first projected onto a binary feature space, to obtain13D binary vectors". Did you mean to say: "The 2D input points (three classes, Fig. A) were first projected onto a binary feature space, to obtain three binary vectors; each 13D binary vector responding to a specific class".

The sentence has been replaced with the reviewer's suggestion (l. 159).

(24) Line 163. "Because our focus is to account for how transient signals can be summed andthresholded robustly, we are assuming that inhibition is implicitly accounted for in the lumped abstraction". Could you please explain your two ideas: [1] "inhibition is implicitly accounted for" and [2] "lumped abstraction", because this reviewer did not get neither idea.

The reviewer is right that as it stood, the sentence was unclear. To clarify the point we have decided to expand upon that sentence and break it out as an individual paragraph (starting l. 171).

Author response:

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

Reviewer 1:

This study is one in a series of excellent papers by the Forstmann group focusing on the ability of fMRI to reliably detect activity in small subcortical nuclei - in this case, specifically those purportedly involved in the hyper- and indirect inhibitory basal ganglia pathways. I have been very fond of this work for a long time, beginning with the demonstration of De Hollander, Forstmann et al. (HBM 2017) of the fact that 3T fMRI imaging (as well as many 7T imaging sequences) do not afford sufficient signal to noise ratio to reliably image these small subcortical nuclei. This work has done a lot to reshape my view of seminal past studies of subcortical activity during inhibitory control, including some that have several thousand citations.

Comments on revised version:

This is my second review of this article, now entitled "Multi-study fMRI outlooks on subcortical BOLD responses in the stop-signal paradigm" by Isherwood and colleagues.

The authors have been very responsive to the initial round of reviews.

I still think it would be helpful to see a combined investigation of the available 7T data, just to really drive the point home that even with the best parameters and a multi-study sample size, fMRI cannot detect any increases in BOLD activity on successful stop compared to go trials. However, I agree with the authors that these "sub samples still lack the temporal resolution seemingly required for looking at the processes in the SST." As such, I don't have any more feedback.

We thank the reviewer for their positive feedback, and for their thorough and constructive comments on our initial submission. 

Reviewer 2:

This work aggregates data across 5 openly available stopping studies (3 at 7 tesla and 2 at 3 tesla) to evaluate activity patterns across the common contrasts of Failed Stop (FS) > Go, FS > stop success (SS), and SS > Go. Previous work has implicated a set of regions that tend to be positively active in one or more of these contrasts, including the bilateral inferior frontal gyrus, preSMA, and multiple basal ganglia structures. However, the authors argue that upon closer examination, many previous papers have not found subcortical structures to be more active on SS than FS trials, bringing into question whether they play an essential role in (successful) inhibition. In order to evaluate this with more data and power, the authors aggregate across five datasets and find many areas that are *more* active for FS than SS, including bilateral preSMA, GPE, thalamus, and VTA. They argue that this brings into question the role of these areas in inhibition, based upon the assumption that areas involved in inhibition should be more active on successful stop than failed stop trials, not the opposite as they observed.

Since the initial submission, the authors have improved their theoretical synthesis and changed their SSRT calculation method to the more appropriate integration method with replacement for go omissions. They have also done a better job of explaining how these fMRI results situate within the broader response inhibition literature including work using other neuroscience methods.

They have also included a new Bayes Factor analysis. In the process of evaluating this new analysis, I recognized the following comments that I believe justify additional analyses and discussion:

First, if I understand the author's pipeline, for the ROI analyses it is not appropriate to run FSL's FILM method on the data that were generated by repeating the same time series across all voxels of an ROI. FSL's FILM uses neighboring voxels in parts of the estimation to stabilize temporal correlation and variance estimates and was intended and evaluated for use on voxelwise data. Instead, I believe it would be more appropriate to average the level 1 contrast estimates over the voxels of each ROI to serve as the dependent variables in the ROI analysis.

We agree with the reviewer’s assertion that this approach could create estimation problems. However, in this instance, we turned off the spatial smoothing procedure that FSL’s FILM normally uses for estimating the amount of autocorrelation – thus, the autocorrelation was estimated based on each voxel’s timeseries individually. We also confirmed that all voxels within each ROI had identical statistics, which would not be the case if the autocorrelation estimates differed per voxel. We have added the following text to the Methods section under fMRI analysis: ROI-wise:

Note that the standard implementation of FSL FILM uses a spatial smoothing procedure prior to estimating temporal autocorrelations which is suitable for use only on voxelwise data (Woolrich et al., 2001). We therefore turned this spatial smoothing procedure off and instead estimated autocorrelation using each voxel’s individual timeseries.

Second, for the group-level ROI analyses there seems to be inconsistencies when comparing the z-statistics (Figure 3) to the Bayes Factors (Figure 4) in that very similar zstatistics have very different Bayes Factors within the same contrast across different brain areas, which seemed surprising (e.g., a z of 6.64 has a BF of .858 while another with a z of 6.76 has a BF of 3.18). The authors do briefly discuss some instances in the frequentist and Bayesian results differ, but they do not ever explain by similar z-stats yield very different bayes factors for a given contrast across different brain areas. I believe a discussion of this would be useful.

We thank the reviewer for their keen observation, and agree that this is indeed a strange inconsistency. Upon reviewing this issue, we came across an error in our analysis pipeline, which led to inconsistent scaling of the parameter estimates between datasets. We corrected this error, and included new tables (Figures 3, 4, and Supplementary Figure 5) which now show improved correspondence between the frequentist results from FSL and the Bayesian results.

We have updated the text of the Results section accordingly. In this revision, we have also updated all BFs to be expressed in log₁₀ form, to ensure consistency for the reader. Updates to the manuscript are given below.

Results: Behavioural Analyses:

Consistent with the assumptions of the standard horse-race model (Logan & Cowan, 1984), the median failed stop RT is significantly faster within all datasets than the median go RT (Aron_3T: p < .001, BF_log10 = 2.77; Poldrack_3T: p < .001, BF_log10 = 23.49; deHollander_7T: p < .001, B BF_log10 = 8.88; Isherwood_7T: p < .001, BF_log10 = 2.95; Miletic_7T: p = .0019, BF_log10 = 1.35). Mean SSRTs were calculated using the integration method and are all within normal range across the datasets.

Results: ROI-wise GLMS: 

To further statistically compare the functional results between datasets, we then fit a set of GLMs using the canonical HRF with a temporal derivative to the timeseries extracted from each ROI. Below we show the results of the group-level ROI analyses over all datasets using z-scores (Fig. 3) and log-transformed Bayes Factors (BF; Fig. 4). Note that these values were time-locked to the onset of the go signal. See Supplementary Figure 5 for analyses where the FS and SS trials were time-locked to the onset of the stop signal. To account for multiple comparisons, threshold values were set using the FDR method for the frequentist analyses. 

For the FS > GO contrast, the frequentist analysis found significant positive z-scores in all regions bar left and right M1, and the left GPi. The right M1 showed a significant negative z-score; left M1 and GPi showed no significant effect in this contrast. The BFs showed moderate or greater evidence for the alternative hypothesis in bilateral IFG, preSMA, caudate, STN, Tha, and VTA, and right GPe. Bilateral M1 and left GPi showed moderate evidence for the null. Evidence for other ROIs was anecdotal (see Fig 4). 

For the FS > SS contrast, we found significant positive z-scores in in all regions except the left GPi. The BFs showed moderate or greater evidence for right IFG, right GPi, and bilateral M1, preSMA, Tha, and VTA, and moderate evidence for the null in left GPi. Evidence for other ROIs was anecdotal (see Fig 4). 

For the SS > GO contrast we found a significant positive z-scores in bilateral IFG, right Tha, and right VTA, and significant negative z-scores in bilateral M1, left GPe, right GPi, and bilateral putamen. The BFs showed moderate or greater evidence for the alternative hypothesis in bilateral M1 and right IFG, and moderate or greater evidence for the null in left preSMA, bilateral caudate, bilateral GPe, left GPi, bilateral putamen, and bilateral SN. Evidence for other ROIs was anecdotal (see Fig 4). 

Although the frequentist and Bayesian analyses are mostly in line with one another, there were also some differences, particularly in the contrasts with FS. In the FS > GO contrast, the interpretation of the GPi, GPe, putamen, and SN differ. The frequentist models suggests significantly increased activation for these regions (except left GPi) in FS trials. In the Bayesian model, this evidence was found to be anecdotal in the SN and right GPi, and moderate in the right GPe, while finding anecdotal or moderate evidence for the null hypothesis in the left GPe, left GPi, and putamen. For the FS > SS contrast, the frequentist analysis showed significant activation in all regions except for the left GPi, whereas the Bayesian analysis found this evidence to be only anecdotal, or in favour of the null for a large number of regions (see Fig 4 for details).  

Since the Bayes Factor analysis appears to be based on repeated measures ANOVA and the z-statistics are from Flame1+2, the BayesFactor analysis model does not pair with the frequentist analysis model very cleanly. To facilitate comparison, I would recommend that the same repeated measures ANOVA model should be used in both cases. My reading of the literature is that there is no need to be concerned about any benefits of using Flame being lost, since heteroscedasticity does not impact type I errors and will only potentially impact power.

We agree with the reviewer that there are differences between the two analyses. The advantage of the z-statistics from FSL’s flame 1+2 is that these are based on a multi-level model in which measurement error in the first level (i.e., subject level) is taken into account in the group-level analysis. This is an advantage especially in the current paper since the datasets differ strongly in the degree of measurement error, both due to the differences in field strength and in the number of trials (and volumes). Although multilevel Bayesian approaches exist, none (except by use of custom code) allow for convolution with the HRF of a design matrix like typical MRI analyses. Thus, we extracted the participant-level parameter estimates (converted to percent signal change), and only estimated the dataset and group level parameters with the BayesFactor package. As such, this approach effectively ignores measurement error. However, despite these differences in the analyses, the general conclusions from the Bayesian and frequentist analyses are very aligned after we corrected for the error described above. The Bayesian results are more conservative, which can be explained by the unfiltered participantlevel measurement error increasing the uncertainty of the group-level parameter estimates. At worst, the BFs represent the lower bounds of the true effect, and are thus safe to interpret. 

We have also included an additional figure (Supplementary Figure 7) that shows the correspondence between the BFs and the z scores. 

Though frequentist statistics suggest that many basal ganglia structures are significantly more active in the FS > SS contrast (see 2nd row of Figure 3), the Bayesian analyses are much more equivocal, with no basal ganglia areas showing Log10BF > 1 (which would be indicative of strong evidence). The authors suggest that "the frequentist and Bayesian analyses are monst in line with one another", but in my view, this frequentist vs. Bayesian analysis for the FS > SS contrast seems to suggest substantially different conclusions. More specifically, the frequentist analyses suggest greater activity in FS than SS in most basal ganglia ROIs (all but 2), but the Bayesian analysis did not find *any* basal ganglia ROIs with strong evidence for the alternative hypothesis (or a difference), and several with more evidence for the null than the alternative hypothesis. This difference between the frequentist and Bayesian analyses seems to warrant discussion, but unless I overlooked it, the Bayesian analyses are not mentioned in the Discussion at all. In my view, the frequentist analyses are treated as the results, and the Bayesian analyses were largely ignored.

The original manuscript only used frequentist statistics to assess the results, and then added Bayesian analyses later in response to a reviewer comment. We agree that the revised discussion did not consider the Bayesian results in enough detail, and have updated the manuscript throughout to more thoroughly incorporate the Bayesian analyses and improve overall readability. 

In the Methods section, we have updated the fMRI analysis – general linear models (GLMs): ROIwise GLMs section to more thoroughly incorporate the Bayesian analyses as follows: 

We compared the full model (H1) comprising trial type, dataset and subject as predictors to the null model (H0) comprising only the dataset and subject as predictor. Datasets and subjects were modeled as random factors in both cases. Since effect sizes in fMRI analyses are typically small, we set the scaling parameter on the effect size prior for fixed effects to 0.25, instead of the default of 0.5, which assumes medium effect sizes (note that the same qualitative conclusions would be reached with the default prior setting; Rouder et al., 2009). We divided the resultant BFs from the full model by the null model to provide evidence for or against a difference in beta weights for each trial type. To interpret the BFs, we used a modified version of Jeffreys’ scale (Andraszewicz et al., 2014; Jeffreys, 1939). To facilitate interpretation of the BFs, we converted them to the logarithmic scale. The approximate conversion between the interpretation of logarithmic BFs and standard interpretation on the adjusted Jeffreys’ scale can be found in Table 3.   

The Bayesian results are also more incorporated into the Discussion as follows: 

Evidence for the role of the basal ganglia in response inhibition comes from a multitude of studies citing significant activation of either the SN, STN or GPe during successful inhibition trials (Aron, 2007; Aron & Poldrack, 2006; Mallet et al., 2016; Nambu et al., 2002; Zhang & Iwaki, 2019). Here, we re-examined activation patterns in the subcortex across five different datasets, identifying differences in regional activation using both frequentist and Bayesian approaches. Broadly, the frequentist approach found significant differences between most ROIs in FS>GO and FS>SS contrasts, and limited differences in the SS>GO contrast. The Bayesian results were more conservative; while many of the ROIs showed moderate or strong evidence, some with small but significant z scores were considered only anecdotal by the Bayesian analysis. In our discussion, where the findings between analytical approaches differ, we focus mainly on the more conservative Bayesian analysis.

Here, our multi-study results found limited evidence that the canonical inhibition pathways (the indirect and hyperdirect pathways) are recruited during successful response inhibition in the SST. We expected to find increased activation in the nodes of the indirect pathway (e.g., the preSMA, GPe, STN, SN, GPi, and thalamus) during successful stop compared to go or failed stop trials. We found strong evidence for activation pattern differences in the preSMA, thalamus, and right GPi between the two stop types (failed and successful), and limited evidence, or evidence in favour of the null hypothesis, in the other regions, such as the GPe, STN, and SN. However, we did find recruitment of subcortical nodes (VTA, thalamus, STN, and caudate), as well as preSMA and IFG activation during failed stop trials. We suggest that these results indicate that failing to inhibit one’s action is a larger driver of the utilisation of these nodes than action cancellation itself. 

These results are in contention to many previous fMRI studies of the stop signal task as well as research using other measurement techniques such as local field potential recordings, direct subcortical stimulation, and animal studies, where activation of particularly the STN has consistently been observed (Alegre et al., 2013b; Aron & Poldrack, 2006; Benis et al., 2014; Fischer et al., 2017; Mancini et al., 2019; Wessel et al., 2016).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study analyzed biomarker data from 28 subjects with geographic atrophy (GA) in a Phase I/II clinical trial of PPY988, a subretinal AAV2 complement factor I (CFI) gene therapy, to evaluate pharmacokinetics and pharmacodynamics. Post-treatment, a 2-fold increase in the vitreous humor (VH) FI was observed, correlating with a reduction in FB breakdown product Ba but minimal changes in other complement factors. The aqueous humor (AH) was found to be an unreliable proxy for VH in assessing complement activation. In vitro assays showed that the increase in FI had a minor effect on the complement amplification loop compared to the more potent C3 inhibitor pegcetacoplan. These findings suggest that PPY988 may not provide enough FI protein to effectively modulate complement activation and slow GA progression, highlighting the need for a thorough biomarker review to determine optimal dosing in future studies.

Strengths:

This manuscript provides critical data on the efficacy of gene therapy for the eye, specifically introducing complement FI expression. It presents the results from a halted clinical trial, making sharing this data essential for understanding the outcomes of this gene therapy approach. The findings offer valuable insights and lessons for future gene therapy attempts in similar contexts.

Weaknesses:

No particular weaknesses. The study was carefully performed and limitations are discussed.

I have just some concerns about the methodology used. The authors use the MILLIPLEX assays, which allow for multiplexed detection of complement proteins and they mention extensive validation. How are the measurements with this assay correlating with gold standard methods? Is the specificity and the expected normal ranges preserved with this assay? This also stands for the Olink assay. Some of the proteins are measured by both assay and/or by standard ELISA. How do these measurements correlate?

The authors thank the reviewer for the positive response. Regarding the ELISA assays used to measure the array of complement proteins described, these were extensively validated for the following parameters: specificity, intra-assay and inter-assay precision, accuracy, stability, reference range, and parallelism. All assays were validated in plasma, vitreous and aqueous humour. Due to the limited volume and availability of ocular fluids from individuals in the study, validation in vitreous and aqueous matrices was performed using a pool of several samples from post-mortem donors. At the time this study was initiated, the Millipore Luminex complement panels and the Quidel C3a and Ba EIA were the most sensitive assays and the only commercially available options capable of measuring the proteins of interest in the context of limited vitreous and aqueous humor sample. The concentrations measured were observed at similar ranges as those published in the literature using assays in distinct patient populations e.g. in (Mandava et al, Invest Ophthalmol Vis Sci, 2020).

Measurements from vitreous and aqueous from subject samples were deemed reportable if they were within the quantifiable ranges defined for these sample types during the validation (coefficient of variation of 20%, or 30% when results were below the lower limit of quantification but above limit of detection). Notably, given the limited amount of biomarker data due to small sample size, we share results from outlier biomarker measurements, to illustrate the heterogeneity in sample quality. We further publish plasma sample biomarker results in supplemental table 5 wherein complement protein concentrations can be observed and compared to normal ranges in the literature.

Adding confidence to the robustness of our assays was the observation that some of the complement proteins quantified by standard assay (e.g. plate and bead-based ELISAs) were also measured by the OLINK assay, and there was a general trend observed for positive correlation between results from both assays for FI levels post-treatment. However, we did not provide detailed correlative statistical analyses for further complement proteins as OLINK findings were deemed highly exploratory and hypothesis generating, and because the OLINK assay produced normalised results which are challenging to directly compare to ELISA results that were absolute.

Reviewer #2 (Public Review):

Summary:

The results presented demonstrate that AAV2-CFI gene therapy delivers long-term and marginally higher FI protein in vitreous humor that results in a concomitant reduction in the FB activation product Ba. However, the lack of clinical efficacy in the phase I/II study, possibly due to lower in vitro potency when compared to currently approved pegcetacoplan, raises important considerations for the utility of this therapeutic approach. Despite the early termination of the PPY988 clinical development program, the study achieved significant milestones, including the implementation of subretinal gene therapy delivery in older adults, complement biomarker comparison between serial vitreous humor and aqueous humor samples and vitreous humor proteomic assessment via Olink.

Strengths:

Long-term augmentation of FI protein in vitreous humor over 96 weeks and reduction of FB breakdown product Ba in vitreous humor suggests modulation of the complement system. Developed a novel in vitro assay suggesting FI's ability to reduce C3 convertase activity is weaker than pegcetacoplan and FH and may suggest a higher dose of FI will be required for clinical efficacy. Warn of the poor correlation between vitreous humor and aqueous humor biomarkers and suggest aqueous humor may not be a reliable proxy for vitreous humor with regard to complement activation/inhibition studies.

Weaknesses:

The vitrectomy required for the subretinal route of administration causes a long-term loss of total protein and may influence the interpretation of complement biomarker results even with normalization. The modified in vitro assay of complement activation suggests a several hundred-fold increase in FI protein is required to significantly affect C3a levels. Interestingly, the in vitro assay demonstrates 100% inhibition of C3a with pegcetacoplan and FH therapeutics, but only a 50% reduction with FI even at the highest concentrations tested. This observation suggests FI may not be rate-limiting for negative complement regulation under the in vitro conditions tested and potentially in the eye. It is unclear if pharmacokinetic and pharmacodynamic properties in aqueous humor and vitreous humor compartments are reliable predictors of FI level/activity after subretinal delivery AAV2-CFI gene therapy.

The authors thank the reviewer for the positive response and we agree that a limitation of the biomarker strategy for ocular gene therapy delivered to the retinal tissues is inferring PK/PD from vitreous and aqueous samples, which are the fluid sample compartments accessible from subjects available to measure molecular treatment response. We agree that these compartments may not accurately represent sub-retinal and tissue level complement turnover. In the discussion, line 508, we state: ‘Overall, the data suggests that fully functional FI is being secreted into the VH, but the regulatory effects on the level of Ba may be representative of convertase formation in the VH and not the macula retina/RPE nor the choroid. To validate this hypothesis, one approach would be to conduct vitreal sampling using an effective drug targeting C3 for GA in a larger cohort’.

However, the observation of elevation of FI in VH (and AH) post treatment, and changes in levels of downstream complement proteins that align with prior knowledge of control of alternative pathway activation, is compelling evidence that these measurements reflect modest but direct consequences of an FI-gene therapy that was delivered to the subretinal space. We add to the discussion, line 479: ‘the findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment.’

Furthermore, the observation of moderately raised FI levels in modelled VH post treatment being insufficient to control CS activation in vitro accords with the lack of clinical response observed at phase II. We note that measuring FI and complement biomarkers in retinal tissues from treated eyes at post-mortem would be one way to explore the PK/PD effects from AAV2-FI gene therapy.

Reviewer #3 (Public Review):

Summary:

The manuscript by Hallam et al describes the analysis of various biomarkers in patients undergoing complement factor I supplementation treatment (PPY988 gene therapy) as part of the FOCUS Phase I/II clinical trial. The authors used validated methods (multiplexed assays and OLINK proteomics) for measuring multiple soluble complement proteins in the aqueous humour (AH) and vitreous humour (VH) of 28 patients over a series of time points, up to and including 96 weeks. Based on biomarker comparisons, the levels of FI synthesised by PPY988 were believed to be insufficient to achieve the desired level of complement inhibition. Subsequent comparative experiments showed that PPY988-delivered FI was much less efficacious than Pegceptacoplan (FDA-approved complement inhibitor under the name SYFORVE) when tested in an artificial VH matrix.

Strengths:

The manuscript is well written with data clearly presented and appropriate statistics used for the analysis itself. It's great to see data from real clinical samples that can help support future studies and therapeutic design. The identification that complement biomarker levels present in the AH do not represent the levels found in the VH is an important finding for the field, given the number of complement-targeting therapies in development and the desperate need for good biomarkers for target engagement. This study also provides a wealth of baseline complement protein measurements in both human AH and VH (and companion measurements in plasma) that will prove useful for future studies.

Weaknesses:

Perhaps the conclusions drawn regarding the lack of observed efficacy are not fully justified. The authors focus on the hypothesis that not enough FI was synthesised in these patients receiving the PPY988 gene therapy, suggesting a delivery/transduction/expression issue. But beyond rare CFI genetic variants, most genetic associations with AMD imply that it is a FI-cofactor disease. A hypothesis supported by the authors' own experiments when they supplement their artificial VH matrix with FH and achieve a significantly greater breakdown of C3b than achieved with PPY988 treatment alone. Justification around doubling FI levels driving complement turnover refers to studies conducted in blood, which has an entirely different complement protein profile than VH. In Supplemental Table 5 we see there is approx. 10-fold more FH than FI (533ug/ml vs 50ug/ml respectively) so increasing FI levels will have a direct effect. Yet in Supplemental Table 3 we see there is more FI than FH in VH (608ng/ml vs 466ng/ml respectively). Therefore, adding more FI without more co-factors would have a very limited effect. Surely this demonstrates that the study was delivering the wrong payload, i.e. FI, which hit a natural ceiling of endogenous co-factors within the eye?

See response to reviewer 3’s review after reviewer 3 recommendations section below.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

The authors present strong evidence using validated complement biomarker assays and comprehensive proteomic profiling that support their findings. The presentation of complement biomarker data in vitreous humor and aqueous humor after FI augmentation is presented in a clear and concise format. The direct comparison of complement biomarkers in vitreous humor and aqueous humor from the same patients and demonstrating similarities and differences is important for the nascent complement gene therapy field. Developing a novel in vitro complement model and comparing pegcetacoplan, FH, and FI inhibitors provides the field with a valuable assay to benchmark other complement therapeutics. As currently designed, the in vitro assay supports why FI augmentation did not contribute to clinical success. It also suggests that non-physiological concentrations of FI protein (over 100 µg/mL) maximally inhibit C3a signal by ~50%, whereas both pegcetacoplan and FH reduce the signal by 100%. Does this suggest that CFI is not an appropriate therapeutic target to control complement overactivation in the eye?

We agree with the reviewer that the new data from the novel in vitro assay coupled with the clinical findings from the phase II gene therapy trial does now suggest FI is less attractive as a therapeutic target for controlling complement activation in the retinal tissues of subjects with Geographic Atrophy.

Reviewer #3 (Recommendations For The Authors):

I think the authors have done a great job collecting and analysing these clinical samples and elucidating the baseline complement protein profile in both the AH and VH. I only have minimal suggested changes.

Perhaps a more direct discussion around the limitations of adding more FI into environments where there is no excess of FI-cofactors present? And a discussion around the limitations of VH (and VA for that matter) biomarker sampling for a disease that primarily affects the neurosensory retina and outer blood/retinal barrier: perhaps the landscape of complement proteins is different yet again (although, admittedly, impossible to sample in a patient)? Finally, would it not have been better to perform complement activation experiments using the VH of treated patients directly rather than creating an artificial VH matrix (there may, or may not, be a couple of things in human VH that directly affect complement turnover...)?

We thank the reviewer for the supportive comments. This study is the first to describe FI and FH levels and respective ratios in vitreous humour (plus aqueous and plasma) from GA subjects, before and after sub-retinal gene therapy. It is compelling to observe that in the VH the levels of FI are greater than FH, the primary fluid phase co-factor for FI enzymatic activity. This new information does indeed argue against further FI supplementation (using gene therapy) being of added benefit to controlling the complement system in the broader population in individuals with Geographic Atrophy. We note that at the start of the clinical development of GT005/PPY988 AAV2-FI gene therapy, there was limited information on FI and FH levels in AMD in ocular fluids to inform the pharmacodynamics of complement activation. Now, by running the FOCUS phase I clinical trial and measuring the complement biomarker data using validated assays we have added to our understanding on the levels and ratio of FI to FH and other complement proteins in a larger number of GA subjects’ ocular samples.  We report the levels of complement proteins measured in ocular and systemic samples, to show the ranges and also the differences in ratios between the different matrices.   

Regarding the statement that FI supplementation could likely be ineffective due to limited FH cofactor; FH is not the only co-factor that FI may partner with at cell surfaces to become enzymatically active (others include MCP (CD46) and CR1 (CD35), although the latter is known to be of limited expression in the eye), as such, it is certainly true that other proteins may be present in the tissue altering the kinetics of FI’s activity after sub-retinal gene-therapy. In addition, the ratio between FI and FH detected in the VH may not be the same as in retinal tissue. As such, we agree that drawing insights from biomarkers in the VH may not fully reflect the disease processes and treatment response at the retinal cell layers, but it is the closest fluid sample available to sample tissue released soluble proteins. We acknowledge that VH biomarkers will not fully capture retinal disease processes and treatment responses, but due to their proximity, will reflect retina-released soluble proteins. The findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment. We agree modelling different inhibitor effects on complement activation directly using subject’s vitreous would be informative, but this was not possible due to the limitations of very small sample volume.

We add several sentences to the discussion regarding the points above. Line 473: ‘Notably, that FI does not reduce C3a breakdown to baseline even at supermolecular concentrations suggests cofactor limitation that might be more pronounced in VH given FH is not in excess of FI as is the case in blood 27. Moreover, there are additional cell-bound cofactors for FI that may be present in retinal tissue that are not present in the VH and could further alter the kinetics of the assay, such as MCP (CD46) albeit with disease related changes observed 37. However, the findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment.’

Minor comments:

Line 237: Missing parenthesis at the end of the sentence

Manuscript updated.

Line 435: Missing secondary parenthesis after .....Figure 3A)......

Manuscript updated.

Line 536: I don't think suggesting the addition of FHR proteins into the neurosensory retina/VH is such a good idea

The reference to FHRs has been clarified in the manuscript, line 558. The authors note that FHR dimerization domains have been engineered to dimerize Factor H constructs increasing half-life and potency for drugs currently in development.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Chlamydia spp. has a biphasic developmental cycle consisting of an extracellular, infectious form called an elementary body (EB) and an intracellular, replicative form known as a reticular body (RB). The structural stability of EBs is maintained by extensive cross-linking of outer membrane proteins while the outer membrane proteins of RBs are in a reduced state. The overall redox state of EBs is more oxidized than RBs. The authors propose that the redox state may be a controlling factor in the developmental cycle. To test this, alkyl hydroperoxide reductase subunit C (ahpC) was overexpressed or knocked down to examine effects on developmental gene expression. KD of ahpC induced increased expression of EB-specific genes and accelerated EB production. Conversely, overexpression of ahpC delayed differentiation to EBs. The results suggest that chlamydial redox state may play a role in differentiation.

Strengths:

Uses modern genetic tools to explore the difficult area of temporal gene expression throughout the chlamydial developmental cycle.

Weaknesses:

The environmental signals triggering ahpC expression/activity are not determined.

Thank you for your comments. Our data and those of others have shown that ahpC is expressed as a mid-developmental cycle gene (i.e., when RBs predominate in the population). This is true of most chlamydial genes, and the factors that determine developmental expression are not fully understood. As we noted in the Discussion, Chlamydia lacks AhpF/D orthologs, so it is not clear how AhpC activity is regulated. Related to determining environmental signals that trigger activity of AhpC, then this is a non-trivial issue in an obligate intracellular bacterium. Our assumption is that AhpC is constitutively active and that the increasing metabolic production of ROS eventually overcomes the innate (and stochastic) activity of AhpC to handle it, hence the threshold hypothesis. Importantly, the stochasticity is consistent with what we know about secondary differentiation in Chlamydia. We have tried to clarify these points in the Discussion.

Reviewer #2 (Public Review):

The factors that influence the differentiation of EBs and RBs during Chlamydial development are not clearly understood. A previous study had shown a redox oscillation during the Chlamydial developmental cycle. Based on this observation, the authors hypothesize that the bacterial redox state may play a role in regulating the differentiation in Chlamydia. To test their hypothesis, they make knock-down and overexpression strains of the major ROS regulator, ahpC. They show that the knock-down of ahpC leads to a significant increase in ROS levels leading to an increase in the production of elementary bodies and overexpression leads to a decrease in EB production likely caused by a decrease in oxidation. From their observations, they present an interesting model wherein an increase in oxidation favors the production of EBs.

Major concern:

In the absence of proper redox potential measurements, it is not clear if what they observe is a general oxidative stress response, especially when the knock-down of ahpC leads to a significant increase in ROS levels. Direct redox potential measurement in the ahpC overexpression and knock-down cells is required to support the model. This can be done using the roGFP-based measurements mentioned in the Wang et al. 2014 study cited by the authors.

Thank you for this suggestion. It is definitely something that we are looking to implement. However, our current vectors don’t allow for roGFP2 in combination with inducible expression of a gene of interest. We will need to completely redesign our vectors, and, in Chlamydia, the validation of such new vectors together with ahpC OE or KD may literally take a year or longer.

In lieu of this, we used the CellRox redox reactive dye to image live chlamydiae during normal growth or ahpC KD. During ahpC KD, these organisms are clearly much brighter than the control, uninduced conditions. These data are included as new Figure 5 to go along with the data we previously reported from the plate reader measurements. These data also clearly indicate that the readings we observed are from Chlamydia and not the host cell.

As far as a general oxidative stress response, Chlamydia lacks any transcriptional regulators akin to OxyR. The response we’ve measured, earlier expression of genes associated with secondary differentiation, would be an odd stress response not consistent with a focused program to respond to oxidative stress. We added new RNAseq data further showing this effect of a global earlier increase in late gene transcripts.

Reviewer #3 (Public Review):

Summary:

The study reports clearly on the role of the AhpC protein as an antioxidant factor in Chlamydia trachomatis and speculates on the role of AhpC as an indirect regulator of developmental transcription induced by redox stress in this differentiating obligate intracellular bacterium.

Strengths:

The question posed and the concluding model about redox-dependent differentiation in chlamydia is interesting and highly relevant. This work fits with other propositions in which redox changes have been reported during bacterial developmental cycles, potentially as triggers, but have not been cited (examples PMID: 2865432, PMID: 32090198, PMID: 26063575). Here, AhpC over-expression is shown to protect Chlamydia towards redox stress imposed by H2O2, CHP, TBHP, and PN, while CRISPRi-mediated depletion of AhpC curbed intracellular replication and resulted in increased ROS levels and sensitivity to oxidizing agents. Importantly, the addition of ROS scavengers mitigated the growth defect caused by AhpC depletion. These results clearly establish the role of AhpC affects the redox state and growth in Ct (with the complicated KO genetics and complementation that are very nicely done).

Weaknesses:

However, with respect to the most important implication and claims of this work, the role of redox in controlling the chlamydial developmental cycle rather than simply being a correlation/passenger effect, I am less convinced about the impact of this work. First, the study is largely observational and does not resolve how this redox control of the cell cycle could be achieved, whereas in the case of _Caulobacte_r, a clear molecular link between DNA replication and redox has been proposed. How would progressive oxidation in RBs eventually trigger the secondary developmental genes to induce EB differentiation? Is there an OxyR homolog that could elicit this change and why would the oxidation stress in RBs gradually accumulate during growth despite the presence of AhpC? In other words, the role of AhpC is simply to delay or dampen the redox stress response until the trigger kicks in, again, what is the trigger? Is this caused by increasing oxidative respiration of RBs in the inclusion? But what determines the redox threshold?

Thank you for your comments. As the reviewer notes, our work clearly demonstrates that AhpC acts as an antioxidant in Chlamydia trachomatis. Further, we have shown that transcription of the late cycle genes is altered upon altered activity of AhpC, which acts as a proof of concept that redox is (one of) the key factor(s) controlling developmental cycle progression in Chlamydia. Our new RNAseq data indicate that a broad swath of well characterized late genes is activated, which contradicts the argument that what we’ve measured is a stress response (unless activation of late genes in Chlamydia is generally a stress response (not the case based on other models of stress) – in which case we would not be able to differentiate between these effects). We hypothesize that ROS production from the metabolic activities of RBs serves as a signal to trigger secondary differentiation from RBs to EBs. How this exact threshold is determined is currently unknown as Chlamydia does not have any annotated homolog for OxyR. It is beyond the scope of the present manuscript to identify and then characterize what specific factor(s) control(s) this response. We fully anticipate that multiple factors are likely impacted by increasing oxidation, so dissecting the exact contributions of any one factor will represent (a) potential separate manuscript(s). Nonetheless, this remains an overarching goal of the lab yet remains challenging given the obligate intracellular nature of Chlamydia. Strategies that would work in a model system, like Caulobacter, that can be grown in axenic media are not easily implemented in Chlamydia.

As we noted above in another response, ahpC is transcribed as a mid-cycle gene with a peak of transcription corresponding to the RB phase of growth. We hypothesize that the gradual accumulation of ROS from metabolic activity will eventually supercede the ability of AhpC to detoxify it. This would result in any given RB asynchronously and stochastically passing this threshold (and triggering EB formation), which is consistent with what we know about secondary differentiation in Chlamydia.

I also find the experiment with Pen treatment to have little predictive power. The fact that transcription just proceeds when division is blocked is not unprecedented. This also happens during the Caulobacter cell cycle when FtsZ is depleted for most developmental genes, except for those that are activated upon completion of the asymmetric cell division and that is dependent on the completion of compartmentalization. This is a smaller subset of developmental genes in caulobacter, but if there is a similar subset that depends on division on chlamydia and if these are affected by redox as well, then the argument about the interplay between developmental transcription and redox becomes much stronger and the link more intriguing. Another possibility to strengthen the study is to show that redox-regulated genes are under the direct control of chlamydial developmental regulators such as Euo, HctA, or others and at least show dual regulation by these inputs -perhaps the feed occurs through the same path.

Comparisons to other model systems are generally of limited value with Chlamydia. All chlamydial cell division genes are mid-cycle (RB-specific) genes, just like ahpC. There is no evidence of a redox-responsive transcription factor (whether EUO, HctA, or another) that activates or represses a subset of genes in Chlamydia. Similarly, there is no evidence that redox directly and specifically impacts transcription of cell division genes based on our new RNAseq data. The types of experiments suggested are not easily implemented in Chlamydia, but we would certainly like to be able to do them.

As it pertains to penicillin specifically, we and others have shown that treating chlamydiae with Pen blocks secondary differentiation (meaning late genes are not transcribed). Effectively, Pen treatment freezes the organism in an RB state with continued transcription of RB genes. What we have shown is that, even during Pen treatment (which blocks late gene transcription), ahpC KD can overcome this block, which shows that elevated oxidation is able to trigger late gene expression even when the organisms are phenotypically blocked from progressing to EBs. The comparison from our perspective to Caulobacter is of limited value.

This redox-transcription shortcoming is also reflected in the discussion where most are about the effects and molecular mitigation of redox stress in various systems, but there is little discussion on its link with developmental transcription in bacteria in general and chlamydia.

We have edited the Discussion to include a broader description of the results and included additional citations as suggested by the reviewer (PMID: 32090198, PMID: 26063575). However, we found one suggested article (PMID: 2865432) is not relevant to our study, so we didn’t cite it in our present manuscript. There may have been a typo, so feel free to provide us the correct PMID that can be cited.

Reviewer #1 (Recommendations For The Authors):

(1) Line 146. A minor point, but inclusion-forming units directly measure infectious EBs. In some cases, the particle-to-infectivity ratio approaches unity. I don't believe IFUs are a "proxy".

Following reviewers comment we have modified the statement.

(2) Figure 2E. Results are normalized to uninduced. The actual number of IFUs in the uninduced should be provided.

In the revised version of the manuscript, we have provided actual number of IFUs at 24 and 48 hpi in the uninduced condition of both ahpC OE and EV.

(3) Figures 3B&D. The shades of gray are not possible to distinguish. I'd suggest color or direct labeling.

Following reviewer’s suggestion, in the latest version of the manuscript we have replaced gray shaded graphs with RGB colored graphs for better visualization and understanding.

(4) Lines 217-224, Figure 4. Is it possible to get micrographs of the reporter retention in chlamydiae to demonstrate that it is chlamydial ROS levels that are being measured and not cellular?

Following reviewer’s comment, we performed live-cell microscopy using uninfected HeLa cells and ahpC KD in the uninduced and induced conditions at 24 and 40 hpi. We have created new Fig. 5A with the quantitative ROS measurement graph done by the plate reader (old figure 4 E) and these new 24 hpi/40 hpi microscopy images (Fig 5B and S4).

(5) The Discussion is overly long and redundant. Large portions of the discussion are simply a rehash of the Results listing by figure number the relevant conclusions.

Following reviewer’s suggestion, the discussion is modified.

Reviewer #2 (Recommendations For The Authors):

(1) In Figure 2, ahpC is significantly overexpressed at 14 hpi. An IFA as in 2B for 14hpi will be useful. This will help to understand how quick the effect of ahpC overexpression is on development.

We have added 14 hpi IFA of ahpC and EV as part of Fig 2B.

(2) In Figure 2E, is there a reason that there is no increase in recoverable IFUs between 24h and 48h for the EV?

The graph in 2E is % of uninduced. For more clarity, we have mentioned absolute IFUs of uninduced samples in the revised manuscript and IFU level at 48 hpi IFU is higher than the 24 hpi.

(3) In Figure 3, Can relative levels of RB vs EB measured? This will provide a convincing case for the production of more EBs even when only less/more RBs are present. The same stands for Figure 4.

We assumed that the comment is for Fig. 2 not the Fig. 3 and following reviewer’s constructive suggestion, we have attempted to resolve the issue. We normalized log10 IFUs/ml with log10 gDNA for 24 hpi and added as figure 2F and 4E. This may resolve the reviewer’s concern about the levels of RBs and EBs.

(4) A colour-coded Figure 3B and D, instead of various shades of grey, will be easy for the reader to interpret.

Agreed with the reviewer. For better visualization and understanding of the data, we have replaced gray shaded graphs with RGB colored graphs in the latest version of the manuscript.

Reviewer #3 (Recommendations For The Authors):

Other comments:

(1) The first paragraph of the discussion should be deleted. It's not very useful or revealing and just delivers self-citations.

Following reviewer’s suggestion, we rewrote the discussion.

(2) The first paragraph of the results section does not present results. It's an intro.

We incorporated this information into the Intro as suggested.

(3) Has the redox difference between RBs and EBs been experimentally verified by these authors as depicted and claimed in Figure 1A with the cell-permeable, fluorogenic dye CellROX Deep Red for example? It is important to confirm this for EBs and RBs in this setup.

The difference between redox status of RBs and EBs is studied and established before by previous studies such as Wang et al., 2014.

(4) l77. Obligate intracellular alpha-proteobacteria also differentiate ... not only chlamydiae.

We have modified the sentence.

(5) l127. Is the redox state altered upon ahpC overexpression?

The ahpC overexpression strain showed hyper resistance for the tested oxidizing agents (including the highest concentration tested) indicating highly reduced conditions as a result of higher activity of AhpC.

Author response:

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

We sincerely thank the Editor and the Reviewers for their time and effort in thoroughly reviewing our manuscript and providing valuable feedback. We hope we have addressed their comments effectively and improved the clarity of our manuscript as a result.

The major revisions in the updated manuscript are as follows:

(1) Immunization experiments using mRNA in Syrian hamsters were performed (Supplementary figures 2A, B and C).

(2) An ELISPOT assay to evaluate cellular immunity in Syrian hamsters inoculated with BK2102 was conducted (Figure 2F).

(3) IgA titers in BK2102-inoculated Syrian hamsters were successfully measured (Supplementary figure 2B).

(4) New immunogenicity data for BK2102 in monkeys was additionally included (Supplementary figure 3B).

(5) The discussion section has been thoroughly revised to integrate the new data.

These results have been incorporated into the manuscript, and additional text has been added accordingly.

Below, we provide point-by-point responses to the reviewers’ comments and concerns.

Public Reviews:

Reviewer #1:

(1) A comparative safety assessment of the available m-RNA and live attenuated vaccines will be necessary. The comparison should include details of the doses, neutralizing antibody titers with duration of protection, tissue damage in the various organs, and other risks, including virulence reversal.

We agree with the Reviewer’s comment regarding the lack of data to compare BK2102 with an mRNA vaccine. Unfortunately, we were unable to obtain commercially available mRNA vaccines for research purposes and could not produce mRNA vaccines of equivalent quality. As a result, a direct comparison of the safety profiles of BK2102 and mRNA vaccines was not possible. To address this, we conducted a GLP study with an additional twelve monkeys to evaluate the safety of BK2102. Following three intranasal inoculations of BK2102 at two-week intervals, no toxic effects were observed in any of the parameters assessed, including tissue damage, respiratory rate, functional observational battery (FOB), hematology, or fever. These results are detailed in lines 115-117.

Furthermore, we compared the immunogenicity of BK2102 with that of an in-house prepared mRNA vaccine. The mRNA vaccine was designed to target the spike protein of SARS-CoV-2, and its immunogenicity was evaluated in hamsters. When serum neutralizing antibody titers were found to be comparable between the two, intranasal inoculation of BK2102 induced higher IgA levels in nasal wash samples compared to those from hamsters injected intramuscularly with the self-made mRNA vaccine (Supplementary figures. 2A and B, respectively). Additionally, while the mRNA vaccine induced Th1 and Th2 immune responses, as indicated by the detection of IgG1 and IgG2/3 (Supplementary figure. 2C), BK2102 mainly induced a Th1 response in hamsters. These explanatory sentences have been added to the manuscript (lines 140-150).

(2) The vaccine's effect on primates is doubtful. The study fails to explain why only two of four monkeys developed neutralizing antibodies. Information about the vaccine's testing in monkeys is also missing: What was the level of protection and duration of the persistence of neutralizing antibodies in monkeys? Were the tissue damages and other risks assessed?

We believe that the reason neutralizing antibody titers were observed in only 2 out of 4 monkeys in the immunogenicity study reported in the original manuscript is that only a single-dose was administered. We measured the neutralizing antibody titers in sera collected from monkeys used in the GLP study and confirmed the induction of neutralizing antibody in all 6 monkeys that received three inoculations of BK2102. This data has been included in a new figure (Supplementary figure 3B). While we would have liked to evaluate the persistence of immunity and conduct a protection study in monkeys, limitations related to facility availability and cost prevented us from doing so. As noted in (1), tissue injury and other risk assessments were evaluated in the GLP study, which showed no evidence of tissue injury or other toxic effects. These results are described in lines 113-117.

(3) The vaccine's safety in immunosuppressed individuals or individuals with chronic diseases should be assessed. Authors should make specific comments on this aspect.

In general, live-attenuated vaccines are contraindicated for immunosuppressed individuals or those with chronic conditions, and therefore BK2102 is also not intended for use in these patients.

This information has been added to the Discussion section (lines 309-311).

(4) The candidate vaccine has been tested with a limited number of SARS-CoV-2 strains. Of note, the latest Omicron variants have lesser virulence than many early variants, such as the alfa, beta, and delta strains.

We have added the results of a protection study against the SARS-CoV-2 gamma strain to Supplementary figures 5A and B. No weight loss was observed in BK2102-inoculated hamsters following infection with the gamma strain. These results are described in lines 109-111, 158-162.

(5) Limitations of the study have not been discussed.

We apologize for the ambiguity in the description of the Limitations of this paper. One major limitation of this study is that, despite observing high immunogenicity in hamsters, it remains uncertain whether the same positive results would be achieved in humans. Differences in susceptibility exist between species, which are not solely attributed to weight differences. For instance, while a single dose of 10³ PFU of BK2102 was sufficient to induce neutralizing antibodies in hamsters, a higher dose of 10⁷ PFU in monkeys was required to induce antibodies in only about 50% of the monkeys. Additionally, two more challenges in development of BK2102 were added to the discussion. The first was the limited availability of analytical reagents for hamster models, which restricted the detailed immunological characterization of the response. Second, it took time to gather preclinical data due to the space-related restrictions of BSL3 facilities, which delayed the clinical trials for BK2102 until many individuals had already acquired immunity against SARS-CoV-2. It remains to be seen whether our candidate will be optimal for human use, as the immunogenicity of live-attenuated vaccines is generally influenced by pre-existing immunity.

We added these considerations to the discussion section (lines 300-309).

Reviewer #2:

No major weaknesses were identified, however, this reviewer notes the following:

The authors missed the opportunity to include a mRNA vaccine to demonstrate that the immunity and protection efficacy of their live attenuated vaccine BK2102 is better than a mRNA vaccine.

One of the potential advantages of live-attenuated vaccines is their ability to induce mucosal

immunity. It would be great if the authors included experiments to assess the mucosal immunity of their live-attenuated vaccine BK2102.

We agree with the Reviewer’s suggestion regarding the importance of comparing BK2102 with the mRNA vaccine modality and evaluating the mucosal immunity induced by BK2102. In hamsters, under conditions where serum neutralizing antibody titers were equivalent, intranasal inoculation of BK2102 induced higher levels of antigen-specific IgA in nasal wash compared to intramuscular injection of the conventional mRNA vaccine. This new data has been added in Supplementary figures 2A and B, and corresponding sentences have been included in the Results and Discussion sections (lines 140-145, 292-299).

Reviewer #3:

Lack of a more detailed discussion of this new vaccine approach in the context of reported live-attenuated SARS-CoV-2 vaccines in terms of its advantages and/or weaknesses.

sCPD9 and CoviLiv^TM, two previously reported live-attenuated vaccines, achieve attenuation through codon deoptimization or a combination of codon deoptimization and FCS deletion. These two strategies affect viral proliferation but do not directly impact virulence. In contrast, the temperature sensitivity-related substitutions in NSP14 included in BK2102 selectively restrict the infection site, reducing the likelihood of lung infection and providing a safety advantage over the other live-attenuated vaccines. As mentioned in the response to comment (5) of Reviewer #1, a limitation of BK2102 is that its development began later than that of the previously reported live-attenuated vaccines. Consequently, we must consider the impact of pre-existing immunity in future human trials. Based on these points, we have added sentences discussing the advantages and disadvantages to the Discussion section (lines 302-305, 312-319).

Antibody endpoint titers could be presented.

Thank you for your suggestion. We calculated the antibody endpoint titers for Figure 2A and included the results in lines 105-107 of the revised manuscript.

Lack of elaboration on immune mechanisms of protection at the upper respiratory tract (URT) against an immune evasive variant in the absence of detectable neutralizing antibodies.

We appreciate the comment. The potential role of cellular and mucosal immunity in protection has been discussed in more detail in the revised manuscript, specifically in lines 283-295. According to the reference we initially cited, Hasanpourghadi et al. evaluated their adenovirus vector vaccine candidates and reported that the protection was enhanced by co-expression of the nucleocapsid protein rather than relying solely on the spike protein (Hasanpourghadi et al., Microbes Infect, 2023). Therefore, cellular immunity against the nucleocapsid and/or other viral proteins induced by BK2102 may also contribute to protection, as evidenced by more pronounced cellular immunity to the nucleocapsid detected through ELISPOT assay. Moreover, antigen-specific mucosal immunity was successfully detected in additional studies. The involvement of mucosal immunity in protection against mutant strains has been documented in the previously cited reference (Thwaites et al., Nat Commun, 2023). We have included these new data in Figure 2F and Supplementary figure 2B. Additionally, the results and discussion regarding the mechanisms of protection in the upper respiratory tract, in the absence of detectable neutralizing antibodies, have been incorporated into the revised lines 136-139, 143-145 and 283-295, respectively.

Recommendations for the authors:

Reviewer #2:

Figure 1: Please include the LOD and statistical analysis in both panels. Please consider passaging the virus in Vero cell s, approved for human vaccine production, to assess the stability of BK2102 after serial passage in vitro, which is important for its implementation as a live-attenuated vaccine. The authors should consider evaluating viral replication in different cell lines, and also assessing the plaque phenotype.

Thank you for your valuable comments. First, we have added the statistical analysis and the limit of detection (LOD) to Figure 1. In response to the comments regarding the stability of BK2102 after serial passage in Vero cells, as well as its replication and plaque phenotype in different cell lines, we manufactured test substances for GLP studies and clinical trials by passaging BK2102 in Vero cells, which are approved for human vaccine production. We confirmed that BK2102 is stable (data not shown). Additionally, we verified that BK2102 replicates in BHK, Vero E6, and Vero E6/TMPRSS2 cells, in addition to Vero cells. Among these options, we selected Vero cells due to their high proliferative capacity and ability to produce clear plaques.

Figure 2: Please, include statistical analysis in panels A, B, and D. Please, include the LOD in panels A and D. Please, include viral titers from these experiments in hamsters and NHPs.

First, we would like to note that Figure 2D has been replaced by Figure 2C in the revised manuscript, and the data on neutralizing antibody titers in non-human primates (NHPs), originally presented as Figure 2C, have been moved to the Supplementary figure 3A.

We have added the statistical analysis to Figure 2B and C, as well as the LOD to Figure 2C. Figure 2A (Spike-specific IgG ELISA) was intended for qualitative evaluation based on OD values, so the LOD was not defined. We have also added a detailed description of virus titer in the Methods section under the headings “Evaluation of Immunogenicity in Hamsters” and “Evaluation of Immunogenicity in Monkeys”, and updated the information in the Figure legends of the revised manuscript (lines 451, 459, 468-474, 566-567, 576-578, 582-584, 661-662).

Figure 3: Please, include the viral titers of the challenge virus in the NT and lungs.

We have added the virus titers for the challenge experiments to the Results section under the heading “BK2102 induced protective immunity against SARS-CoV-2 infection” (lines 168-174).

Figure 4: Please, include statistical analysis in panels B and C and evaluate viral titers.

We have added the statistical analysis to Figure 4B and C. Unfortunately, all samples in Figure 4 were fixed in formalin for histopathological examination, so virus titers could not be measured. However, in past experiments, we measured viral titers in the nasal wash samples and lungs of hamsters three days post-infection with D614G and BK2102. We confirmed that infectious virus was detected in both the nasal wash and lungs of the hamsters infected with D614G strain (2.9 log10 PFU/mL and 5.3 log10 PFU/g, respectively), but not in the lungs of the hamsters with BK2102. The viral titers in the nasal wash of BK2102-infected hamsters were equivalent to those of the hamsters infected with the D614G wild-type strain (3.0 log10 PFU/mL). However, we did not include this data to the revised manuscript.

Figure 5: Please, include viral titers in different tissues with the different vaccines (panels A and B). Please, include the body weight changes.  Finally, please, consider the possibility of challenging the vaccinated mice with the same SARS-CoV-2 strains used in the manuscript to demonstrate similar protection efficacy in this new ACE2 transgenic mice.

The different tissues of Tg mice were not sampled, as no gross abnormalities were observed in organs other than lungs and brains during necropsy. We have added new data on the body weight of Tg mice after infection to Supplementary figures 9B and 9C in the revised manuscript, along with additional lines in the Results section (lines 228-230 and 247-248). Although we do not know the reason, we have observed that immunization of this animal model does not lead to an increase in antibody titers. Therefore, we do not consider this animal model suitable for the protection study as you suggested. However, it could be useful in passive immunization experiments.

Supplementary Figure 1: Since most of the manuscript focuses on BK2102, the authors should consider removing the other live-attenuated vaccines (Supplementary Figure 1A).

We agree with the Reviewer’s suggestion and have simplified the description for Supplementary Figure 1A (lines 93-97).

Supplementary Figure 3: Please, include statistical analysis.

In the revised manuscript, Supplementary Figure 3 from the original manuscript has been moved to Supplementary Figure 2D. The IgG subclass ELISA was intended for a qualitative evaluation based on OD values, and therefore the results were included in the Supplementary figure. However, we realized the description was not clear, so we added further clarification in the Results section (lines 145-147).

Supplementary Figure 4: Please, include the viral titers in both infected and contact hamsters from this experiment.

In the revised manuscript, Supplementary Figure 4 in the original manuscript has been moved to Supplementary Figure 6. Unfortunately, due to limited breeding space for the hamsters, we were unable to prepare groups for the evaluation of viral titer, and instead prioritized evaluation by body weight.

Reviewer #3:

(1) It would be helpful to discuss this new vaccine in the context of other reported live-attenuated vaccines in terms of its advantages and/or disadvantages.

Please refer to our response to the Reviewer’s “first comment” above, as well as to the response in Public comment (5) of Reviewer #1. The modifications made in the manuscript are described in lines 302-305 and 312-319.

(2) Figure 2A: end-point titers could be presented, other than OD values.

This comment is addressed in the reviewer’s second public comment. The endpoint titer has been included in lines 105-107 of the revised manuscript.

(3) Figure 2C: it is unclear why only 2 out of 4 NHPs show neutralization titers. This could be moved to a supplementary figure.

As suggested by the Reviewer, Figure 2C of the original manuscript has been moved to Supplementary Figure 3A in the revised manuscript. In response Public comment (2) from Reviewer #1, we have also added new data on neutralizing antibodies in the monkeys as Supplementary figure 3B.

(4) Figures 2E-F: bulk measurement of cytokine production in supernatants is not an optimal way to measure vaccine-induced Ag-specific T cells. ELISPOT or ICS are better. T-cell ELSIPOT for hamsters is available. This should at least be discussed.

Please refer to our response to this Reviewer’s third public comment. We have added the new results in Figure 2F of the revised manuscript.

(5) It is quite interesting that no N-specific cellular response was observed, given that it is a live-attenuated vaccine. What about N-specific binding Abs?

We conducted the ELISPOT assay as suggested by the Reviewer and detected cellular immunity against both spike and nucleocapsid proteins (Figure 2F). We did not examine nucleocapsid-specific antibodies, as they do not contribute to the neutralizing activity; however, nucleocapsid-specific cellular immunity was confirmed.

(6) Figure 3: limit of detection for virological assays could be labeled.

We have added the LOD in Figures 3C, D, F and G.

(7) Figures 3E-F: it is interesting to see that the vaccine elicits almost complete protection at URT against BA.5, despite no BA.5 neutralizing titers being detected at all. What mechanism of URT protection by BK2102 would the authors speculate? T cells or other Ab effector functions?

Please refer to the response to this Reviewer’s third public comment. We have added new results regarding cellular and mucosal immunity (Figure 2F and Supplementary figure 2B) and discussed the mechanisms of protection in the upper respiratory tract in the absence of detectable neutralizing antibodies (lines 136-139, 143-145 and 283-295, respectively).

(8) Figure 3I: the durability of protection is a strength of the study. Other than body weight changes, what about viral loads in the animals after the challenge?

We primarily assessed the effect of the vaccine by monitoring changes in body weight, as the differences compared to the naïve group were clear. Unfortunately, we did not collect samples at different time points throughout the study, which prevented us from evaluating the viral titers.

In addition, we made corrections to several other sections identified during the revision process. The revised parts are as follows:

- In the Methods section under the title “Evaluation of BK2102 pathogenicity in hamsters”, the infectious virus titer of D614G strain has been corrected (line 478).

- In the Methods section under the title “In vivo passage of BK2102 in hamsters”, infectious virus titer of BK2102 and A50-18 strain has been corrected (line 487).

- The collection time of splenocytes after inoculation has been corrected in the figure legend of Figure 2D, (line 583).

- There was an error in Figure 2D. The figure has been replaced with the appropriate version.

- A new reference on NSP1 deletion (Ueno et al., Virology, 2024) has been added to the references.

- Several methods have been described more clearly.

Author response:

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

Comments on the revised version:

Concerns flagged about using CRISPR -guide RNA mediated knockdown of viral has yet to be addressed entirely. I understand that the authors could not get knock out despite attempts and hence they have guide RNA mediated knockdown strategy. However, I wondered if the authors looked at the levels of the downstream genes in this knockdown.

We thank the reviewer for bringing this up since it is known that certain artifacts derived from this approach may be related with changes in expression of downstream genes. We run a qPCR of Rv0432 and Rv0433 and confirmed that no significant differences in expression of virR downstream genes were detected in the virR mutant or the complemented strains relative to WT. This is now indicated in the method section on Generation of the CRISPR mutants. The data is now presented as Supplementary Figure 13.

Authors have used the virmut-Comp strain for some of the experiments. However, the materials and methods must describe how this strain was generated. Given the mutant is a CRISPR-guide RNA mediated knockdown. The CRISPR construct may have taken up the L5 loci. Did authors use episomal construct for complementation? If so, what is the expression level of virR in the complementation construct? What are the expression levels of downstream genes in mutant and complementation strains? This is important because the transcriptome analysis was redone by considering complementation strain. The complemented strain is written as virmut-C or virmut-Comp. This has to be consistent.

We apologize for not having included the information about the generation of the complemented strain in our last version of the manuscript. We took the complementing vector from a previous paper on VirR (Rath et al., (2013) PNAS 110(49):E4790). This vector was constructed as follows: Complementation plasmids were cloned using Gateway® Cloning Technology (Invitrogen). E. coli strains expressing the following Gateway vectors were kindly provided by Dirk Schnappinger and Sabine Ehrt: pDO221A, pDO23A, pEN23A-linker1, pEN41A-TO2, pEN21A-Hsp60, pDE43-MEH. PCR was used to amplify the following target sequences from H37Rvgenomic DNA: coding sequence of Rv0431, coding sequence of Rv0431 with a FLAG tag either in its C-terminus or its N-terminus, and the predicted cytosolic sequence of Rv0431 with a FLAG tag in its new C-terminus. The primers used for PCR were designed such that the amplicons would be flanked with Gateway® cloning- specific attachment (att) sites. These PCR products were recombined into Gateway® donor vectors using bacteriophage-derived integrase and integration host factor, resulting in entry vectors. The recombination events are specific to the attB sites on the PCR products and to the attP sequences on the donor vectors, such that the orientation of the target sequence is maintained during the recombination reaction, also known as the BP reaction, for attB-attP recombination. Using the MultiSite Gateway® system, three DNA fragments, derived from each of three distinct entry vectors, can be simultaneously inserted into a final complementation vector called the destination vector in a specific order and orientation. Multisite recombination events are mediated by Integrase and Integrase Host Factor, in a process called the LR reaction (for the attL and attR sites in the entry and destination vectors). The Gateway® entry vectors thus generated were recombined with another entry vector containing either the Hsp60 promoter, an empty entry vector, and a complementation vector (episomal) to give rise to the final destination vector. The destination vector (episomal) was engineered to contain a hygromycin resistance cassette. These vectors were used to transform competent Rv0431-deficient Mtb. The transformation mixture was plated on 7H11 plates containing OADC and hygromycin (50 μg/ml). Colonies, typically observed 3-5 weeks later, were isolated and grown in 7H9 media and characterized.

For simplicity, we have just referenced our previous paper to indicate that the complementing plasmid is the same used in that study.

Regarding the virR expression levels in the WT, virR^mut and complemented virR strains please see previous Figure 6 C.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have revised the manuscript in light of previous reviews. The authors have addressed some of my concerns appropriately. However, the specific dataset remains unchanged and unclear.

Fig 8G and H: In response to a comment on the mechanism of how VirR mediates EV release, the authors have added new data showing an increase in the abundance of deacetylated muropeptides in the mutant. This observation is linked to altered lysozyme activity or PG fragility. In my opinion, this is another indirect observation. More concerning is the complemented strain, which also showed a comparable increase in deacetylated muropeptides, indicating that the altered muropeptides could be unrelated to VirR.

We must disagree here with the reviewer assessment about the fact that the abundance of deacetylated muropeptides is an indirect indication of PG fragility. We consider that this observation and quantitative fact is another additional evidence that indicate a more fragile PG. We believe that considering each of the supporting facts individually may be seen as indirect, but we would like that the reviewer take all the evidence together: (i) sensitivity to lysozyme; (ii) enlargement and altered physicochemical morphological characteristics including porosity or thickness; (iii) altered penetrance of FDAAs; and (iv) increased released of muropeptides. In this later fact, the complemented strain may not display the WT features, but this may be due to some artifacts derived from the complementation.

Taking all together, we believe that the PG of virR^mut is more fragile than that of the WT and the complemented strains based on a series of evidence. We hope the reviewer may consider this perspective when analyzing such a complex feature like PG fragility. So far, there is not a direct method to assess this condition.

Lipid analyses are not comprehensive. The issue related to the need for more clarity of DIMA and DIMB still needs to be addressed. I understand that the authors do not have facilities to perform radioactive assays. However, they could have repeated the experiment to generate a better-quality image. Similarly, the newly generated SL-1, PAT, and DAT TLC could be of better quality. Bands still need to be resolved. The solvent front is irregular. The same is true for PIMs and DPG TLCs. With the evidence provided, the deregulation of cell wall lipids is incomplete.

We agree with the reviewer that the quality of the TLC is not appropriate. We have no repeated the PDIM TLC (new Fig 7D). In addition, we have repeated the TLCs resolving sulfolipids in a 2D mode. For simplicity we just run the glycerol condition including the three strains. This is now part of a new Supplementary figure 8 B. For PIMs, we have a 1D and a 2D analysis that, after checking previous papers using similar approaches with no radioactivity, we consider that it has the desired quality to identify the indicated lipids.

We hope this new data and repeated experiments satisfy the reviewer concerns.

Thank you very much for your assessment and time to review this paper.

Author response:

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

Reviewer # 1 (Public Review):

Summary:

Inthispreprint, theauthorssystematicallyandrigorouslyinvestigatehowspecificclassesofresiduemutations alter the critical temperature as a proxy for the driving forces for phase separation. The work is well executed, the manuscript well-written, and the results reasonable and insightful.

Strengths:

The introductory material does an excellent job of being precise in language and ideas while summarizing the state of the art. The simulation design, execution, and analysis are exceptional and set the standard for these types of large-scale simulation studies. The results, interpretations, and Discussion are largely nuanced, clear, and well-motivated.

We thank the reviewer for their assessment of our work and for highlighting the key strengths of the paper.

Weaknesses:

This is not exactly a weakness, but I think it would future-proof the authors’ conclusions to clarify a few key caveats associated with this work. Most notably, given the underlying implementation of the Mpipi model, temperature dependencies for intermolecular interactions driven by solvent effects (e.g., hydrophobic effect and charge-mediated interactions facilitated by desolvation penalties) are not captured. This itself is not a “weakness” per se, but it means I would imagine CERTAIN types of features would not be wellcaptured; notably, my expectation is that at higher temperatures, proline-rich sequences drive intermolecular interactions, but at lower temperatures, they do not. This is likely also true for the aliphatic residues, although these are found less frequently in IDRs. As such, it may be worth the authors explicitly discussing.

We also thank the reviewer for pointing out that a more detailed discussion of the model limitations is needed. The original Mpipi model was designed to probe UCST-type transitions (that are associative in nature) of disordered sequences. The reviewer is correct, that in its current form, the model does not capture LCST-type transitions that depend on changes in solvation of hydrophobic residues with temperature. We have amended the discussion to highlight this fact.

Similarly, prior work has established the importance of an alpha-helical region in TDP-43, as well as the role of aliphatic residues in driving TDP-43’s assembly (see Schmidt et al 2019). I recognize the authors have focussed here on a specific set of mutations, so it may be worth (in the Discussion) mentioning [1] what impact, if any, they expect transient or persistent secondary structure to have on their conclusions and [2] how they expect aliphatic residues to contribute. These can and probably should be speculative as opposed to definitive.

Again - these are not raised as weaknesses in terms of this work, but the fact they are not discussed is a minor weakness, and the preprint’s use and impact would be improved on such a discussion.

We agree with the reviewer that the effects of structural changes/propensities on these scaling behaviors would be an interesting and important angle to probe. We also comment on this in the discussion.

Reviewer # 2 (Public Review):

This is an interesting manuscript where a CA-only CG model (Mpipi) was used to examine the critical temperature (Tc) of phase separation of a set of 140 variants of prion-like low complexity domains (PLDs). The key result is that Tc of these PLDs seems to have a linear dependence on substitutions of various sticker and space residues. This is potentially useful for estimating the Tc shift when making novel mutations of a PLD. However, I have strong reservations about the significance of this observation as well as some aspects of the technical detail and writing of the manuscript.

We thank the reviewer for their thoughtful and detailed feedback on the manuscript.

(1) Writing of the manuscript: The manuscript can be significantly shortened with more concise discussions. The current text reads as very wordy in places. It even appears that the authors may be trying a bit too hard to make a big deal out of the observed linear dependence.

The manuscript needs to be toned done to minimize self-promotion throughout the text. Some of the glaring examples include the wording “unprecedented”, “our research marks a significant milestone in the field of computational studies of protein phase behavior ..”, “Our work explores a new framework to describe, quantitatively, the phase behavior ...”, and others.

We thank the reviewer for their suggestions on the writing of the manuscript. We understand the concern regarding the length and tone of the manuscript, and in response to their feedback, we have revised the language throughout the manuscript.

There is really little need to emphasize the need to manage a large number of simulations for all 140 variants. Yes, some thoughts need to go into designing and managing the jobs and organizing the data, but it is pretty standard in computational studies. For example, large-scale protein ligand-free energy calculations can require one to a few orders of magnitude larger number of runs, and it is pretty routine.

We fully agree with the reviewer that this aspect of the study is relatively standard in computational research and does not require special emphasis. In response, we have revised the manuscript to shorten the aforementioned section, focusing instead on the scientific insights gained from the simulations rather than the logistical challenges of managing them.

When discussing the agreement with experimental results on Tm, it should be noted that the values of R > 0.93 and RMSD < 14 K are based on only 16 data points. I am not sure that one should refer to this as “extended validation”. It is more like a limited validation given the small data size.

We thank the reviewer for their consideration of our validation set. Indeed, the agreement with experimental results is based on 16 data points, as this set represents the available published data at the time of writing of this manuscript. The term “extended validation” is used to signify that our current dataset builds upon previous validations (in Joseph, Reinhardt et al. Nat Comput. Sci. 2021), incorporating additional variants not previously examined. The metrics of an r>0.93 and a low RMSD indicate a strong agreement between the model and experiments, and an improvement with respect to other reported models. We are committed to continue validating our methods.

Results of linear fitting shown in Eq 4-12 should be summarized in a single table instead of scattering across multiple pages.

We considered the reviewer’s suggestion to compile all the laws into a single table. However, we believe it would be more effective for readers to reference each relationship directly where it is first discussed in the text. That said, we do include Table 1 in the original manuscript, which provides a summary of all the laws.

The title may also be toned down a bit given the limited significance of the observed linear dependence.

We respectfully disagree with the reviewer and believe that the current title accurately captures the scope of the manuscript.

(2) Significance and reliability of Tc: Given the simplicity of Mpipi (a CA-only model that can only describe polymerchaindimension)andthelowcomplexitynatureofPLDs, thesequencecompositionitselfisexpected to be the key determinant of Tc. This is also reflected in various mean-field theories. It is well known that other factors will contribute, such as patterning (examined in this work as well), residual structures, and conformational preferences in dilute and dense phases. The observed roughly linear dependence is a nice confirmation but really unsurprising by itself. It appears how many of the constructs deviate from the expected linear dependence (e.g., Figure 4A) may be more interesting to explore.

While linear dependencies in critical solution temperatures may appear expected for certain systems, for example, symmetric hard spheres, the heterogeneity of intrinsically disordered regions (IDRs), like prion-like domains (PLDs), make this finding notable. The simplicity of our linear scaling law belies the underlying complexity of multivalent interactions and sequence-dependent behaviors in a certain sequence regime, which has not been quantitatively characterized in this manner before. Likewise, although linear dependencies may be expected in simplified models, the real-world applicability and empirical validation of these laws in biologically relevant systems are not guaranteed. Our chemically based model provides the robustness needed to do that. The linear relationship observed is significant because it provides a predictive framework for understanding how specific mutations affect a diverse set of PLDs. The framework presented can be extended to other protein families upon the application of a validated model, which might or might not yield linear relationships depending on the cooperative effects of their collective behavior. This extends beyond confirming known theories—it offers a practical tool for predicting phase behavior based on sequence composition

We agree with the reviewer that, while the overarching linear trend is clear, deviations from linearity observed in constructs like those in Figure 4A point to additional, and interesting, layers of complexity. These deviations offer interesting avenues for future research and suggest that while linearity might dominate PLD critical behavior, other factors may modulate this behavior under specific conditions.

This is an excellent suggestion from the reviewer that, while it falls outside the scope of the current study, we are interested in exploring in the future.

Finally, the relationships are all linear, they have been normalized in different ways—the strength of the study also lies in that. Instead of focusing solely on linearity, our study explores the physical mechanisms that underlie these relationships. This approach provides a more complete understanding of how sequence composition and the underlying chemistry of the mutated residues influence T<sub>c</sub.

The assumption that all systems investigated here belong to the same universality class as a 3D Ising model and the use of Eqn 20 and 21 to derive Tc is poorly justified. Several papers have discussed this issue, e.g., see Pappu Chem Rev 2023 and others. Muthukumar and coworkers further showed that the scaling of the relevant order parameters, including the conserved order parameter, does not follow the 3D Ising model. More appropriate theoretical models including various mean field theories can be used to derive binodal from their data, such as using Rohit Pappu’s FIREBALL toolset. Imposing the physics of the 3D Ising model as done in the current work creates challenges for equivalence relationships that are likely unjustified.

We thank the reviewer for raising this point and for highlighting the FIREBALL toolset. Based on our understanding, FIREBALL is designed to fit phase diagrams using mean-field theories, such as Flory–Huggins and Gaussian Cluster Theory. Our experience with this toolset suggests that it places a higher weight on the dilute arm of the binodal. However, in our slab simulations, we observe greater uncertainty in the density of the dilute arm. This leads to only a moderate fit of the data to the mean-field theories employed in the toolset. While we agree that there is no reason to assume the phase behavior of these systems is fully captured by the 3D Ising model, we expect that such a model will describe the behavior near the critical point better than mean-field theories. Testing our results further with different critical exponents would be valuable in assessing how these predictions compare to a broader set of experimental data. Additionally, we have made the raw data points for the phase diagrams available on our GitHub, enabling practitioners to apply alternative fitting methods.

While it has been a common practice to extract Tc when fitting the coexistence densities, it is not a parameter that is directly relevant physiologically. Instead, Csat would be much more relevant to think about if phase separation could occur in cells.

WhileitistruethatCsatisdirectlyrelevanttowhetherphaseseparationcanoccurincellsunder physiological conditions, T_c should not be dismissed as irrelevant.T_c provides fundamental insights into the thermodynamics of phase separation, reflecting the overall stability and strength of interactions driving condensate formation. This stability is crucial for understanding how environmental factors, such as temperature or mutations, might affect phase behavior. In Figure 2C and D we compare experimental C_sat values with our predicted T_c from simulations. These quantities are roughly inversely proportional to each other and so we expect that, to a first approximation, the relationships recovered for T_c should hold when consideringC_sat at a fixed temperature.

Reviewer # 3 (Public Review):

Summary:

“Decoding Phase Separation of Prion-Like Domains through Data-Driven Scaling Laws” by Maristany et al. offers a significant contribution to the understanding of phase separation in prion-like domains (PLDs). The study investigates the phase separation behavior of PLDs, which are intrinsically disordered regions within proteins that have a propensity to undergo liquid-liquid phase separation (LLPS). This phenomenon is crucial in forming biomolecular condensates, which play essential roles in cellular organization and function. The authors employ a data-driven approach to establish predictive scaling laws that describe the phase behavior of these domains.

Strengths:

The study benefits from a robust dataset encompassing a wide range of PLDs, which enhances the generalizability of the findings. The authors’ meticulous curation and analysis of this data add to the study’s robustness. The scaling laws derived from the data provide predictive insights into the phase behavior of PLDs, which can be useful in the future for the design of synthetic biomolecular condensates.

We thank the reviewer for highlighting the importance of our work and for their critical feedback.

Weaknesses:

While the data-driven approach is powerful, the study could benefit from more experimental validation. Experimental studies confirming the predictions of the scaling laws would strengthen the conclusions. For example, in Figure 1, the Tc of TDP-43 is below 300 K even though it can undergo LLPS under standard conditions. Figure 2 clearly highlights the quantitative accuracy of the model for hnRNPA1 PLD mutants, but its applicability to other systems such as TDP-43, FUS, TIA1, EWSR1, etc., may be questionable.

In the manuscript, we have leveraged existing experimental data for the A1-LCD variants, extracting critical temperatures and saturation concentrations to compare with our model and scaling law predictions. We acknowledge that a larger set of experiments would be beneficial. By selecting sequences that are related, we hypothesize that the scaling laws described herein should remain robust. In the case of TDP-43, to our knowledge this protein does not phase separate on its own under standard conditions. In vitro experiments that report phase separation at/above 300 K involve either the use of crowding agents (such as dextran or PEG) or multicomponent mixtures that include RNA or other proteins. Therefore, our predictions for TDP-43 are consistent with experiments. In general, we hope that the scaling laws presented in our work will inspire other researchers to further test their validity.

The authors may wish to consider checking if the scaling behavior is only observed for Tc or if other experimentally relevant quantities such as Csat also show similar behavior. Additionally, providing more intuitive explanations could make the findings more broadly accessible.

In Figure 2C and D we compare experimental C_sat values with our predicted T_c from simulations. These quantities are roughly inversely proportional to each other and so we expect that, to a first approximation, the relationships recovered for T_c should hold when considering C_sat at a fixed temperature.

The study focuses on a particular subset of intrinsically disordered regions. While this is necessary for depth, it may limit the applicability of the findings to other types of phase-separating biomolecules. The authors may wish to discuss why this is not a concern. Some statements in the paper may require careful evaluation for general applicability, and I encourage the authors to exercise caution while making general conclusions. For example, “Therefore, our results reveal that it is almost twice more destabilizing to mutate Arg to Lys than to replace Arg with any uncharged, non-aromatic amino acid...” This may not be true if the protein has a lot of negative charges.

A significant number of proteins, in addition to those mentioned in the manuscript, that contain prion-like low complexity domains have been reported to exhibit phase separation behaviors and/or are constituents of condensates inside cells. We therefore expect these laws to be applicable to such systems and have further revised the text to emphasize this point. As the reviewer suggests, we have also clarified that the reported scaling of various mutations applies to these systems.

I am surprised that a quarter of a million CPU hours are described as staggering in terms of computational requirements.

We have removed the note on CPU hours from the manuscript. However, we would like to clarify that the amount of CPU hours was incorrectly reported. The correct estimate is 1.25 million hours, but this value was unfortunately misrepresented during the editing process. We thank the reviewer for catching this mistake on our part.

Reviewer # 1 (Recommendations For The Authors):

Some minor points here:

“illustrating that IDPs indeed behave like a polymer in a good solvent [43]. ” Whether or not an IDP depends as a polymer in a good solvent depends on the amino acid sequence - the referenced paper selected a set of sequences that do indeed appear on average to map to a good-solvent-like polymer, but lest we forget SAXS experiments require high protein concentrations and until the recent advent of SEC-SAXS, your protein essentially needed to be near infinitely soluble to be measured. As such, this paper’s conclusions are, apparently, ignorant of the limitations associated with the data they are describing, drawing sweeping generalizations that are clearly not supported by a multitude of studies in which sequence-dependencies have led to ensembles with a scaling exponent far below 0.59 (See Riback et al 2017, Peng et al 2019, Martin et al 2020, etc).

We thank the reviewer for raising this point. To avoid making incorrect generalizations and potentially misleading readers, we have removed the quoted statement from our manuscript.

As of right now, the sequences are provided in a convenient multiple-sequence alignment figure. However, it would be important also to provide all sequences in an Excel table to make it easy for folks to compare.

In addition to the sequence alignment figure, we now provide all tested sequences in an Excel table format in the GitHub repository.

Maybe I’m missing it, but it would be extremely valuable if the coexistence points plot in all the figures were provided as so-called source data; this could just be on the GitHub repository, but I’m envisaging a scenario where for each sequence you have a 4 column file where Col1=concentration and Col2=temperature, col3=fit concentration and col4=fit temperature, such that someone could plot col1 vs. col2 and col3 vs. col4 and reproduce the binodals in the various figures. Given the tremendous amount of work done to achieve binodals:

The coexistence points used to plot the figures are now provided in the GitHub, in a format similar to that suggested by the reviewer.

It would be nice to visually show how finite size effects are considered/tested for (which they are very nicely) because I think this is something the simulation field should be thinking about more than they are.

Thank you for highlighting this point. In our previous work (supporting information of the original Mpipi paper), we demonstrated a thorough approach by varying both the cross-sectional area of the box and the long axis while keeping the overall density constant. In this work, we verified that the cross-sectional area was larger than the average R_g of the protein. We then maintained a fixed cross-sectional area to long-axis ratio, varying the number of proteins while keeping the overall density constant. We have updated Appendix 1–Figure 2 to clarify our procedure and revised the caption to better explain how we ensured the number of proteins was adequate.

When explaining the law of reticular diameters, it would be good to explain where the 3.06 exponent comes from.

Based on the reviewer’s suggestion, we have added to the text: “The constant 3.06 in the equation is a dimensionless empirical factor that was derived from simulations of the 3D Ising model.”

The NCPR scale in Figure 5 being viridis is not super intuitive and may benefit from being seismic or some other r-w-b colormap just to make it easier for a reader to map the color to meaning.

We thank the reviewer for this suggestion and have replaced the scale with a r-w-b colormap.

The “sticker and spacer” framework has received critiques recently given its perceived simplicity. However, this work seems to clearly illustrate that certain types of residues have a large effect on Tc when mutated, whereas others have a smaller effect. It may be worth re-phrasing the sticker-spacer introduction not as “everyone knows aromatic/arginine residues are stickers” but as “aromatic and arginine residues have been proposed to be stickers, yet other groups have argued all residues matter equally” and then go on to make the point that while a black-and-white delineation is probably not appropriate, based on the data, certain residues ARE demonstrably more impactful on Tc than others, which is the definition of stickers. With this in mind, it may be useful to separate out a sticker and a spacer distribution in Figure 1D, because the different distribution between the two residues types is not particularly obvious from the overlapping points.

We have revised the introduction of the sticker–spacer model in the manuscript for clarity. As the reviewer suggests, we have also separated the sticker and spacer distribution, which is now summarized in new Appendix 0–figure 8.

Reviewer # 3 (Recommendations For The Authors):

Figure 2 clearly highlights the quantitative accuracy of the model for hnRNPA1 PLD mutants, but its applicability to other systems such as TDP-43, FUS, TIA1, EWSR1, etc., may be questionable. The following sentence may be revised to reflect this: “Our extended validation set confirms that the Mpipi potential can ...”

Based on the reviewer’s suggestion, we have revised the text: “Our validation set, which expands the range of proteins variants originally tested [32], highlights that the Mpipi potential can effectively capture the thermodynamic behavior of a wide range of hnRNPA1-PLD variants, and suggests that Mpipi is adequate for proteins with similar sequence compositions, as in the set of proteins analyzed in this study. In recent work by others [66], Mpipi was tested against experimental radius of gyration data for 137 disordered proteins and the model produced highly accurate results, which further suggests the applicability of the approach to a broad range of sequences.”

Author response:

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

Reviewer #1 (Public review):

As a starting point, the authors discuss the so-called "additive partitioning" (AP) method proposed by Loreau & Hector in 2001. The AP is the result of a mathematical rearrangement of the definition of overyielding, written in terms of relative yields (RY) of species in mixtures relative to monocultures. One term, the so-called complementarity effect (CE), is proportional to the average RY deviations from the null expectations that plants of both species "do the same" in monocultures and mixtures. The other term, the selection effect (SE), captures how these RY deviations are related to monoculture productivity. Overall, CE measures whether relative biomass gains differ from zero when averaged across all community members, and SE, whether the "relative advantage" species have in the mixture, is related to their productivity. In extreme cases, when all species benefit, CE becomes positive.

This is not true; positive CE does not require positive RY deviations of all species. CE is positive as long as average RY deviation is greater than 0. In a 2-species mixture, for example, if the RY deviation of one species is -0.2 and that of the other species is +0.3, CE would be still positive. Positive CE can be associated with negative NE (net biodiversity effects) when more productivity species have smaller negative RY deviation compared to positive RY deviation of less productive species. Therefore, the suggestion by the reviewer “This is intuitively compatible with the idea that niche complementarity mitigates competition (CE>0)” is not correct.   

When large species have large relative productivity increases, SE becomes positive. This is intuitively compatible with the idea that niche complementarity mitigates competition (CE>0), or that competitively superior species dominate mixtures and thereby driver overyielding (SE>0).

The use of word “mitigate” indicates that the effects of niche complementarity and competition are in opposite directions, which is not true with biodiversity experiments based on replacement design. We have explained this in detail in our first responses to reviewers.    

However, it is very important to understand that CE and SE capture the "statistical structure" of RY that underlies overyielding. Specifically, CE and SE are not the ultimate biological mechanisms that drive overyielding, and never were meant to be. CE also does not describe niche complementarity. Interpreting CE and SE as directly quantifying niche complementarity or resource competition, is simply wrong, although it sometimes is done. The criticism of the AP method thus in large part seems unwarranted. The alternative methods the authors discuss (lines 108-123) are based on very similar principles.

Agree. However, If CE and SE are not meant to be biological mechanisms, as suggested by the reviewer, the argument “This is intuitively compatible with the idea that niche complementarity mitigates competition (CE>0), or that competitively superior species dominate mixtures and thereby driver overyielding (SE>0)” would be invalid.  

Lines 108-123 are not on our method.   

The authors now set out to develop a method that aims at linking response patterns to "more true" biological mechanisms.

Assuming that "competitive dominance" is key to understanding mixture productivity, because "competitive interactions are the predominant type of interspecific relationships in plants", the authors introduce "partial density" monocultures, i.e. monocultures that have the same planting density for a species as in a mixture. The idea is that using these partial density monocultures as a reference would allow for isolating the effect of competition by the surrounding "species matrix".

The authors argue that "To separate effects of competitive interactions from those of other species interactions, we would need the hypothesis that constituent species share an identical niche but differ in growth and competitive ability (i.e., absence of positive/negative interactions)." - I think the term interaction is not correctly used here, because clearly competition is an interaction, but the point made here is that this would be a zero-sum game.

We did not say that competition is not an interaction.

The authors use the ratio of productivity of partial density and full-density monocultures, divided by planting density, as a measure of "competitive growth response" (abbreviated as MG). This is the extra growth a plant individual produces when intraspecific competition is reduced.

Here, I see two issues: first, this rests on the assumption that there is only "one mode" of competition if two species use the same resources, which may not be true, because intraspecific and interspecific competition may differ. Of course, one can argue that then somehow "niches" are different, but such a niche definition would be very broad and go beyond the "resource set" perspective the authors adopt. Second, this value will heavily depend on timing and the relationship between maximum initial growth rates and competitive abilities at high stand densities.

True. Research findings indicate that biodiversity effect detected with AP is not constant.    

The authors then progress to define relative competitive ability (RC), and this time simply uses monoculture biomass as a measure of competitive ability. To express this biomass in a standardized way, they express it as different from the mean of the other species and then divide by the maximum monoculture biomass of all species.

I have two concerns here: first, if competitive ability is the capability of a species to preempt resources from a pool also accessed by another species, as the authors argued before, then this seems wrong because one would expect that a species can simply be more productive because it has a broader niche space that it exploits. This contradicts the very narrow perspective on competitive ability the authors have adopted. This also is difficult to reconcile with the idea that specialist species with a narrow niche would outcompete generalist species with a broad niche.

Competitive ability is not necessarily associated with species niche space. Both generalist and specialist species can be more productive at a particular study site, as long as they are more capable of obtaining resources from a local pool. Remember, biodiversity experiments are conducted at a site of particular conditions, not across a range of species niche space at landscape level.

Second, I am concerned by the mathematical form. Standardizing by the maximum makes the scaling dependent on a single value.

As explained in lines 370-376, the mathematical form is a linear approximation as the relationship between competitive growth responses and species relative competitive ability is generally unknow but would be likely nonlinear. Once the relationship is determined in future research, the scaling factor is not needed.    

As a final step, the authors calculate a "competitive expectation" for a species' biomass in the mixture, by scaling deviations from the expected yield by the product MG ⨯ RC. This would mean a species does better in a mixture when (1) it benefits most from a conspecific density reduction, and (2) has a relatively high biomass.

Put simply, the assumption would be that if a species is productive in monoculture (high RC), it effectively does not "see" the competitors and then grows like it would be the sole species in the community, i.e. like in the partial density monoculture.

Overall, I am not very convinced by the proposed method.

Comments on revised version:

Only minimal changes were made to the manuscript, and they do not address the main points that were raised.

Reviewer #2 (Public review):

This manuscript by Tao et al. reports on an effort to better specify the underlying interactions driving the effects of biodiversity on productivity in biodiversity experiments. The authors are especially concerned with the potential for competitive interactions to drive positive biodiversity-ecosystem functioning relationships by driving down the biomass of subdominant species. The authors suggest a new partitioning schema that utilizes a suite of partial density treatments to capture so-called competitive ability. While I agree with the authors that understanding the underlying drivers of biodiversity-ecosystem functioning relationships is valuable - I am unsure of the added value of this specific approach for several reasons.

No responses.

Comments on revised version:

The authors changed only one minor detail in response to the last round of reviews.

Reviewer #3 (Public review):

Summary:

This manuscript claims to provide a new null hypothesis for testing the effects of biodiversity on ecosystem functioning. It reports that the strength of biodiversity effects changes when this different null hypothesis is used. This main result is rather inevitable. That is, one expects a different answer when using a different approach. The question then becomes whether the manuscript's null hypothesis is both new and an improvement on the null hypothesis that has been in use in recent decades.

Our approach adopts two hypotheses, null hypothesis that is also with the additive partitioning model and competitive hypothesis that is new. Null hypothesis assumes that inter- and intra-specie interactions are the same, while competitive hypothesis assumes that species differ in competitive ability and growth rate. Therefore, our approach is an extension of current approach. Our approach separates effects of competitive interactions from those of other species interactions, while the current approach does not.      

Strengths:

In general, I appreciate studies like this that question whether we have been doing it all wrong and I encourage consideration of new approaches.

Weaknesses:

Despite many sweeping critiques of previous studies and bold claims of novelty made throughout the manuscript, I was unable to find new insights. The manuscript fails to place the study in the context of the long history of literature on competition and biodiversity and ecosystem functioning.

We have explained in our first responses that competition and biodiversity effects are studied in different experimental approaches, i.e., additive and replacement designs. Results from one approach are not compatible with those from the other. For example, competition effect with additive design is negative but generally positive with replacement design that is used extensively in biodiversity experiments. We have considered species competitive ability, density-growth relationship, and different effects of competitive interactions between additive and replacement design, while the current method does not reflect any of those.        

The Introduction claims the new approach will address deficiencies of previous approaches, but after reading further I see no evidence that it addresses the limitations of previous approaches noted in the Introduction. Furthermore, the manuscript does not reproducibly describe the methods used to produce the results (e.g., in Table 1) and relies on simulations, claiming experimental data are not available when many experiments have already tested these ideas and not found support for them.

We used simulation data, as partial density monocultures are generally not available in previous biodiversity experiments.

Finally, it is unclear to me whether rejecting the 'new' null hypothesis presented in the manuscript would be of interest to ecologists, agronomists, conservationists, or others.

Our null hypothesis is the same as the null hypothesis with the additive partitioning assuming that inter- and intra-species interactions are the same, while our competitive hypothesis assumes that species differ in competitive ability and growth rate. Rejecting null hypothesis means that inter- and intra-species interactions are different, whereas rejecting competitive hypothesis indicates existence of positive/negative species interactions. This would be interesting to everyone.       

Comments on revised version:

Please see review comments on the previous version of this manuscript. The authors have not revised their manuscript to address most of the issues previously raised by reviewers.

No responses.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Do take reviews seriously. Even if you think the reviewers all are wrong and did not understand your work, then this seems to indicate that it was not clearly presented.

Reviewer #2 (Recommendations for the authors):

I can understand that the authors are perhaps frustrated with what they perceive as a basic misunderstanding of their goals and approach. This misunderstanding however, provides with it an opportunity to clarify. I believe that the authors have tried to clarify in rebutting our statements but would do better to clarify in the manuscript itself. If we reviewers, who are deeply invested in this field, don't understand the approach and its value, then it is likely that many readers will not as well.

The additive partitioning has been publicly questioned at least for serval times since the conception of the method in 2001. Our work provides an alternative.

Author response:

We thank the editor and the three reviewers for the positive assessment and constructive feedback on how to improve our manuscript. We greatly appreciate that our work is considered valuable to the field, the recognition of the high-resolution model we presented, and the comments on our investigation of CisA’s role in the attachment and firing mechanism of the extended assembly. It is truly gratifying to know that our study contributes to expanding the current understanding of the biology of Streptomyces and the role of these functionally diverse and fascinating bacterial nanomachines.

We have provided specific responses to each reviewer's comments below. In summary, we intend to address the following requested revisions:

We will expand our bioinformatic analysis of CisA and provide additional information on the oligomeric state of CisA. We will also modify the text, figures, and figure legends to improve the clarity of our work and experimental procedures.

Some reviewer comments would require additional experimental work, some of which would involve extensive optimization of experimental conditions. Because both lead postdoctoral researchers involved in this work have now left the lab, we currently do not have the capability to perform additional experimental work.

Reviewer #1 (Public review):

Contractile Injection Systems (CIS) are versatile machines that can form pores in membranes or deliver effectors. They can act extra or intracellularly. When intracellular they are positioned to face the exterior of the cell and hence should be anchored to the cell envelope. The authors previously reported the characterization of a CIS in Streptomyces coelicolor, including significant information on the architecture of the apparatus. However, how the tubular structure is attached to the envelope was not investigated. Here they provide a wealth of evidence to demonstrate that a specific gene within the CIS gene cluster, cisA, encodes a membrane protein that anchors the CIS to the envelope. More specifically, they show that:

- CisA is not required for assembly of the structure but is important for proper contraction and CIS-mediated cell death

- CisA is associated to the membrane (fluorescence microscopy, cell fractionation) through a transmembrane segment (lacZ-phoA topology fusions in E. coli)

- Structural prediction of interaction between CisA and a CIS baseplate component<br /> - In addition they provide a high-resolution model structure of the >750-polypeptide Streptomyces CIS in its extended conformation, revealing new details of this fascinating machine, notably in the baseplate and cap complexes.

All the experiments are well controlled including trans-complemented of all tested phenotypes.

One important information we miss is the oligomeric state of CisA.

While it would have been great to test the interaction between CisA and Cis11, to perform cryo-electron microscopy assays of detergent-extracted CIS structures to maintain the interaction with CisA, I believe that the toxicity of CisA upon overexpression or upon expression in E. coli render these studies difficult and will require a significant amount of time and optimization to be performed. It is worth mentioning that this study is of significant novelty in the CIS field because, except for Type VI secretion systems, very few membrane proteins or complexes responsible for CIS attachment have been identified and studied.

We thank this reviewer for their highly supportive and positive comments on our manuscript. We are grateful for this reviewer’s recognition of the novelty of our study, particularly in the context of membrane proteins and complexes involved in CIS attachment.

We agree that further experimental evidence on the direct interaction between CisA and Cis11 would have strengthened our model of CisA function. However, as noted by this reviewer, this additional work is technically challenging and currently beyond the scope of this study.

We thank Reviewer #1 for suggesting discussing the potential oligomeric state of CisA. We will perform additional AlphaFold modelling of CisA and discuss the result of this analysis in the revised manuscript.

Reviewer #2 (Public review):

Summary:

The overall question that is addressed in this study is how the S. coelicolor contractile injection system (CISSc) works and affects both cell viability and differentiation, which it has been implicated to do in previous work from this group and others. The CISSc system has been enigmatic in the sense that it is free-floating in the cytoplasm in an extended form and is seen in contracted conformation (i.e. after having been triggered) mainly in dead and partially lysed cells, suggesting involvement in some kind of regulated cell death. So, how do the structure and function of the CISSc system compare to those of related CIS from other bacteria, does it interact with the cytoplasmic membrane, how does it do that, and is the membrane interaction involved in the suggested role in stress-induced, regulated cell death? The authors address these questions by investigating the role of a membrane protein, CisA, that is encoded by a gene in the CIS gene cluster in S. coelicolor. Further, they analyse the structure of the assembled CISSc, purified from the cytoplasm of S. coelicolor, using single-particle cryo-electron microscopy.

Strengths:

The beautiful visualisation of the CIS system both by cryo-electron tomography of intact bacterial cells and by single-particle electron microscopy of purified CIS assemblies are clearly the strengths of the paper, both in terms of methods and results. Further, the paper provides genetic evidence that the membrane protein CisA is required for the contraction of the CISSc assemblies that are seen in partially lysed or ghost cells of the wild type. The conclusion that CisA is a transmembrane protein and the inferred membrane topology are well supported by experimental data. The cryo-EM data suggest that CisA is not a stable part of the extended form of the CISSc assemblies. These findings raise the question of what CisA does.

We thank Reviewer #2 for the overall positive evaluation of our manuscript and the constructive criticism. 

Weaknesses:

The investigations of the role of CisA in function, membrane interaction, and triggering of contraction of CIS assemblies, are important parts of the paper and are highlighted in the title. However, the experimental data provided to answer these questions appear partially incomplete and not as conclusive as one would expect.

We acknowledge that some aspects of our work have not been fully answered. We believe that providing additional experimental data is currently beyond the scope of this study. To improve this study, we will modify the text and clarify experimental procedures and figures where possible in the revised version of our manuscript.

The stress-induced loss of viability is only monitored with one method: an in vivo assay where cytoplasmic sfGFP signal is compared to FM5-95 membrane stain. Addition of a sublethal level of nisin lead to loss of sfGFP signal in individual hyphae in the WT, but not in the cisA mutant (similarly to what was previously reported for a CIS-negative mutant). Technically, this experiment and the example images that are shown give rise to some concern. Only individual hyphal fragments are shown that do not look like healthy and growing S. coelicolor hyphae. Under the stated growth conditions, S. coelicolor strains would normally have grown as dense hyphal pellets. It is therefore surprising that only these unbranched hyphal fragments are shown in Fig. 4ab.

We thank Reviewer #2 for their thoughtful criticism regarding our stress-induced viability assay and the data presented in Figure 4. We acknowledge the importance of ensuring that the presented images should reflect the physiological state of S. coelicolor under the stated growth conditions and recognize that hyphal fragments shown in Figure 4 do not fully capture the typical morphology of S. coelicolor. As pointed out by this reviewer, S. coelicolor grows in large hyphal clumps when cultured in liquid media, making the quantification of fluorescence intensities in hyphae expressing cytoplasmic GFP and stained with the membrane dye FM5-95 particularly challenging. To improve the image analysis and quantification of GFP and FM5-95-fluorescent intensities across the three S. coelicolor strains (wildtype, cisA deletion mutant and the complemented cisA mutant), we vortexed the cell samples briefly before imaging to break up hyphal clumps, increasing hyphal fragments. The hyphae shown in our images were selected as representative examples across three biological replicates. 

Further, S. coelicolor would likely be in a stationary phase when grown 48 h in the rich medium that is stated, giving rise to concern about the physiological state of the hyphae that were used for the viability assay. It would be valuable to know whether actively growing mycelium is affected in the same way by the nisin treatment, and also whether the cell death effect could be detected by other methods.

The reasoning behind growing S. coelicolor for 48 h before performing the fluorescence-based viability assay was that we (DOI: 10.1038/s41564-023-01341-x ) and others (e.g.: DOI: 10.1038/s41467-023-37087-7 ) previously showed that the levels of CIS particles peak at the transition from vegetative to reproductive/stationary growth, thus indicating that CIS activity is highest during this growth stage. The obtained results in this manuscript are in agreement with our previous study, in which we showed a similar effect on the viability of wildtype versus cis-deficient S. coelicolor strains (DOI: 10.1038/s41564-023-01341-x ) using nisin, the protonophore CCCP and UV light, and supported by biological replicate experiments and appropriate controls. Furthermore, our results are in agreement with the findings reported in a complementary study by Vladimirov et al. (DOI: 10.1038/s41467-023-37087-7 ) that used a different approach (SYTO9/PI staining of hyphal pellets) to demonstrate that CIS-deficient mutants exhibit decreased hyphal death. We agree that it would be interesting to test if actively growing hyphae respond differently to nisin treatment, and such experiments will be considered in future work. 

Taken together, we believe that the results obtained from our fluorescence-based viability assay are consistent with data reported by others and provide strong experimental evidence that functional CIS mediate hyphal cell death. 

The model presented in Fig. 5 suggests that stress leads to a CisA-dependent attachment of CIS assemblies to the cytoplasmic membrane, and then triggering of contraction, leading to cell death. This model makes testable predictions that have not been challenged experimentally. Given that sublethal doses of nisin seem to trigger cell death, there appear to be possibilities to monitor whether activation of the system (via CisA?) indeed leads to at least temporally increased interaction of CIS with the membrane.

We thank this reviewer for their suggestions on how to test our model further. In the meantime, we have performed co-immunoprecipitation experiments using S. coelicolor cells that produced CisA-FLAG as bait and were treated with a sub-lethal nisin concentration for 0/15/45 min.  Mass spectrometry analysis of co-eluted peptides did not show the presence of CIS-associated peptides. While we cannot exclude the possibility that our experimental assay requires further optimization to successfully demonstrate a CisA-CIS interaction (e.g. optimization of the use of detergents to improve the solubilization of CisA from Streptomyces membrane, which is currently not an established method), an alternative and equally valid hypothesis is that the interaction between CIS particles and CisA is transient and therefore difficult to capture. We would like to mention that we did detect CisA peptides in crude purifications of CIS particles from nisin-stressed cells (Supplementary Table 2, manuscript: line 265/266), supporting our model that CisA associates with CIS particles in vivo.

Further, would not the model predict that stress leads to an increased number of contracted CIS assemblies in the cytoplasm? No clear difference in length of the isolated assemblies if Fig. S7 is seen between untreated and nisin-exposed cells, and also no difference between assemblies from WT and cisA mutant hyphae.

The reviewer is correct that there is no clear difference in length in the isolated CIS particles shown in Figure S7. This is in line with our results, which show that CisA is not required for the correct assembly of CIS particles and their ability to contract in the presence and absence of nisin treatment. The purpose of Figure S7 was to support this statement. We would like to note that the particles shown in Figure S7 were purified from cell lysates using a crude sheath preparation protocol, during which CIS particles generally contract irrespective of the presence or absence of CisA. Thus, we cannot comment on whether there is an increased number of contracted CIS assemblies in the cytoplasm of nisin-exposed cells. To answer this point, we would need to acquire additional cryo-electron tomograms (cyroET) of the different strains treated with nisin. We appreciate this reviewer's suggestions. However, cryoET is an extremely time and labour-intensive task, and given that we currently don’t know the exact dynamics of the CIS-CisA interaction following exogenous stress, we believe this experiment is beyond the scope of this work.

The interaction of CisA with the CIS assembly is critical for the model but is only supported by Alphafold modelling, predicting interaction between cytoplasmic parts of CisA and Cis11 protein in the baseplate wedge. An experimental demonstration of this interaction would have strengthened the conclusions.

We agree that direct experimental evidence of this interaction would have further strengthened the conclusions of our study, and we have extensively tried to provide additional experimental evidence. Unfortunately, due to the toxicity of CisA expression in E. coli and the transient nature of the interaction under our experimental conditions, we were unable to pursue direct biochemical or biophysical validation methods, such as co-purification or bacterial two-hybrid assays. While these challenges limited our ability to experimentally confirm the interaction, the AlphaFold predictions provided a valuable hypothesis and mechanistic insight into the role of CisA.

The cisA mutant showed a similarly accelerated sporulation as was previously reported for CIS-negative strains, which supports the conclusion that CisA is required for function of CISSc. But the results do not add any new insights into how CIS/CisA affects the progression of the developmental life cycle and whether this effect has anything to do with the regulated cell death that is caused by CIS. The same applies to the effect on secondary metabolite production, with no further mechanistic insights added, except reporting similar effects of CIS and CisA inactivations.

We thank this reviewer for their thoughtful feedback and for highlighting the connections between CisA, CIS function, and their effects on the developmental life cycle and secondary metabolite production in S. coelicolor. The main focus of this study was to provide further insight into how CIS contraction and firing are mediated in Streptomyces, and we used the analysis of accelerated sporulation and secondary metabolite production to assess the functionality of CIS in the presence or absence of CisA.

We agree that we still don’t fully understand the nature of the signals that trigger CIS contraction, but we do know that the production of CIS assemblies seems to be an integral part of the Streptomyces multicellular life cycle as demonstrated in two independent previous studies (DOI: 10.1038/s41564-023-01341-x and DOI: 10.1038/s41467-023-37087-7 ). We propose that the assembly and firing of Streptomyces CIS particles could present a molecular mechanism to sacrifice only a part of the mycelium to either prevent the spread of local cellular damage or to provide additional nutrients for the rest of the mycelium and delay the terminal differentiation into spores and affect the production of secondary metabolites.

We recognize the importance of understanding the regulation and mechanistic details underpinning the proposed CIS-mediated regulated cell death model. This will be further explored in future studies.

Concluding remarks:

The work will be of interest to anyone interested in contractile injection systems, T6SS, or similar machineries, as well for people working on the biology of streptomycetes. There is also a potential impact of the work in the understanding of how such molecular machineries could have been co-opted during evolution to become a mechanism for regulated cell death. However, this latter aspect remains still poorly understood. Even though this paper adds excellent new structural insights and identifies a putative membrane anchor, it remains elusive how the Streptomyces CIS may lead to cell death. It is also unclear what the advantage would be to trigger death of hyphal compartments in response to stress, as well as how such cell death may impact (or accelerate) the developmental progression. Finally, it is inescapable to wonder whether the Streptomyces CIS could have any role in protection against phage infection.

We thank Reviewer #2 for their supportive assessment of our work. In the revised manuscript, we will briefly discuss the impact of functional CIS assemblies on Streptomyces development. We previously tested if Streptomyces could defend against phages but have not found any experimental evidence to support this idea. The analysis of phage defense mechanisms is an underdeveloped area in Streptomyces research, partly due to the currently limited availability of a diverse phage panel.

Reviewer #3 (Public review):

Summary:

In this work, Casu et al. have reported the characterization of a previously uncharacterized membrane protein CisA encoded in a non-canonical contractile injection system of Streptomyces coelicolor, CISSc, which is a cytosolic CISs significantly distinct from both intracellular membrane-anchored T6SSs and extracellular CISs. The authors have presented the first high-resolution structure of extended CISSc structure. It revealed important structural insights in this conformational state. To further explore how CISSc interacted with cytoplasmic membrane, they further set out to investigate CisA that was previously hypothesized to be the membrane adaptor. However, the structure revealed that it was not associated with CISSc. Using fluorescence microscope and cell fractionation assay, the authors verified that CisA is indeed a membrane-associated protein. They further determined experimentally that CisA had a cytosolic N-terminal domain and a periplasmic C-terminus. The functional analysis of cisA mutant revealed that it is not required for CISSc assembly but is essential for the contraction, as a result, the deletion significantly affects CISSc-mediated cell death upon stress, timely differentiation, as well as secondary metabolite production. Although the work did not resolve the mechanistic detail how CisA interacts with CISSc structure, it provides solid data and a strong foundation for future investigation toward understanding the mechanism of CISSc contraction, and potentially, the relation between the membrane association of CISSc, the sheath contraction and the cell death.

Strengths:

The paper is well-structured, and the conclusion of the study is supported by solid data and careful data interpretation was presented. The authors provided strong evidence on (1) the high-resolution structure of extended CISSc determined by cryo-EM, and the subsequent comparison with known eCIS structures, which sheds light on both its similarity and different features from other subtypes of eCISs in detail; (2) the topological features of CisA using fluorescence microscopic analysis, cell fractionation and PhoA-LacZα reporter assays, (3) functions of CisA in CISSc-mediated cell death and secondary metabolite production, likely via the regulation of sheath contraction.

Weaknesses:

The data presented are not sufficient to provide mechanistic details of CisA-mediated CISSc contraction, as authors are not able to experimentally demonstrate the direct interaction between CisA with baseplate complex of CISSc (hypothesized to be via Cis11 by structural modeling), since they could not express cisA in E. coli due to its potential toxicity. Therefore, there is a lack of biochemical analysis of direct interaction between CisA and baseplate wedge. In addition, there is no direct evidence showing that CisA is responsible for tethering CISSc to the membrane upon stress, and the spatial and temporal relation between membrane association and contraction remains unclear. Further investigation will be needed to address these questions in future.

We thank Reviewer #3 for the supportive evaluation and constructive criticism of our study in the public and non-public review. We appreciate your recognition of the technical limitations of experimentally demonstrating a direct interaction between CisA and CIS baseplate complex, and we agree that further investigations in the future will hopefully provide a full mechanistic understanding of the spatiotemporal interaction of CisA and CIS particular and the subsequent CIS firing.

To further improve the manuscript, we will revise the text and clarify figures and figure legends as suggested in the non-public review.

Discussion:

Overall, the work provides a valuable contribution to our understanding on the structure of a much less understood subtype of CISs, which is unique compared to both membrane-anchored T6SSs and host-membrane targeting eCISs. Importantly, the work serves as a good foundation to further investigate how the sheath contraction works here. The work contributes to expanding our understanding of the diverse CIS superfamilies.

Thank you.

Author response:

Both reviewers made thoughtful and constructive comments, suggesting improvements that we are keen to provide. The comments fall under 3 headings (1) Further validation of the design, regarding both optical performance and utility, for both education and research (2) Further description and facilitation of the build process and (3) Further description of future plans, in particular plans for dissemination and long-term support. We think these requirements will be best served by adding new content to our Github site and our YouTube channel. We will create this new content and provide a revised manuscript in which these materials are linked from our existing narrative.

Author response:

Reviewer #1 (Public review):

Summary:

The authors showed the presence of Mtb in human liver biopsy samples of TB patients and reported that chronic infection of Mtb causes immune-metabolic dysregulation. Authors showed that Mtb replicates in hepatocytes in a lipid rich environment created by up regulating transcription factor PPARγ. Authors also reported that Mtb protects itself from anti-TB drugs by inducing drug metabolising enzymes.

Strengths:

It has been shown that Mtb induces storage of triacylglycerol in macrophages by induction of WNT6/ACC2 which helps in its replication and intracellular survival, however, creation of favorable replicative niche in hepatocytes by Mtb is not reported. It is known that Mtb infects macrophages and induces formation of lipid-laden foamy macrophages which eventually causes tissue destruction in TB patients. In a recent article it has been reported that "A terpene nucleoside from M. tuberculosis induces lysosomal lipid storage in foamy macrophages" that shows how Mtb manipulates host defense mechanisms for its survival. In this manuscript, authors reported the enhancement of lipid droplets in Mtb infected hepatocytes and convincingly showed that fatty acid synthesis and triacylglycerol formation is important for growth of Mtb in hepatocytes. The authors also showed the molecular mechanism for accumulation of lipid and showed that the transcription factor associated with lipid biogenesis, PPARγ and adipogenic genes were upregulated in Mtb infected cells.

The comparison of gene expression data between macrophages and hepatocytes by authors is important which indicates that Mtb modulates different pathways in different cell type as in macrophages it is related to immune response whereas, in hepatocytes it is related to metabolic pathways.

Authors also reported that Mtb residing in hepatocytes showed drug tolerance phenotype due to up regulation of enzymes involved in drug metabolism and showed that cytochrome P450 monooxygenase that metabolize rifampicin and NAT2 gene responsible for N-acetylation of isoniazid were up regulated in Mtb infected cells.

We thank the reviewer for the positive feedback and for highlighting the strengths of our study.

Weaknesses:

There are reports of hepatic tuberculosis in pulmonary TB patients especially in immune-compromised patients, therefore finding granuloma in human liver biopsy samples is not surprising.

Mtb infected hepatic cells showed induced DME and NAT and this could lead to enhanced metabolism of drug by hepatic cells as a result Mtb in side HepG2 cells get exposed to reduced drug concentration and show higher tolerance to drug. The authors mentioned that " hepatocyte resident Mtb may display higher tolerance to rifampicin". In my opinion higher tolerance to drugs is possible only when DME of Mtb inside is up regulated or the target is modified. Although, in the end authors mentioned that drug tolerance phenotype can be better attributed to host intrinsic factors rather than Mtb efflux pumps. It may be better if the Drug tolerant phenotype section can be rewritten to clarify the facts.

We agree that several case studies regarding liver infection in pulmonary TB patients have been reported in the literature, however this report is the first comprehensive study that establishes hepatocytes to be a favourable niche for Mtb survival and growth.

Drug tolerance is a phenomenon that is exhibited by the bacteria and in the course of host-pathogen interactions, can be influenced by both intrinsic (bacterial) and extrinsic (host-mediated) factors. Multiple examples of tolerance being attributed to host driven factors can be found in literature (PMID 32546788, PMID: 28659799, PMID: 32846197). Our studies demonstrate that Mtb infected hepatocytes create a drug tolerant environment by modulating the expression of Drug modifying enzymes (DMEs) in the hepatocytes.

As suggested by the reviewer we will rewrite the drug tolerant phenotype section.

Reviewer #2 (Public review):

The manuscript by Sarkar et al has demonstrated the infection of liver cells/hepatocytes with Mtb and the significance of liver cells in the replication of Mtb by reprogramming lipid metabolism during tuberculosis. Besides, the present study shows that similar to Mtb infection of macrophages (reviewed in Chen et al., 2024; Toobian et al., 2021), Mtb infects liver cells but with a greater multiplication owing to consumption of enhanced lipid resources mediated by PPARg that could be cleared by its inhibitors. The strength of the study lies in the clinical evaluation of the presence of Mtb in human autopsied liver samples from individuals with miliary tuberculosis and the presence of a clear granuloma-like structure. The interesting observation is of granuloma-like structure in liver which prompts further investigations in the field.

The modulation of lipid synthesis during Mtb infection, such as PPARg upregulation, appears generic to different cell types including both liver cells and macrophage cells. It is also known that infection affect PPARγ expression and activity in hepatocytes. It is also known that this can lead to lipid droplet accumulation in the liver and the development of fatty liver disease (as shown for HCV). This study is in a similar line for M.tb infection. As the liver is the main site for lipid regulation, the availability of lipid resources is greater and higher is the replication rate. In short, the observations from the study confirm the earlier studies with these additional cell types. It is known that higher the lipid content, the greater are Lipid Droplet-positive Mtb and higher is the drug resistance (Mekonnen et al., 2021). The DMEs of liver cells add further to the phenotype.

We thank the reviewer for emphasizing on the strengths of our study and how it can lead to further investigations in the field.

Reviewer #3 (Public review):

This manuscript by Sarkar et al. examines the infection of the liver and hepatocytes during M. tuberculosis infection. They demonstrate that aerosol infection of mice and guinea pigs leads to appreciable infection of the liver as well as the lung. Transcriptomic analysis of HepG2 cells showed differential regulation of metabolic pathways including fatty acid metabolic processing. Hepatocyte infection is assisted by fatty acid synthesis in the liver and inhibiting this caused reduced Mtb growth. The nuclear receptor PPARg was upregulated by Mtb infection and inhibition or agonism of its activity caused a reduction or increase in Mtb growth, respectively, supporting data published elsewhere about the role of PPARg in lung macrophage Mtb infection. Finally, the authors show that Mtb infection of hepatocytes can cause upregulation of enzymes that metabolize antibiotics, resulting in increased tolerance of these drugs by Mtb in the liver.

Overall, this is an interesting paper on an area of TB research where we lack understanding. However, some additions to the experiments and figures are needed to improve the rigor of the paper and further support the findings. Most importantly, although the authors show that Mtb can infect hepatocytes in vitro, they fail to describe how bacteria get from the lungs to the liver in an aerosolized infection. They also claim that "PPARg activation resulting in lipid droplets formation by Mtb might be a mechanism of prolonging survival within hepatocytes" but do not show a direct interaction between PPARg activation and lipid droplet formation and lipid metabolism, only that PPARg promotes Mtb growth. Thus, the correlations with PPARg appear to be there but causation, implied in the abstract and discussion, is not proven.

The human photomicrographs are important and overall, well done (lung and liver from the same individuals is excellent). However, in lines 120-121, the authors comment on the absence of studies on the precise involvement of different cells in the liver. In this study there is no attempt to immunophenotype the nature of the cells harboring Mtb in these samples (esp. hepatocytes). Proving that hepatocytes specifically harbor the bacteria in these human samples would add significant rigor to the conclusions made.

We thank the reviewer for nicely summarizing our manuscript.

Our study establishes the involvement of liver and hepatocytes in pulmonary TB infection in mice. Understanding the mechanism of bacterial dissemination from the lung to the liver in aerosol infections demands a detailed separate study.

Figure 6E and 6F shows how PPARγ agonist and antagonist modulate (increase and decrease respectively) bacterial growth in hepatocytes (further supported by the CFU data in Supplementary Figure 9B). Again, the number of lipid droplets in hepatocytes increase and decrease with the application of PPARγ agonist and antagonist respectively as shown in Figure 6G and 6H. Collectively, these studies provide strong evidence that PPARγ activation leads to more lipid droplets that support better Mtb growth.

We thank the reviewer for finding our human photomicrographs convincing. In the manuscript, we provide evidence for the direct involvement of the hepatocytes (and liver) in Mtb infection. We perform detailed immunophenotyping of hepatocyte cells in the mice model with ASPGR1 (asialoglycoprotein receptor 1) and in the revised version of record, we will further stain the infected hepatocytes with anti-albumin antibody.

Author response:

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

Reviewer #3:

Concerns and comments on current version:

The revision has improved the manuscript but, in my opinion, remains inadequate. While most of my requested changes have been made, I do not see an expansion of Fig1A legend to incorporate more details about the analysis. Lacking details of methodology was a concern from all reviewers.

To address this concern, we expanded Fig.1A legend, and also significantly expanded the text describing experimental design, to also include the description of the data analysis approach.

“BCR repertoires libraries were obtained using the 5’-RACE (Rapid Amplification of cDNA Ends) protocol as previously described21 and sequenced with 150+150 bp read length. This approach allowed us to achieve high coverage for the obtained libraries (Table S1) to reveal information on clonal composition, CDR-H3 properties, IgM/IgG/IgA isotypes and somatic hypermutation load within CDR-H3. For B cell clonal lineage reconstruction and phylogenetic analysis, however, 150+150 bp read length is suboptimal because it does not cover V-gene region outside CDR-H3, where hypermutations also occur. Therefore, to verify our conclusions based on the data obtained by 150+150 bp sequencing (“short repertoires”), for some of our samples we also generated BCR libraries by IG RNA Multiplex protocol (See Materials and Methods) and sequenced them at 250+250 bp read length (“long repertoires”). Libraries obtained by this protocol cover V gene sequence starting from CDR-H1 and capture most of the hypermutations in the V gene. Conclusions about clonal lineage phylogeny were drawn only when they were corroborated by “long repertoire” analysis.

For BCR repertoire reconstruction from sequencing data, we first performed unique molecular identifier (UMI) extraction and error correction (reads/UMI threshold = 3 for 5`RACE and 4 for IG Multiplex libraries). Then, we used MIXCR58 software to assemble reads into clonotypes, determine germline V, D, and J genes, isotypes, and find the boundaries of target regions, such as CDR-H3. Only

UMI counts, and not read counts, were used for quantitative analysis. Clonotypes derived from only one UMI were excluded from the analysis of individual clonotype features but were used to analyze clonal lineages and hypermutation phylogeny, where sample size was crucial. Samples with 50 or less clonotypes left after preprocessing were excluded from the analysis.”

Similarly, the 'fragmented' narrative was a concern of all reviewers. These matters have not been dealt with adequately enough - there are parts of the manuscript which remain fragmented and confusing.

Unfortunately, the reviewers do not give us a hint as to which parts of the text are the most problematic in their opinion. We identified the parts describing physicochemical properties of CDR3s, Intratumoral heterogeneity and Intra-LN heterogeneity as the most problematic, and edited these parts significantly. Also, we significantly edited the Discussion section (please see the Comparison file for details). Other parts sections were also edited to improve readability and clarity.

The narrative and analysis does not explain how the plasma cell bias has been dealt with adequately and in fact is simply just confusing. There is a paragraph at the beginning of the discussion re the plasma cell bias, which should be re-written to be clearer and moved to have a prominent place early in the results. Why are these results not properly presented? They are key for interpretation of the manuscript. Furthermore, the sorted plasma cell sequencing analysis also has only been performed on two patients.

In response to this concern, we moved the section describing plasma cell bias in the bulk BCR repertoires to the main text.

Another issue is that some disease cohorts are entirely composed of patients with metastasis, some without but metastasis is not mentioned. Metastasis has been shown to impact the immune landscape.

Intrinsic heterogeneity of the cohort is indeed one of the weaknesses of our work, which could negatively impact the statistical significance of our results and, as a consequence, mask certain observations or make them less statistically significant. We mention this in the discussion section. It should not, in our understanding, lead to any false conclusions. We did not, however, pool data from primary and metastatic tumor samples, and all tumor samples that we mention are primary tumors.

The following part of a sentence was added to the discussion:

“...which could negatively impact the statistical significance of our results and, as a consequence, mask certain observations or make them less statistically significant.”

A reviewer brought up a concern about the overlap analysis and I also asked for an explanation on why this F2 metric was chosen. Part of the rebuttal argues that another metric was explored showing similar results, thus the conclusion reached is reasonable. Remarkably, these data are not only omitted from the manuscript, but are not even provided for the reviewers.

We did not intend to conceal any data from the reviewers, and we now added the panel for D metric to the S1 figure. We would also like to point out that the panel describing R metric for repertoire overlaps (a measure of similarity of overlapping clonotype frequencies), was included in the first version of the S2 Figure (now S1 Figure), and it also showed a similar trend. We hope that now the data are fully conclusive.

This manuscript certainly includes some interesting and useful work. Unfortunately, a comprehensive re-write was required to make the work much clearer and easier to understand and this has not been realized.

Again, we thank the reviewers for their thorough evaluation, and hopefully we could make the text clearer in the second reviewed version.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, a screening platform is presented for rapid and cost-effective screening of candidate genes involved in Fragile Bone Disorders. The authors validate the approach of using crispants, generating FO mosaic mutants, to evaluate the function of specific target genes in this particular condition. The design of the guide RNAs is convincingly described, while the effectiveness of the method is evaluated to 60% to 92% of the respective target genes being presumably inactivated. Thus, injected F0 larvae can be directly used to investigate the consequences of this inactivation.

Skeletal formation is then evaluated at 7dpf and 14dpf, first using a transgenic reporter line revealing fluorescent osteoblasts, and second using alizarin-red staining of mineralized structures. In general, it appears that the osteoblast-positive areas are more often affected in the crispants compared to the mineralized areas, an observation that appears to correlate with the observed reduced expression of bglap, a marker for mature osteoblasts, and the increased expression of col1a1a in more immature osteoblasts.

Finally, the injected fish (except two lines that revealed high mortality) are also analyzed at 90dpf, using alizarin red staining and micro-CT analysis, revealing an increased incidence of skeletal deformities in the vertebral arches, fractures, as well as vertebral fusions and compressions for all crispants except those for daam2. Finally, the Tissue Mineral Density (TMD) as determined by micro-CT is proposed as an important marker for investigating genes involved in osteoporosis.

Taken together, this manuscript is well presented, the data are clear and well analyzed, and the methods are well described. It makes a compelling case for using the crispant technology to screen the function of candidate genes in a specific condition, as shown here for bone disorders.

Strengths:

Strengths are the clever combination of existing technologies from different fields to build a screening platform. All the required methods are comprehe Zebrafish tanks_13062024nsively described.

We would like to thank the reviewer for highlighting the strengths of our paper.  

Weaknesses:

One may have wished to bring one or two of the crispants to the stage of bona fide mutants, to confirm the results of the screening, however, this is done for some of the tested genes as laid out in the discussion.

We thank the reviewer for their comment. We would like to point out that indeed similar phenotypes have been observed in existing models, as mentioned in the discussion section.

Reviewer #2 (Public review):

Summary:

More and more genes and genetic loci are being linked to bone fragility disorders like osteoporosis and osteogenesis imperfecta through GWAS and clinical sequencing. In this study, the authors seek to develop a pipeline for validating these new candidate genes using crispant screening in zebrafish. Candidates were selected based on GWAS bone density evidence (4 genes) or linkage to OI cases plus some aspect of bone biology (6 genes). NGS was performed on embryos injected with different gRNAs/Cas9 to confirm high mutagenic efficacy and off-target cutting was verified to be low. Bone growth, mineralization, density, and gene expression levels were carefully measured and compared across crispants using a battery of assays at three different stages.

Strengths:

(1) The pipeline would be straightforward to replicate in other labs, and the study could thus make a real contribution towards resolving the major bottleneck of candidate gene validation.

(2) The study is clearly written and extensively quantified.

(3) The discussion attempts to place the phenotypes of different crispant lines into the context of what is already known about each gene's function.

(4) There is added value in seeing the results for the different crispant lines side by side for each assay.

We would like to thank the reviewer for highlighting the strengths of our paper.  

Weaknesses:

(1) The study uses only well-established methods and is strategy-driven rather than question/hypothesis-driven.

We thank the reviewer for this correct remark. The mayor aim of this study was to establish a workflow for rapid in vivo functional screening of candidate genes across a broad range of FBDs. 

(2) Some of the measurements are inadequately normalized and not as specific to bone as suggested:

(a) The measurements of surface area covered by osteoblasts or mineralized bone (Figure 1) should be normalized to body size. The authors note that such measures provide "insight into the formation of new skeletal tissue during early development" and reflect "the quantity of osteoblasts within a given structure and [is] a measure of the formation of bone matrix." I agree in principle, but these measures are also secondarily impacted by the overall growth and health of the larva. The surface area data are normalized to the control but not to the size/length of each fish - the esr1 line in particular appears quite developmentally advanced in some of the images shown, which could easily explain the larger bone areas. The fact that the images in Figure S5 were not all taken at the same magnification further complicates this interpretation.

We thank the reviewer for this detailed and insightful remark. We agree with the reviewer and recognize that the results may be influenced by size differences. However, we do not normalize for size, as variations in growth were considered as part of the phenotypic outcome. This consideration has been addressed in the discussion section.

Line 335-338: ‘Although the measurements of osteoblast-positive and mineralized surface areas may be influenced by size differences among some of the crispants, normalization to size parameters was not conducted, as variations in growth were considered integral to the phenotypic outcome.’

Line 369: ‘Phenotypic variability in these zebrafish larvae can be attributed to several factors, including crispant mosaicism, allele heterogeneity, environmental factors, differences in genomic background and development, and slightly variable imaging positioning.’

(b) Some of the genes evaluated by RT-PCR in Figure 2 are expressed in other tissues in addition to bone (as are the candidate genes themselves); because whole-body samples were used for these assays, there is a nonzero possibility that observed changes may be rooted in other, non-skeletal cell types.

We thank the reviewer for this valuable comment. We acknowledge that the genes assessed by RT-PCR are expressed in other tissues beyond bone. This consideration has been addressed in the discussion section.

Line 362-365: “However, it is important to note that the genes evaluated by RT-PCR are not exclusively expressed in bone tissue. Since whole-body samples were used for expression analysis, there is a possibility that the observed changes in gene expression may be influenced by other non-skeletal cell types”.

(3) Though the assays evaluate bone development and quality at several levels, it is still difficult to synthesize all the results for a given gene into a coherent model of its requirement.

We appreciate the reviewer’s  remark. We acknowledge that the results for the larval stages exhibit variability, making it challenging to synthesize them into a coherent model. However, it is important to emphasize that all adult crispant consistently display a skeletal phenotype. Consequently, the feasibility and reproducibility of this screening method are primarily focusing on the adult stages. This consideration has been addressed in the discussion section of the manuscript.

Line 391-399: ‘In adult crispants, the skeletal phenotype was generally more penetrant. All crispants showed malformed arches, a majority displayed vertebral fractures and fusions and some crispants exhibited distinct quantitative variations in vertebral body measurements. This confirmed the role of the selected genes in skeletal development and homeostasis and their involvement in skeletal disease and established the crispant approach as a valid approach for rapidly providing in vivo gene function data to support candidate gene identification.’

(4) Several additional caveats to crispant analyses are worth noting:

(a) False negatives, i.e. individual fish may not carry many (or any!) mutant alleles. The crispant individuals used for most assays here were not directly genotyped, and no control appears to have been used to confirm successful injection. The authors therefore cannot rule out that some individuals were not, in fact, mutagenized at the loci of interest, potentially due to human error. While this doesn't invalidate the results, it is worth acknowledging the limitation.

We thank the reviewer for this valuable remark. We recognize the fact that working with crispants has certain limitations, including the possibility that some individuals may carry few or no mutant alleles. To address this issue, we use 10 individual crispants during the larval stage and 5 during the adult stage. Although some individuals may lack the mutant alleles, using multiple fish helps reduce the risk of false negatives.

Furthermore, we perform NGS analysis on pools of 10 embryos from the same injection clutch as the fish used in the various assays to assess the indel efficiency. While there remains a possibility of false negatives, the overall indel efficiency, as indicated by our NGS analysis,  is high (>90%), thereby reducing the likelihood of having crispants with very low indel efficiency. We included this in the discussion.

Line 387-390: ‘While there remains a possibility of false negatives, the overall indel efficiency, as indicated by our NGS analysis,  is high (>90%), thereby reducing the likelihood of having crispants with very low indel efficiency.’

(b) Many/most loci identified through GWAS are non-coding and not easily associated with a nearby gene. The authors should discuss whether their coding gene-focused pipeline could be applied in such cases and how that might work.

The authors thank the reviewer for this insightful comment. Our study is focused on strong candidate genes rather than non-coding variants. We recognize that the use of this workflow poses challenges for analyzing non-coding variants, which represents a limitation of the crispant approach. We have addressed this issue in the discussion section of the manuscript.

Line 131: ‘Gene-based’

Line 453: ‘Gene-based’

Line 311-314: ‘It is important to note that this study focused on candidate genes for osteoporosis, not on the role of specific variants identified in GWAS studies. Non-coding variants for instance, which are often identified in GWAS studies,  present significant challenges in terms of functional validation and interpretation.’

Reviewer #3 (Public review):

Summary:

The manuscript "Crispant analysis in zebrafish as a tool for rapid functional screening of disease-causing genes for bone fragility" describes the use of CRISPR gene editing coupled with phenotyping mosaic zebrafish larvae to characterize functions of genes implicated in heritable fragile bone disorders (FBDs). The authors targeted six high-confident candidate genes implicated in severe recessive forms of FBDs and four Osteoporosis GWAS-implicated genes and observed varied developmental phenotypes across all crispants, in addition to adult skeletal phenotypes.

A major strength of the paper is the streamlined method that produced significant phenotypes for all candidate genes tested.

We would like to thank the reviewer for highlighting the strengths of our paper.  

A major weakness is a lack of new insights into underlying mechanisms that may contribute to disease phenotypes, nor any clear commonalities across gene sets. This was most evident in the qRT-PCR analysis of select skeletal developmental genes, which all showed varied changes in fold and direction, but with little insight into the implications of the results.

We thank the reviewer for this insightful remark. We want to emphasize that this study focusses on establishing a new screening method for candidate genes involved in FBDs, rather than investigating the underlying mechanisms contributing to disease phenotypes. However, to investigate the underlying mechanisms in these crispants, the creation of bona fide mutants is necessary. We have included this consideration in the discussion.

Furthermore, we acknowledge that the results for the larval stages exhibit variability, which can complicate the interpretation of these findings. This is particularly true for the RT-PCR analysis, where whole-body samples were used, raising the possibility that other tissues may influence the expression results. Therefore, our primary focus is on the adult stages, as all crispants display a skeletal phenotype at this age. We have elaborated on this point in the discussion.

Line 462-463: ‘Moreover, to explore the underlying mechanisms contributing to disease phenotypes, it is essential to establish stable knockout mutants derived from the crispants’.

Line 391-399: ‘In adult crispants, the skeletal phenotype was generally more penetrant. All crispants showed malformed arches, a majority displayed vertebral fractures and fusions and some crispants exhibited distinct quantitative variations in vertebral body measurements. This confirmed the role of the selected genes in skeletal development and homeostasis and their involvement in skeletal disease and established the crispant approach as a valid approach for rapidly providing in vivo gene function data to support candidate gene identification.’

Ultimately, the authors were able to show their approach is capable of connecting candidate genes with perturbation of skeletal phenotypes. It was surprising that all four GWAS candidate genes (which presumably were lower confidence) also produced a result.

We appreciate the reviewer’s comment. We would like to direct attention to the discussion section, where we offer a possible explanation for the observation that all four GWAS candidate genes produce a skeletal phenotype.

Line 460-410: 'The more pronounced and earlier phenotypes in these zebrafish crispants are most likely attributed to the quasi knock-out state of the studied genes, while more common less impactful variants in the same genes result in typical late-onset osteoporosis (Laine et al., 2013) . This phenomenon is also observed in knock-out mouse models for these genes (Melville et al., 2014)(Coughlin et al., 2019).’

These authors have previously demonstrated that crispants recapitulate skeletal phenotypes of stable mutant lines for a single gene, somewhat reducing the novelty of the study.

We thank the reviewer for this comment and appreciate their concern. We have indeed demonstrated that crispants can recapitulate the skeletal phenotypes observed in stable mutant lines for the osteoporosis gene LRP5. However, we would like to highlight that the current study represents the first large-scale screening of candidate genes associated with bone disorders, including genes related to both OI and osteoporosis. We have included this information in both the abstract and the discussion

Line 60-62: ‘We advocate for a novel comprehensive approach that integrates various techniques and evaluates distinct skeletal and molecular profiles across different developmental and adult stages.’

Line 456-457: ‘While this work represents a pioneering effort in establishing a screening platform for skeletal diseases, it offers opportunities for future improvement and refinement.’

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 1a: what does the differential shading of the bone elements represent? Explain in the legend.

The differential shading doesn't represent anything specific. It's simply used to enhance the visual appeal and to help distinguish between the different structures. We removed the shading in the figure.

(2) Supplementary Figures 2-5: should the numbering of these figures be also in order of appearance in the text? I understand that the authors prefer to associate the transgenic and the alizarin red-stained specimens, however, the reading would be easier that way.

We changed this accordingly.

(3) Lines 275-276: "no significant differences in standard length (Figure 4a)": should be Figure 4b.

The suggested changes are incorporated in the manuscript.

Line 276-277: ‘Among the eight crispants that successfully matured into adulthood, none exhibited significant differences in standard length and head size (n=5 fish per crispant) (Figure 4b).’

(4) Line 277 "larger eye diameter": should be Figure 4b.

The suggested changes are incorporated in the manuscript.

Line 378: ‘However, esr1 crispants were observed to have notably larger eye diameters (Figure 4b).’

(5) Line 280: "no obvious abnormalities were detected (Figure 4b,c)": should be Figure 4a, c. Note that the authors may reconsider the a, b, c numbering in Figure 4 by inverting a and b.

The suggested changes are incorporated in the manuscript.

Line 278-281: ‘All these crispants demonstrated various abnormalities in the caudal part of the vertebral column such as fusions, compressions, fractures, or arch malformations, except for daam2 crispants where no obvious abnormalities were detected (Figure 4a,c; Supplementary Figure 6).’

(6) Table 2: This table, which recapitulates all the results presented in the manuscript, is in the end the centerpiece of the work. It is however difficult to read in its present form. Three suggestions:

- Transpose it such that each gene has its own column, and the lines give the results for the different measurements

- Place the measurements that result in "ns" for all crispants at the end (bottom) of the table.

- Maybe bring the measurements at 7dpf, 14dpf, and 90 dpf together.

We agree with the reviewer and have added a new table where we transposed the data. However, we chose not to place the measurements that resulted in 'ns' for all crispants at the end of the table, as we believe it is important to track the evolution of the phenotype over time. Where possible, we have grouped the measurements for 7 dpf and 14 dpf together.

Reviewer #2 (Recommendations for the authors):

(1) It would help to justify why these particular area measurements are appropriate for this set of candidate genes, which were selected based on putative links to bone quality rather than bone development.

The selected methods are among the most commonly used to evaluate bone phenotypes. They are straightforward to reproduce, as well as cost- and time-effective. The strength of this approach lies in its use of simple, reproducible techniques that form the foundation for characterizing bone development.  Although the candidate genes were chosen based on their putative links to bone quality, early skeletal phenotypes can already be observed during bone development.

The mineralized surface area of the total head and specific head structures was selected to evaluate the degree of mineralization in early skeletal development, as mineralization is a direct indicator of bone formation. Additionally, the osteoblast-positive surface areas were measured to provide insight into the formation of new skeletal tissue during early development. Osteoblasts, as active bone-forming cells, are essential for understanding bone growth and the dynamics of skeletal phenotypes.

Examples in the manuscript:

Line 212-214: ‘The osteoblast-positive areas in both the total head and the opercle were then quantified to gain insight into the formation of new skeletal tissue during early development.’

Line 221-223: ‘Subsequently, Alizarin Red S (ARS) staining was conducted on the same 7 and 14 dpf crispant zebrafish larvae in order to evaluate the degree of mineralization in the early skeletal structures.’

(2) Reword: The opercle bone is the earliest forming bone of the opercular series, and appears to be what the authors are referring to as the "operculum" at 7-14 dpf. The operculum is the larger structure (gill cover) in which the opercle is embedded. It would be more accurate to simply refer to the opercle at these stages.

We agree with this comment and changed the text accordingly.

(3) Define BMD and TMD at first usage.

BMD and TMD are now defined in the manuscript.

Line 41-43: ‘Six genes associated with severe recessive forms of Osteogenesis Imperfecta (OI) and four genes associated with bone mineral density (BMD), a key osteoporosis indicator, identified through genome-wide association studies (GWAS) were selected.’

Line 286-288: ‘For each of the vertebral centra, the length, tissue mineral density (TMD), volume, and thickness were determined and tested for statistical differences between groups using a regression-based statistical test (Supplementary Figure 7).’

(4) It would be helpful to note the grouping of candidates into OI vs. BMD GWAS throughout the figures.

We agree with this comment and added this to all figure legends.

‘The first four genes are associated with the pathogenesis of osteoporosis, while the last six are linked to osteogenesis imperfecta’

Reviewer #3 (Recommendations for the authors):

Major points:

(1) For the Results, it would be useful to the Reader to justify the selection of human candidate genes and their associated zebrafish orthologs to model skeletal functions. For example, what are variants identified from human studies, and do they impact functional domains? Are these domains and/or proteins conserved between humans/zebrafish? Is there evidence of skeletal expression in humans/zebrafish?

Supplementary Table 4 lists the selected human candidate genes with reported mutations and/or polymorphisms associated with both skeletal and non-skeletal phenotypes. The table also includes additional findings from studies in mice and zebrafish. An extra column was now added to indicate gene conservation between human and zebrafish. We consulted UniProt (https://www.uniprot.org) and ZFIN (https://zfin.org) to assess the skeletal expression of these genes in human and zebrafish. All genes showed expression in the trabecular bone and/or bone marrow in humans, as well as in bone elements in zebrafish. We added this in the discussion.

Line 309: ‘All selected genes show skeletal expression in both human and zebrafish.’

Supplemental table 4 legend: ‘The conservation between human and zebrafish is reported in the last column.’

As part of this, some version of Supplementary Table 4 might be included as a main display to introduce the targeted genes, ideally separated by rare (recessive OI) vs. common disease (osteoporosis). In the case of common disease and GWAS hits, how did authors narrow in on candidate genes (which often have Mbp-scale associated regions spanning multiple genes)? Further, what is the evidence that the mechanism of action of the GWAS variant is haploinsufficiency modeled by their crispant zebrafish?

We have kept Supplementary Table 4 in the supplementary material but have referred to it earlier in the manuscript’s introduction. Consequently, the table has been renumbered from ‘Supplementary Table 4’  to ‘Supplementary Table 1’.

The selection of genes potentially involved in the pathogenesis of osteoporosis is based on the data from the GWAS catalog, which annotates SNPs using the Ensemble mapping pipeline. The available annotation on their online search interface includes any Ensemble genes to which a SNP maps, or the closest upstream and downstream gene within a 50kb window. Four genes were selected for this screening method based on the criteria outlined in the results section. In this study, we aim to evaluate the general involvement of specific genes in bone metabolism, rather than to model a specific variant.

Line 135-136 and 309-311: ‘An overview of the selected genes with observed mutant phenotypes in human, mice and zebrafish is provided in Supplementary Table 1.’

(2) Using the crispant approach does not impact maternally-deposited RNAs that would dampen early developmental phenotypes. Considering the higher variability in larval phenotypes, perhaps the maternal effect plays a role. The authors might investigate developmental expression profiles of their genes using existing RNA-seq datasets such as from White et al (doi: 10.7554/eLife.30860).

We thank the reviewer for this comment and agree with the possibility that maternally-deposited RNAs might have an impact on early developmental phenotypes. We included this in the discussion.

Line 369-372: ‘Phenotypic variability in these zebrafish larvae can be attributed to several factors, including crispant mosaicism, allele heterogeneity, environmental factors, differences in genomic background and development, maternally-deposited RNAs, and slightly variable imaging positioning.’

(3) While making comparisons within a clutch of mutant vs scrambled control is crucial, it is also important to ensure phenotypes are not specific to a single clutch. Do phenotypes remain consistent across different crosses/clutches?

Yes, phenotypes remain consistent across different crosses and clutches. We included images from a second clutch in the Supplementary material (Supplementary Figure 8) and refereed to it in the discussion.

Line 394-397: ‘Additionally, these skeletal malformations were consistently observed in a second clutch of crispants (Supplementary Figure 8), underscoring the reproducibility of these phenotypic features across independent clutches.’

(4) Understanding that antibodies may not exist for many of the selected genes for zebrafish, authors should verify haploinsufficiency using an RT-qPCR of targeted genes in crispants vs. controls.

We appreciate the reviewer’s suggestion to use RT-qPCR to examine expression levels of the targeted genes in crispants. However, previous experience suggests that relying on RNA expression to verify haploinsufficiency in zebrafish can be challenging. In zebrafish KO mutants, RT-qPCR often still detects gene transcripts, potentially due to incomplete nonsense-mediated decay (NMD) of the mutated mRNA, which may allow residual expression even in the absence of functional protein. As a more definitive approach, we prefer to use antibodies to confirm haploinsufficiency at the protein level. However, as the reviewer noted, generating and applying specific antibodies in zebrafish remains challenging.

(5) Please indicate how parametric vs. non-parametric statistical tests were selected for datasets.

We initially selected the parametric unpaired t-test, assuming the data were normally distributed with similar variances between groups. We verified the assumption of equal variances using the F-test, which was not significant across all assays. However, we did not assess the normality of the data directly, meaning we cannot confirm the normality assumption required for the t-test. Given this, we have opted to use the non-parametric Mann-Whitney U test, which does not require assumptions of normality, to ensure the robustness of our statistical analyses. We changed the Figures, the figure legends and the text accordingly.

(6) In the figures and tables, I recommend adding notation showing the grouping of the first four genes as GWAS osteoporosis, the next three genes as osteoblast differentiation, the next two genes as bone mineralization, and the final gene as collagen transport to orient the reader. One might expect there to be a clustering of phenotypic outcomes based on the selection of genes, and it would be easier to follow this. This would be particularly useful to include in Table 2.

Our primary objective is to assess the feasibility and reproducibility of the crispant screen rather than performing an in-depth pathway analysis or categorizing genes by biological processes. For this purpose, we have organized candidate genes based on their relevance to osteoporosis and Osteogenesis Imperfecta, without subdividing them further. We have clarified this focus in the figure legends, as suggested in an earlier recommendation.

(7) For Figure 1, consider adding a smaller zoomed version of 1a embedded in each sub-figure with each measured element highlighted to improve readability.

We agree with this comment and changed the figure accordingly.

Minor points:

(1) Table 2 could be simplified to improve readability. The headers have redundancies across columns with varied time points and could be merged.

The suggested changes are incorporated in the manuscript (see earlier comment about this).

(2) "BMD" is not defined in the Abstract. This is a personal preference, but there were numerous abbreviations in the text that made it difficult to follow at times.

The suggested changes are incorporated in the manuscript (see earlier comment about this).

Author response:

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

eLife Assessment

This valuable study reveals how a rhizobial effector protein cleaves and inhibits a key plant receptor for symbiosis signaling, while the host plant counters by phosphorylating the effector. The molecular evidence for the protein-protein interaction and modification is solid, though biological evidence directly linking effector cleavage to rhizobial infection is incomplete. With additional functional data, this work could have implications for understanding intricate plant-microbe dynamics during mutualistic interactions.

Thank you for this positive comment. Our data strongly support the view that NFR5 cleavage by NopT impairs Nod factor signaling resulting in reduced rhizobial infection. However, other mechanisms may also have an effect on the symbiosis, as NopT targets other proteins in addition to NFR5. In our revised manuscript version, we discuss the possibility that negative NopT effects on symbiosis could be due to NopT-triggered immune responses. As mentioned in our point-by-point answers to the Reviewers, we included additional data into our manuscript. We would also like to point out that we are generally more cautious in our revised version in order to avoid over-interpreting the data obtained.

Public Reviews:

Reviewer #1 (Public Review):

Bacterial effectors that interfere with the inner molecular workings of eukaryotic host cells are of great biological significance across disciplines. On the one hand they help us to understand the molecular strategies that bacteria use to manipulate host cells. On the other hand they can be used as research tools to reveal molecular details of the intricate workings of the host machinery that is relevant for the interaction/defence/symbiosis with bacteria. The authors investigate the function and biological impact of a rhizobial effector that interacts with and modifies, and curiously is modified by, legume receptors essential for symbiosis. The molecular analysis revealed a bacterial effector that cleaves a plant symbiosis signaling receptor to inhibit signaling and the host counterplay by phosphorylation via a receptor kinase. These findings have potential implications beyond bacterial interactions with plants.

Thank you for highlighting the broad significance of rhizobial effectors in understanding legume-rhizobia interactions. We fully agree with your assessment and have expanded our Discussion (and Abstract) regarding the potential implications of our findings beyond bacterial interactions with plants. We mention the prospect of developing specific kinase-interacting proteases to fine-tune cellular signaling processes in general.

Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis. A rhizobial effector is described to directly modify symbiosis-related signaling proteins, altering the outcome of the symbiosis. Overall, the paper presents findings that will have a wide appeal beyond its primary field.

Out of 15 identified effectors from Sinorhizobium fredii, they focus on the effector NopT, which exhibits proteolytic activity and may therefore cleave specific target proteins of the host plant. They focus on two Nod factor receptors of the legume Lotus japonicus, NFR1 and NFR5, both of which were previously found to be essential for the perception of rhizobial nod factor, and the induction of symbiotic responses such as bacterial infection thread formation in root hairs and root nodule development (Madsen et al., 2003, Nature; Tirichine et al., 2003; Nature). The authors present evidence for an interaction of NopT with NFR1 and NFR5. The paper aims to characterize the biochemical and functional consequences of these interactions and the phenotype that arises when the effector is mutated.

Thank you for your positive feedback.  We have now emphasized the interdisciplinary significance of our work in the Introduction and Discussion of our revised manuscript. We highlight how the insights gained from our study can contribute to a better understanding of microbial interactions with eukaryotic hosts in general, and hope that our findings could benefit future research in the fields of pathogenesis, immunity, and symbiosis.

We appreciate your detailed summary of our work, which is focused on NopT and its interaction with Nod factor receptors. To ensure that the readers can easily follow the rationale behind our work, we have included a more detailed explanation of how NopT was identified to target Nod factor receptors. In particular, we now better describe the test system (Nicotiana benthamiana cells co-expressing NFR1/NFR5 with a given effector of Sinorhizobium fredii NGR234). In addition, we provide now a more thorough background on the roles of NFR1 and NFR5 in symbiotic signaling and refer to the two Nature papers from 2003 on NFR1 and NFR5 (Madsen et al., 2003; Radutoiu et al., 2003).

Evidence is presented that in vitro NopT can cleave NFR5 at its juxtamembrane region. NFR5 appears also to be cleaved in vivo. and NFR1 appears to inhibit the proteolytic activity of NopT by phosphorylating NopT. When NFR5 and NFR1 are ectopically over-expressed in leaves of the non-legume Nicotiana benthamiana, they induce cell death (Madsen et al., 2011, Plant Journal). Bao et al., found that this cell death response is inhibited by the coexpression of nopT. Mutation of nopT alters the outcome of rhizobial infection in L. japonicus. These conclusions are well supported by the data.

We appreciate your recognition of the robustness of our conclusions. In the context of your comments, we made the following improvements to our manuscript:

We included a more detailed description of the experimental conditions under which the cleavage of NFR5 by NopT was observed in vitro and in vivo. Furthermore, additional experiments were added to strengthen the evidence for NFR5 cleavage by NopT (Fig 3, S3, S6, and S14).

We provided more comprehensive data on the phosphorylation of NopT by NFR1, including phosphorylation assays (Fig. 4) and mass spectrometry results (Fig. S7 and Table S1). These data provide additional information on the mechanism by which NFR1 inhibits the proteolytic activity of NopT.

We expanded the discussion on the cell death response induced by ectopic expression of NFR1 and NFR5 in Nicotiana benthamiana. We also included further details from Madsen et al. (2011) to contextualize our findings within the known literature.

We believe that these additions and clarifications have improved the significance and impact of our study.

The authors present evidence supporting the interaction of NopT with NFR1 and NFR5. In particular, there is solid support for cleavage of NFR5 by NopT (Figure 3) and the identification of NopT phosphorylation sites that inhibit its proteolytic activity (Figure 4C). Cleavage of NFR5 upon expression in N. benthamiana (Figure 3A) requires appropriate controls (inactive mutant versions) that have been provided, since Agrobacterium as a closely rhizobia-related bacterium, might increase defense related proteolytic activity in the plant host cells.

We appreciate your recognition of the importance of appropriate controls in our experimental design. In response to your comments, we revised our manuscript to ensure that the figures and legends provide a clear description of the controls used. We also included a more detailed description of our experimental design at several places. In particular, we have highlighted the use of the protease-dead version of NopT as a control (NopT^C93S). Therefore, NFR5-GFP cleavage in N. benthamiana clearly depended on protease activity of NopT and not on Agrobacterium (Fig. 3A). In the revised text, we are now more cautious in our wording and don’t conclude at this stage that NopT proteolyzes NFR5. However, our subsequent experiments, including in vitro experiments, clearly show that NopT is able to proteolyze NFR5.

We are convinced that these changes have improved the quality of our work.

Key results from N. benthamiana appear consistent with data from recombinant protein expression in bacteria. For the analysis in the host legume L. japonicus transgenic hairy roots were included. To demonstrate that the cleavage of NFR5 occurs during the interaction in plant cells the authors build largely on western blots. Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with nopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). It is not quite clear how the authors explain the loss of NFR5 function (loss of cell death, impact on symbiosis), as a vast excess of the tested target remains intact. It is also not clear why a large proportion of NFR5 is unaffected by the proteolytic activity of NopT. This is particularly interesting in Nicotiana in the absence of Nod factor that could trigger NFR1 kinase activity.

Thank you for your comments regarding the cleavage of NFR5 by NopT and its functional implications. We acknowledge that our immunoblots indicate only a relatively small proportion of  the NFR5 cleavage product.  Possible explanations could be as follows:

(1) The presence of full-length NFR5 does not preclude a significant impact of NopT on function of NFR5, as NopT is able to bind to NFR5. In other words, the NopT-NFR5 and NopT-NFR1 interactions at the plasmamembrane might influence the function of the NFR1/NFR5 receptor without proteolytic cleavage of NFR5. In fact, protease-dead NopT^C93S expressed in NGR234Δ_nopT_ showed certain effects in L. japonicus (less infection foci were formed compared to NGR234Δ_nopT_ Fig. 5E).  In this context, it is worth mentioning that the non-acylated NopT^C93S (Fig. 1B) and not_USDA257 (Fig. 6B) proteins were unable to suppress NFR1/NFR5-induced cell death in N. benthamina, but this could be explained by the lack of acylation and altered subcellular localization.

(2) The cleaved NFR5 fraction, although small, may be sufficient to disrupt signaling pathways, leading to the observed phenotypic changes  (loss of cell death in N. benthamiana; altered infection in L. japonicus).

(3) The used expression systems produce high levels of proteins in the cell. This may not reflect the natural situation in L. japonicus cells.

(4) Cellular conditions could impair cleavage of NFR5 by NopT.  Expression of proteins in E. coli may partially result in formation of protein aggregates (inactive NopT; NFR5 resistant to proteolysis).

(5) In N. benthamiana co-expressing NFR1/NFR5, the NFR1 kinase activity is constitutively active (i.e., does not require Nod factors), suggesting an altered protein conformation of the receptor complex, which may influence the proteolytic susceptibility of NFR5.

(6) The proteolytic activity of NopT may be reduced by the interaction of NopT with other proteins such as NFR1, which phosphorylates NopT and inactivates its protease activity.

In our revised manuscript version, we provide now quantitative data for the efficiency of NFR5 cleavage by NopT in different expression systems used (Supplemental Fig.  14).  We have also improved our Discussion in this context. Future research will be necessary to better understand loss of NFR5 function by NopT. 

It is also difficult to evaluate how the ratios of cleaved and full-length protein change when different versions of NopT are present without a quantification of band strengths normalized to loading controls (Figure 3C, 3D, 3F). The same is true for the blots supporting NFR1 phosphorylation of NopT (Figure 4A).

Thank you for pointing out this. Following your suggestions, we quantified the band intensities for cleaved and full-length NFR5 in our different expression systems (N. benthamiana, L. japonicus and E. coli). The protein bands were normalized to loading controls. The data are shown in the new Supplemental Fig. 14. Similarly, the bands of immunoblots supporting phosphorylation of NopT by NFR1 were quantified. The data on band intensities are shown in Fig.  4B of our revised manuscript. These improvements provide a clearer understanding of how the ratios of cleaved to full-length proteins change in different protein expression systems, and to which extent NopT was phosphorylated by NFR1.

Nodule primordia and infection threads are still formed when L. japonicus plants are inoculated with ∆nopT mutant bacteria, but it is not clear if these primordia are infected or develop into fully functional nodules (Figure 5). A quantification of the ratio of infected and non-infected nodules and primordia would reveal whether NopT is only active at the transition from infection focus to thread or perhaps also later in the bacterial infection process of the developing root nodule.

Thank you for highlighting this aspect of our study. In response to your comment, we have conducted additional inoculation experiments with L. japonicus plants inoculated with NGR234 and NGR234_ΔnopT_ mutant. The new data are shown in Fig 5A, 5E, and 5G. However, we could not find any uninfected nodules (empty) nodules when roots were inoculated with these strains and mention this observation in the Results section of our revised manuscript.

Reviewer #2 (Public Review):

Summary:

This manuscript presents data demonstrating NopT's interaction with Nod Factor Receptors NFR1 and NFR5 and its impact on cell death inhibition and rhizobial infection. The identification of a truncated NopT variant in certain Sinorhizobium species adds an interesting dimension to the study. These data try to bridge the gaps between classical Nod-factor-dependent nodulation and T3SS NopT effector-dependent nodulation in legume-rhizobium symbiosis. Overall, the research provides interesting insights into the molecular mechanisms underlying symbiotic interactions between rhizobia and legumes.

Strengths:

The manuscript nicely demonstrates NopT's proteolytic cleavage of NFR5, regulated by NFR1 phosphorylation, promoting rhizobial infection in L. japonicus. Intriguingly, authors also identify a truncated NopT variant in certain Sinorhizobium species, maintaining NFR5 cleavage but lacking NFR1 interaction. These findings bridge the T3SS effector with the classical Nod-factor-dependent nodulation pathway, offering novel insights into symbiotic interactions.

Weaknesses:

(1) In the previous study, when transiently expressed NopT alone in Nicotiana tobacco plants, proteolytically active NopT elicited a rapid hypersensitive reaction. However, this phenotype was not observed when expressing the same NopT in Nicotiana benthamiana (Figure 1A). Conversely, cell death and a hypersensitive reaction were observed in Figure S8. This raises questions about the suitability of the exogenous expression system for studying NopT proteolysis specificity.

We appreciate your attention to these plant-specific differences. Previous studies showed that NopT expressed in tobacco (N. tabacum) or in specific Arabidopsis ecotypes (with PBS1/RPS5 genes) causes rapid cell death (Dai et al. 2008; Khan et al. 2022). Khan et al. 2022 reported recently that cell death does not occur in N. benthamiana unless the leaves were transformed with PBS1/RPS5 constructs. Our data shown in Fig. S15 confirm these findings. As cell death (effector triggered immunity) is usually associated with induction of plant protease activities, we considered N. tabacum and A. thaliana plants as not suitable for testing NFR5 cleavage by NopT. In fact, no NopT/NFR5 experiments were not performed with these plants in our study.  In response to your comment, we now better describe the N. benthamiana expression system and cite the previous articles_. Furthermore,  We have revised the Discussion section to better emphasize effector-induced immunity in non-host plants and the negative effect of rhizobial effectors during symbiosis. Our revisions certainly provide a clearer understanding of the advantages and limitations of the _N.  benthamiana expression system.

(2) NFR5 Loss-of-function mutants do not produce nodules in the presence of rhizobia in lotus roots, and overexpression of NFR1 and NFR5 produces spontaneous nodules. In this regard, if the direct proteolysis target of NopT is NFR5, one could expect the NGR234's infection will not be very successful because of the Native NopT's specific proteolysis function of NFR5 and NFR1. Conversely, in Figure 5, authors observed the different results.

Thank you for this comment, which points out that we did not address this aspect precisely enough in the original manuscript version.  We improved our manuscript and now write that nfr1 and nfr5 mutants do not produce nodules (Madsen et al., 2003; Radutoiu et al., 2003) and that over-expression of either NFR1 or NFR5 can activate NF signaling, resulting in formation of spontaneous nodules in the absence of rhizobia (Ried et al., 2014). In fact, compared to the nopT knockout mutant NGR234_ΔnopT_, wildtype NGR234 (with NopT) is less successful in inducing infection foci in root hairs of L. japonicus (Fig. 5). With respect to formation of nodule primordia, we repeated our inoculation experiments with NGR234_ΔnopT_ and wildtype NGR234 and also included a nopT over-expressing NGR234 strain into the analysis. Our data clearly showed that nodule primordium formation was negatively affected by NopT. The new data are shown in Fig. 5 of our revised version. Our data show that NGR234's infection is not really successful, especially when NopT is over-expressed. This is consistent  with our observations that NopT targets Nod factor receptors in L. japonicus and inhibits NF signaling (NIN promoter-GUS experiments). Our findings indicate that NopT is an “Avr effector” for L. japonicus.  However, in other host plants of NGR234, NopT possesses a symbiosis-promoting role (Dai et al. 2008; Kambara et al. 2009). Such differences could be explained by different NopT targets in different plants (in addition to Nod factor receptors), which may influence the outcome of the infection process. Indeed, our work shows hat NopT can interact with various kinase-dead LysM domain receptors, suggesting a role of NopT in suppression or activation of plant immunity responses depending on the host plant. We discuss such alternative mechanisms in our revised manuscript version and emphasize the need for further investigation to elucidate the precise mechanisms underlying the observed infection phenotype and the role of NopT in modulating symbiotic signaling pathways. In this context, we would also like to mention the two new figures of our manuscript which are showing (i) the efficiency of NFR5 cleavage by NopT in different expression systems, (ii) the interaction between NopT^C93S and His-SUMO-NFR5^JM-GFP, and (iii) cleavage of His-SUMO-NFP^JM-GFP by NopT (Supplementary Figs. S8 and S9).

(3) In Figure 6E, the model illustrates how NopT digests NFR5 to regulate rhizobia infection. However, it raises the question of whether it is reasonable for NGR234 to produce an effector that restricts its own colonization in host plants.

Thank you for mentioning this point. We are aware of the possible paradox that the broad-host-range strain NGR234 produces an effector that appears to restrict its infection of host plants. As mentioned in our answer to the previous comment, NopT could have additional functions beyond the regulation of Nod factor signaling. In our revised manuscript version, we have modified our text as follows:

(1) We mention the potential evolutionary aspects of NopT-mediated regulation of rhizobial infection and discuss the possibility that interactions between NopT and Nod factor receptors may have evolved to fine-tune Nod factor signaling to avoid rhizobial hyperinfection in certain host legumes.

(2) We also emphasize that the presence of NopT may confer selective advantages in other host plants than L. japonicus due to interactions with proteins related to plant immunity. Like other effectors, NopT could suppress activation of immune responses (suppression of PTI) or cause effector-triggered immunity (ETI) responses, thereby modulating rhizobial infection and nodule formation. Interactions between NopT and proteins related to the plant immune system may represent an important evolutionary driving force for host-specific nodulation and explain why the presence of NopT in NGR234 has a negative effect on symbiosis with L. japonicus but a positive one with other legumes.

(4) The failure to generate stable transgenic plants expressing NopT in Lotus japonicus is surprising, considering the manuscript's claim that NopT specifically proteolyzes NFR5, a major player in the response to nodule symbiosis, without being essential for plant development.

We also thank for this comment. We have revised the Discussion section of our manuscript and discuss now our failure to generate stable transgenic L. japonicus plants expressing NopT. We observed that the protease activity of NopT in aerial parts of L. japonicus had a negative effect on plant development, whereas NopT expression in hairy roots was possible. Such differences may be explained by different NopT substrates in roots and aerial parts of the plant. In this context, we also discuss our finding that NopT not only cleaves NFR5 but is also able to proteolyze other proteins of L. japonicus such as LjLYS11, suggesting that NopT not only suppresses Nod factor signaling, but may also interfere with signal transduction pathways related to plant immunity. We speculate that, depending on the host legume species, NopT could suppress PTI or induce ETI, thereby modulating rhizobial infection and nodule formation.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Overall the text and figure legends must be double-checked for correctness of scientific statements. The few listed here are just examples. There are more that are potentially damaging the perception by the readers and thus the value of the manuscript.

The nopT mutant leads to more infections. In line 358 the statement: "...and the proteolysis of NFR5 are important for rhizobial infection", is wrong, as the infection works even better without it. It is, according to my interpretation of the results, important for the regulation of infection. Sounds a small difference, but it completely changes the meaning.

We appreciate your thorough review and have taken the opportunity to correct this error. Following your suggestions, we carefully rephrased the whole text and figure legends to ensure that the scientific statements accurately reflect the findings of our study. We are convinced that these changed have increased the value of this study.

In line 905 the authors state that NopTC indicates the truncated version of NopT after autocleavage by releasing about 50 a.a. at its N-terminus.

They do not analyse this cleavage product to support this claim. So better rephrase.

According to Dai et al. (2008), NopT expressed in E. coli is autocleaved. The N-terminal sequence GCCA obtained by Edman sequencing suggests that NopT was cleaved between M49 and G50.  We improved our manuscript and now write:

(1) “A previous study has shown that NopT is autocleaved at its N-terminus to form a processed protein that lacks the first 49 amino acid residues (Dai et al., 2008)”

(2) “However, NopT^ΔN50, which is similar to autocleaved NopT, retained the ability to interact with NFR5 but not with NFR1 (Fig. S2D).”.

In line 967: "Both NopT and NopTC after autocleavage exert proteolytic activities" This is confusing as it was suggested earlier that NopTc is a product of the autocleavage. There is no indication of another round of NopTc autocleavage or did I miss something?

Thank you for bringing this inaccuracy to our attention. There is no second round of NopT autocleavage. We have corrected the text and write: “NopT and not^C (autocleaved NopT) proteolytically cleave NFR5 at the juxtamembrane domain to release the intracellular domain of NFR5”

Given the amount of work that went into the research, the presentation of the figures should be considerably improved. For example, in Figure 3F the mutant is not correctly annotated. In figure 5 the term infection foci and IT occur but it is not explained in the legend what these are, where they can be seen in the figure and how the researchers discriminated between the two events.

In general, the labeling of the figure panels should be improved to facilitate the understanding. For example, in Figure 3 the panels switch between different host plant systems. The plant could be clarified for each panel to aid the reader. The asterisks are not in line with the signal that is supposed to be marked. And so on. I strongly advise to improve the figures.

Thank you for your valuable suggestions. We acknowledge the importance of clear and informative figure presentation to enhance the understanding of our research findings. In response to your comments, we made a comprehensive revision of the figures to address the mentioned issues:

(1) We corrected annotations of the mutant in Figure 3F to accurately represent the experimental conditions.

(2) We revised the legend of Figure 5 and provide clear explanations of the terms "infection foci" and "IT" (infection threads) in the Methods section.

(3) We improved the labeling of figure panels and improved the writing of the figure legend specifying the protein expression system (N. benthamiana, L. japonicus and E. coli, respectively). . We ensured that the asterisks indicating statistically significant results are properly aligned.

Furthermore, we carefully reviewed each figure to enhance clarity and readability, including optimizing font size and line thickness. Captions and annotations were also revised.

Figure 1

• To verify that the lack of observed cell death is not linked to differential expression levels, an expression control Western blot is essential. In the expression control Western blot given in the supplemental materials (Supplemental fig. 1E), NFR5 is not visible in the first lane.

We appreciate your comments on the control immunoblot which were made to verify the presence of NFR1, NFR5 and NopT in N. benthamiana.  However, as shown in Supplemental Fig. 1E, the intact NFR5 could not be immuno-detected when co-expressed with NFR1 and NopT. To ensure co-expression of NFR1/NFR5, A. tumefaciens carrying a binary vector with both NFR1 and NFR5 was used. In the revised version, we modified the figure legend accordingly and also included a detailed description of the procedure at lines 165-166

• Labeling of NFR1/LjNFR1 should be kept consistent between the text and the figures. Currently, the text refers to both NFR1 and LjNFR1 and figures are labelled NFR1. The same is true for NFR5.

Thank you for pointing out this inconsistency. We revised our manuscript and use now consistently NFR1 and NFR5 without a prefix to avoid any confusions.

• A clearer description of how cell death was determined would be useful. In the selected pictures in panel D, leaves coexpressing nopT with Bax1 or Cerk1 appear very different from the pictures selected for NopM and AVr3a/R3a.

We agree that a clearer description of our cell death experiments with N. benthamiana was necessary. We have re-worded the figure legend to provide more detailed information on the criteria used for assessing cell death. Additionally, we show now our images at higher resolution.

• In panel D, the "Death/Total" ratio is only shown for leaf discs where nopT was coexpressed with the cell-death triggering proteins. Including the ratio for leaf discs where only the cell-death triggering protein (without nopT ) was expressed would make the figure more clear.

Thank you for this suggestion. To provide a more comprehensive comparison, we included the "Cell death/Total" ratio for all leaf disc images shown in Fig. 1D. 

Figure 2:

• A: Split-YFP is not ideal as evidence for colocalization because of the chemical bond formed between the YFP fragments that may lead to artificial trapping/accumulation outside the main expression domains. Overall, the authors should revise if this figure aims to show colocalization or interaction. In the current text, both terms are used, but these are different interpretations.

We appreciate your concern regarding the use of Split-YFP for colocalization analysis. We carefully reviewed the figure and corresponding text to ensure clarity in the interpretation of the results. The primary aim of this figure was to explore protein-protein interactions rather than strict colocalization. Protein-protein interactions have also been validated by other experiments of our work. We have revised the text accordingly and no longer emphasize on “co-localization”.

• Given the focus on proteolytic activity in this paper, all blots need to be clearly labeled with size markers, and it would be good to include a supplemental figure with all other bands produced in the Western blot, regardless of their size. Without this, the results in panel 2D seem inconsistent with results presented in figure 3A, since NFR5 does not appear to be cleaved in the Western blot in 2D, but 3A shows cleavage when the same proteins (with different tags) are coexpressed in the same system.

Thank you for bringing up this point. We ensured that all immunoblots are clearly labeled with size markers in our revised manuscript. We also carefully checked the consistency of the results presented in Figures 2D and Figure 3A and included appropriate clarifications in the revised manuscript. In Figure 2D, we show the bands at around 75 kD  (multi-bands would be detected below, including cleaved NFR5 by NopT, but also other non-specific bands).

Figure 3:

• In panel E, NopTC93S cannot cleave His-Sumo-NFR5JM-GFP, but it would be interesting to also show if NopTC93S can bind the NFR5JM fragment. It would also be useful to see this experiment done with the JM of NFP.

Thank you for the suggestion. We agree that investigating the binding of NopT^C93S to the NFR5^JM fragment provides valuable insights into the interaction between NopT and NFR5. In our revised version, we show in the new Supplemental Fig. S4 that NopT interacts with NFR5JM and cleaves NFP^JM. The Results section has been modified accordingly.

• The panels in this figure require better labeling. In many panels, asterisks are misplaced relative to the bands they should highlight, and not all blots have size markers or loading controls.

Thank you for bringing this to our attention. We carefully reviewed the labeling of all panels in Figure 3 to ensure accuracy and clarity. We ensured that asterisks are correctly placed in the figures. We also included size markers and loading controls to improve the quality of the shown immunoblots.

• Since there is no clear evidence in this figure that the smear in the blot in panel C is phosphorylated NopT, it is recommended to provide a less interpretative label on the blot, and explain the label in the text.

We appreciate your suggestion regarding the labeling of the blot in panel C of Fig. 3. We revised the label and provided a less interpretative designation in Fig. 3C. We also rephrased the figure legend and the text in the Results section as recommended.

Figure 4

• In B, a brief introduction in the text to the function of the Zn-phostag would make the figure easier to understand for more readers.

Thank you for the suggestion. We agree and have provided a brief explanation in the Results section: “On such gels, a Zn²⁺-Phos-tag bound phosphorylated protein migrates slower than its unbound nonphosphorylated form. Furthermore, we have included the reference (Kato & Sakamoto, 2019) into the Methods section.

Figure 5:

• Change "Scar bar" to "Scale bar" in the figure captions

Thank you for spotting that typo. We have corrected it.

• Correct the references to the figures in the text

We carefully reviewed the Figure 5 and made corresponding corrections to improve the quality of our manuscript Please check line 394-451.

• It should be clarified what was quantified as "infection foci" (C, F, G)

We revised the legend of Figure 5 and provide now explanations of the terms "infection foci" and "IT" (infection threads) in the Methods section.  Please check line 399-451.

• It is recommended to use pictures that are from the same region of the plant root (the susceptible zone). The pictures in panel A appear to be from different regions, since the density of root hairs is different.

Thank you for bringing this to our attention. We ensured that the images selected for panel A were from the same region of the plant root to guarantee consistency and accuracy of the comparison.

• Panel G should be labeled so it is clearer that nopT is being expressed in L. japonicus transgenic roots.

We have labeled this panel more clearly to help the reader understand that nopT was expressed in transgenic L. japonicus roots.

• Panel F is missing statistical tests for ITs

We apologize and have included the results of our statistical tests for ITs.

Figure 6:

• The model presented in panel E misrepresents the role of NFR5 according to the results in the paper. From the evidence presented, it is not clear if the observed rhizobial infection phenotype is due to reduced abundance of full-length NFR5, or if the cleaved NFR5 fragment is suppressing infection. Additionally, S. fredii should not be drawn so close to the plasma membrane, since the bacteria are located outside the cell wall when the T3SS is active.

We appreciate your comment which helps us to improve the interpretation of our results. We agree that the model should accurately reflect the uncertainties regarding the role of NFR5. We revised the model (positioning of S. fredii etc.) and write in the Discussion:

“NopT impairs the function of the NFR1/NFR5 receptor complex. Cleavage of NFR5 by NopT reduces its protein levels. Possible inhibitory effects of NFR5 cleavage products on NF signaling are unknown but cannot be excluded.”

Reviewer #2 (Recommendations For The Authors):

(1) Some minor weaknesses need addressing: In Figure 5A, the root hair density in the two images appears significantly different. Are these images representative of each treatment?

We appreciate your attention to detail and the importance of ensuring that the images in Figure 5A are representative. We carefully reviewed our image selection process and confirm that the shown images are indeed representative of each treatment group. In our revised version, we show additional images and also improved the text in the figure legend. Furthermore, we performed additional GUS staining tests and the new data are shown in Fig 5A abd 5B.

(2) Additionally, please ensure consistency in the format of genotype names throughout the manuscript. For instance, in Line 897, "Italy" should be used in place of "N. benthamiana."

We thank you for pointing out the format of genotype names and corrected our manuscript as requested.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review): 

Summary: 

The authors introduced their previous paper with the concise statement that "the relationships between lineage-specific attributes and genotypic differences of tumors are not understood" (Chen et al., JEM 2019, PMID: 30737256). For example, it is not clear why combined loss of RB1 and TP53 is required for tumorigenesis in SCLC or other aggressive neuroendocrine (NE) cancers, or why the oncogenic mutations in KRAS or EGFR that drive NSCLC tumorigenesis are found so infrequently in SCLC. This is the main question addressed by the previous and current papers. 

One approach to this question is to identify a discrete set of genetic/biochemical manipulations that are sufficient to transform non-malignant human cells into SCLC-like tumors. One group reported the transformation of primary human bronchial epithelial cells into NE tumors through a complex lentiviral cocktail involving the inactivation of pRB and p53 and activation of AKT, cMYC, and BCL2 (PARCB) (Park et al., Science 2018, PMID: 30287662). The cocktail previously reported by Chen and colleagues to transform human pluripotent stem-cell (hPSC)-derived lung progenitors (LPs) into NE xenografts was more concise: DAPT to inactivate NOTCH signaling combined with shRNAs against RB1 and TP53. However, the resulting RP xenografts lacked important characteristics of SCLC. Unlike SCLC, these tumors proliferated slowly and did not metastasize, and although small subpopulations expressed MYC or MYCL, none expressed NEUROD1. 

MYC is frequently amplified or expressed at high levels in SCLC, and here, the authors have tested whether inducible expression of MYC could increase the resemblance of their hPSC-derived NE tumors to SCLC. These RPM cells (or RPM T58A with stabilized cMYC) engrafted more consistently and grew more rapidly than RP cells, and unlike RP cells, formed liver metastases when injected into the renal capsule. Gene expression analyses revealed that RPM tumor subpopulations expressed NEUROD1, ASCL1, and/or YAP1. 

The hPSC-derived RPM model is a major advance over the previous RP model. This may become a powerful tool for understanding SCLC tumorigenesis and progression and for discovering gene dependencies and molecular targets for novel therapies. However, the specific role of cMYC in this model needs to be clarified. 

cMYC can drive proliferation, tumorigenesis, or apoptosis in a variety of lineages depending on concurrent mutations. For example, in the Park et al., study, normal human prostate cells could be reprogrammed to form adenocarcinoma-like tumors by activation of cMYC and AKT alone, without manipulation of TP53 or RB1. In their previous manuscript, the authors carefully showed the role of each molecular manipulation in NE tumorigenesis. DAPT was required for NE differentiation of LPs to PNECs, shRB1 was required for expansion of the PNECs, and shTP53 was required for xenograft formation. cMYC expression could influence each of these steps, and importantly, could render some steps dispensable. For example, shRB1 was previously necessary to expand the DAPT-induced PNECs, as neither shTP53 nor activation of KRAS or EGFR had no effect on this population, but perhaps cMYC overexpression could expand PNECs even in the presence of pRB, or even induce LPs to become PNECs without DAPT. Similarly, both shRB1 and shTP53 were necessary for xenograft formation, but maybe not if cMYC is overexpressed. If a molecular hallmark of SCLC, such as loss of RB1 or TP53, has become dispensable with the addition of cMYC, this information is critically important in interpreting this as a model of SCLC tumorigenesis.  

The reviewer’s suggestion may be possible; indeed, in a recent report from our group (Gardner EE, et al., Science 2024) we have shown, using genetically engineered mouse modeling coupled with lineage tracing, that the cMyc oncogene can selectively expand Ascl1+ PNECs in the lung.

We agree with the reviewer that not having a better understanding of the individual components necessary and/or sufficient to transform hESC-derived LPs is an important shortcoming of this current work. However, we would like to stress three important points about the comments:  1) tumors were reviewed and the histological diagnoses were certified by a practicing pulmonary pathologist at WCM (our co-author, C. Zhang); 2 )the observed  transcriptional programs were consistent with primary human SCLC; and 3) RB1-proficient SCLC is now recognized as a rare presentation of SCLC (Febrese-Aldana CA, et al., Clin. Can. Res. 2022. PMID: 35792876).

To interpret the role of cMYC expression in hPSC-derived RPM tumors, we need to know what this manipulation does without manipulation of pRB, p53, or NOTCH, alone or in combination. Seven relevant combinations should be presented in this manuscript: (1) cMYC alone in LPs, (2) cMYC + DAPT, (3) cMYC + shRB1, (4) cMYC + DAPT + shRB1, (5) cMYC + shTP53, (6) cMYC + DAPT + shTP53, and (7) cMYC + shRB1 + shTP53. Wildtype cMYC is sufficient; further exploration with the T58A mutant would not be necessary. 

We respectfully disagree that an interrogation of the differences between the phenotypes produced by wildtype and Myc(T58A) would not be informative. (Our view is confirmed by the second reviewer; see below.)    It is well established that Myc gene or protein dosage can have profound effects on in vivo phenotypes (Murphy DJ, et al., Cancer Cell 2008. PMID: 19061836). The “RPM” model of variant SCLC developed by Trudy Oliver’s lab relied on the conditional T58A point mutant of cMyc, originally made by Rob Wechsler-Reya. While we do not discuss the differences between Myc and Myc(T58A), it is nonetheless important to present our results with both the WT and mutant MYC constructs, as we are aware of others actively investigating differences between them in GEMM models of SCLC tumor development.

We agree with the reviewer about the virtues of trying to identify the effects of individual gene manipulations; indeed our original paper (Chen et al., J. Expt. Med. 2019), describing the RUES2derived model of SCLC did just that, carefully dissecting events required to transform LPs towards a SCLC-like state. The central  purpose of the current study was to determine the effects of adding cMyc on the behavior of weakly tumorigenic SCLC-like cells cMyc.  Presenting data with these two alleles to seek effects of different doses of MYC protein seems reasonable.

This reviewer considers that there should be a presentation of the effects of these combinations on LP differentiation to PNECs, expansion of PNECs as well as other lung cells, xenograft formation and histology, and xenograft growth rate and capacity for metastasis. If this could be clarified experimentally, and the results discussed in the context of other similar approaches such as the Park et al., paper, this study would be a major addition to the field.  

Reviewer #2 (Public Review): 

Summary: 

Chen et al use human embryonic stem cells (ESCs) to determine the impact of wildtype MYC and a point mutant stable form of MYC (MYC-T58A) in the transformation of induced pulmonary neuroendocrine cells (PNEC) in the context of RB1/P53 (RP) loss (tumor suppressors that are nearly universally lost in small cell lung cancer (SCLC)). Upon transplant into immune-deficient mice, they find that RP-MYC and RP-MYC-T58A cells grow more rapidly, and are more likely to be metastatic when transplanted into the kidney capsule, than RP controls. Through single-cell RNA sequencing and immunostaining approaches, they find that these RPM tumors and their metastases express NEUROD1, which is a transcription factor whose expression marks a distinct molecular state of SCLC. While MYC is already known to promote aggressive NEUROD1+ SCLC in other models, these data demonstrate its capacity in a human setting that provides a rationale for further use of the ESC-based model going forward. Overall, these findings provide a minor advance over the previous characterization of this ESC-based model of SCLC published in Chen et al, J Exp Med, 2019. 

We consider the findings more than a “minor” advance in the development of the model, since any useful model for SCLC would need to form aggressive and metastatic tumors.

The major conclusion of the paper is generally well supported, but some minor conclusions are inadequate and require important controls and more careful analysis. 

Strengths:

(1) Both MYC and MYC-T58A yield similar results when RP-MYC and RP-MYCT58A PNEC ESCs are injected subcutaneously, or into the renal capsule, of immune-deficient mice, leading to the conclusion that MYC promotes faster growth and more metastases than RP controls. 

(2) Consistent with numerous prior studies in mice with a neuroendocrine (NE) cell of origin (Mollaoglu et al, Cancer Cell, 2017; Ireland et al, Cancer Cell, 2020; Olsen et al, Genes Dev, 2021), MYC appears sufficient in the context of RB/P53 loss to induce the NEUROD1 state. Prior studies also show that MYC can convert human ASCL1+ neuroendocrine SCLC cell lines to a NEUROD1 state (Patel et al, Sci Advances, 2021); this study for the first time demonstrates that RB/P53/MYC from a human neuroendocrine cell of origin is sufficient to transform a NE state to aggressive NEUROD1+ SCLC. This finding provides a solid rationale for using the human ESC system to better understand the function of human oncogenes and tumor suppressors from a neuroendocrine origin. 

Weaknesses:

(1) There is a major concern about the conclusion that MYC "yields a larger neuroendocrine compartment" related to Figures 4C and 4G, which is inadequately supported and likely inaccurate. There is overwhelming published data that while MYC can promote NEUROD1, it also tends to correlate with reduced ASCL1 and reduced NE fate (Mollaoglu et al, Cancer Cell, 2017; Zhang et al, TLCR, 2018; Ireland et al, Cancer Cell, 2020; Patel et al, Sci Advances, 2021). Most importantly, there is a lack of in vivo RP tumor controls to make the proper comparison to judge MYC's impact on neuroendocrine identity. RPM tumors are largely neuroendocrine compared to in vitro conditions, but since RP control tumors (in vivo) are missing, it is impossible to determine whether MYC promotes more or less neuroendocrine fate than RP controls. It is not appropriate to compare RPM tumors to in vitro RP cells when it comes to cell fate. Upon inspection of the sample identity in S1B, the fibroblast and basal-like cells appear to only grow in vitro and are not well represented in vivo; it is, therefore, unclear whether these are transformed or even lack RB/P53 or express MYC. Indeed, a close inspection of Figure S1B shows that RPM tumor cells have little ASCL1 expression, consistent with lower NE fate than expected in control RP tumors. 

We would like to clarify two points related to the conclusions that we draw about MYC’s ability to promote an increase in the neuroendocrine fraction in hESC-derived cultures:  1) The comparisons in Figures 4C were made between cells isolated in culture following the standard 50 day differentiation protocol, where, following generation of LPs around day 25, MYC was added to the other factors previously shown to enrich for a PNEC phenotype (shRB1, shTP53, and DAPT). Therefore, the argument that MYC increased the frequency of “neuroendocrine cells” (which we define by a gene expression signature) is a reasonable conclusion in the system we are using; and 2) following injection of these cells into immunocompromised mice, an ASCL1-low / NEUROD1-high presentation is noted (Supplemental Figures 1F-G). In the few metastases that we were able use to sequence bulk RNA, there is an even more pronounced increase in expression of NEUROD1 with a decrease in ASCL1.

Some confusion may have arisen from our previous characterization of neuroendocrine (NE) cells using either ASCL1 or NEUROD1 as markers. To clarify, we have now designated cells positive for ASCL1 as classical NE cells and those positive for NEUROD1 as the NE variant. According to this revised classification, our findings indicate that MYC expression leads to an increase in the NEUROD1+ NE variant and a decrease in ASCL1+ classical NE cells. This adjustment has been reflected on the results section titled, “Inoculation of the renal capsule facilitates metastasis of the RUES2-derived RPM tumors” of the manuscript.  

From the limited samples in hand, we compared the expression of ASCL1 and NEUROD1 in the weakly tumorigenic hESC RP cells after successful primary engraftment into immunocompromised mice. As expected, the RP tumors were distinguished by the lack of expression of NEUROD1, compared to levels observed in the RPM tumors.

In addition, since MYC appears to require Notch signaling to induce  NE fate (cf Ireland et al), the presence of DAPT in culture could enrich for NE fate despite MYC's presence. It's important to clarify in the legend of Fig 4A which samples are used in the scRNA-seq data and whether they were derived from in vitro or in vivo conditions (as such, Supplementary Figure S1B should be provided in the main figure). Given their conclusion is confusing and challenges robustly supported data in other models, it is critical to resolve this issue properly. I suspect when properly resolved, MYC actually consistently does reduce NE fate compared to RP controls, even though tumors are still relatively NE compared to completely distinct cellular identities such as fibroblasts.

We have clarified the source of tumor sequencing data and the platform (single cell or bulk) in Figure 4 and Supplemental Figure 1. To reiterate – the RNA sequencing results from paired metastatic and primary tumors from the RPM model are derived from bulk RNA;  the single cell RNA data in RP or RPM datasets are from cells in culture.  These distinctions are clarified in the legend to Supplemental Figure 1.

(2) The rigor of the conclusions in Figure 1 would be strengthened by comparing an equivalent number of RP animals in the renal capsule assay, which is n = 6 compared to n = 11-14 in the MYC conditions.

As we did not perform a power calculation to determine a sample size required to draw a level of statistical significance from our conclusions, this comment is not entirely accurate. Our statistical rigor was limited by the availability of samples from the RP tumor model.

(3) Statistical analysis is not provided for Figures 2A-2B, and while the results are compelling, may be strengthened by additional samples due to the variability observed. 

We acknowledge that the cohorts are relatively small but we have added statistical comparisons in Figure 2B. 

(4a) Related to Figure 3, primary tumors and liver metastases from RPM or RPM-T58A-expressing cells express NEUROD1 by immunohistochemistry (IHC) but the putative negative controls (RP) are not shown, and there is no assessment of variability from tumor to tumor, ie, this is not quantified across multiple animals. 

The results of H&E and IF staining for ASCL1, NEUROD1, CGRP, and CD56 in negative control (RP tumors) are presented in the updated Figure 3F-G.

(4b) Relatedly, MYC has been shown to be able to push cells beyond NEUROD1 to a double-negative or YAP1+ state (Mollaoglu et al, Cancer Cell, 2017; Ireland et al, Cancer Cell, 2020), but the authors do not assess subtype markers by IHC. They do show subtype markers by mRNA levels in Fig 4B, and since there is expression of ASCL1, and potentially expression of YAP1 and POU2F3, it would be valuable to examine the protein levels by IHC in control RP vs. RPM samples.

YAP1 positive SCLC is still somewhat controversial, so it is not clear what value staining for YAP1 offers beyond showing the well-established markers, ASCL1 and NEUROD1.  

(5) Given that MYC has been shown to function distinctly from MYCL in SCLC models, it would have raised the impact and value of the study if MYC was compared to MYCL or MYCL fusions in this context since generally, SCLC expresses a MYC family member. However, it is quite possible that the control RP cells do express MYCL, and as such, it would be useful to show. 

We now include Supplemental Figure S2 to illustrate four important points raised by this reviewer and others:  1) expression of MYC family members in the merged dataset (RP and RPM) is low or undetectable in the basal/fibroblast cultures; 2) MYC does have a weak correlation with EGFP in the neuroendocrine cluster when either WT MYC or T58A MYC is overexpressed; 3) MYCL and MYCN are detectable, but at low levels compared to CMYC; and 4) Expression of  ASCL1 is anticorrelated with MYC expression across the merged single cell datasets using RP and RPM models.

Reviewer #3 (Public Review): 

Summary: 

The authors continue their study of the experimental model of small cell lung cancer (SCLC) they created from human embryonic stem cells (hESCs) using a protocol for differentiating the hESCs into pulmonary lineages followed by NOTCH signaling inactivation with DAPT, and then knockdown of TP53 and RB1 (RP models) with DOX inducible shRNAs. To this published model, they now add DOX-controlled activation of expression of a MYC or T58A MYC transgenes (RPM and RPMT58A models) and study the impact of this on xenograft tumor growth and metastases. Their major findings are that the addition of MYC increased dramatically subcutaneous tumor growth and also the growth of tumors implanted into the renal capsule. In addition, they only found liver and occasional lung metastases with renal capsule implantation. Molecular studies including scRNAseq showed that tumor lines with MYC or T58A MYC led surprisingly to more neuroendocrine differentiation, and (not surprisingly) that MYC expression was most highly correlated with NEUROD1 expression. Of interest, many of the hESCs with RPM/RPMT58A expressed ASCL1. Of note, even in the renal capsule RPM/RPMT58A models only 6/12 and 4/9 mice developed metastases (mainly liver with one lung metastasis) and a few mice of each type did not even develop a renal sub capsule tumor. The authors start their Discussion by concluding: " In this report, we show that the addition of an efficiently expressed transgene encoding normal or mutant human cMYC can convert weakly tumorigenic human PNEC cells, derived from a human ESC line and depleted of tumor suppressors RB1 and TP53, into highly malignant, metastatic SCLC-like cancers after implantation into the renal capsule of immunodeficient mice.". 

Strengths: 

The in vivo study of a human preclinical model of SCLC demonstrates the important role of c-Myc in the development of a malignant phenotype and metastases. Also the role of c-Myc in selecting for expression of NEUROD1 lineage oncogene expression. 

Weaknesses: 

There are no data on results from an orthotopic (pulmonary) implantation on generation of metastases; no comparative study of other myc family members (MYCL, MYCN); no indication of analyses of other common metastatic sites found in SCLC (e.g. brain, adrenal gland, lymph nodes, bone marrow); no studies of response to standard platin-etoposide doublet chemotherapy; no data on the status of NEUROD1 and ASCL1 expression in the individual metastatic lesions they identified. 

We have acknowledged from the outset that our study has significant limitations, as noted by this reviewer, and we explained in our initial letter of response why we need to present this limited, but still consequential, story at this time. 

In particular, while we have attempted orthotopic transplantations of RPM tumor cells into NSG mice (by tail vein or intra-pulmonary injection, or intra-tracheal instillation of tumor cells), these methods were not successful in colonizing the lung. Additionally, we have compared the efficacy of platinum/etoposide to that of removing DOX in established RPM subcutaneous tumors, but we chose not to include these data as we lacked a chemotherapy responsive tumor model, and thus could not say with confidence that the chemotherapeutic agants were active and that the RPM models were truly resistant to standard SCLC chemotherapy. In a discussion about other metastatic sites, we have now included the following text: 

“In animals administered DOX, histological examinations showed that approximately half developed metastases in distant organs, including the liver or lung (Figure 1D). No metastases were observed in the bone, brain, or lymph nodes. For a more detailed assessment, future studies could employ more sensitive imaging methods, such as luciferase imaging.”

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors): 

Technical points related to Major Weakness #1: 

For Figure 4: Cells were enriched for EGFP-high cells only, under the hypothesis that cells with lower EGFP may have silenced expression of the integrated vector. Since EGFP is expressed only in the shRB1 construct, selection for high EGFP may inadvertently alter/exclude heterogeneity within the transformed population for the other transgenes (shP53, shMYC/MYC-T58A). Can authors include data to show the expression of MYC/MYC T58A in EGFP-high v -med v-low cells? MYC levels may alter the NEdifferentiation status of tumor cells. 

Please now refer to Supplemental Figure S2.

Related to the appropriateness of the methods for Figure 4C, the authors state, "We performed differential cluster abundance analysis after accounting for the fraction of cells that were EGFP+". If only EGFP+ cells were accounted for in the analysis for 4C, the majority of RP cells in the "Neuroendocrine differentiated" cluster would not be included in the analysis (according to EGFP expression in Fig S1A-B), and therefore inappropriately reduce NE identity compared to RPM samples that have higher levels of EGFP. 

There is no consideration or analysis of cell cycling/proliferation until after the conclusion is stated. Yet, increased proliferation of MYC-high vs MYC-low cultures would enhance selection for more tumors (termed "NE-diff") than non-tumors (basal/fibroblast) in 2D cultures. 

The expression of MYC itself isn't assessed for this analysis but assumed, and whether higher levels of MYC/MYC-T58A may be present in EGFP+ tumor cells that are in the NE-low populations isn't clear. Can MYC-T58A/HA also be included in the reference genome? 

We did not include an HA tag in our reference transcriptome. For [some] answers to this and other related questions, please refer to Supplemental Figure S2.

Reviewer #3 (Recommendations For The Authors): 

(1) The experiments are all technically well done and clearly presented and represent a logical extension exploring the role of c-Myc in the hESC experimental model system. 

We appreciate this supportive comment!

(2) It is of great interest that both the initial RP model only forms "benign" tumors and that with the addition of a strong oncogene like c-myc, where expression is known to be associated with a very bad prognosis in SCLC, that while one gets tumor formation there are still occasional mice both for subcutaneous and renal capsule test sites that don't get tumors even with the injection of 500,000 RPM/RPMT58A cells. In addition, of the mice that do form tumors, only ~50% exhibit metastases from the renal sub-capsule site. The authors need to comment on this further in their Discussion. To me, this illustrates both how incredibly resistant/difficult it is to form metastases, thus indicating the need for other pathways to be activated to achieve such spread, and also represents an opportunity for further functional genomic tests using their preclinical model to systematically attack this problem. Obvious candidate genes are those recently identified in genetically engineered mouse models (GEMMs) related to neuronal behavior. In addition, we already know that full-fledged patient-derived SCLC when injected subcutaneously into immune-deprived mice don't exhibit metastases - thus, while the hESC RPM result is not surprising, it indicates to me the power of their model (logs less complicated genetically than a patient SCLC) to sort through a mechanism that would allow metastases to develop from subcutaneous sites. The authors can point these things out in their Discussion section to provide a "roadmap" for future research. 

Although we remain mindful of the relatively small cohorts we have studied, the thrust of Reviewer #3’s comments is now included in the Discussion. And there is, of course, a lot more to do, and it has taken several years already to get to this point. Additional information about the prolonged gestation of this project and about the difficulties of doing more in the near future was described in our initial response to reviewers/Editor, included near the start of this letter.    

(3) I will state the obvious that this paper would be much more valuable if they had compared and contrasted at least one of the myc family members (MYCL or MYCN) with the CMYC findings whatever the results would be. Most SCLC patients develop metastases, and most of their tumors don't express high levels of CMYC (and often use MYCL). In any event, as the authors Discuss, this will be an important next stage to test.

We have acknowledged and explained the limitations of the work in several ways. Further, we were unaware of the relationship between metastases and the expression of MYC and MYCL1 noted by the reviewer; we will look for confirmation of this association in any future studies, although we have not encountered it in current literature.

(4) Their assays for metastases involved looking for anatomically "gross" lesions. While that is fine, particularly given that the "gross" lesions they show in figures are actually pretty small, we still need to know if they performed straightforward autopsies on mice and looked for other well-known sites of metastases in SCLC patients besides liver and lung - namely lymph nodes, adrenal, bone marrow, and brain. I would guess these would probably not show metastatic growth but with the current report, we don't know if these were looked for or not. Again, while this could be a "negative" result, the paper's value would be increased by these simple data. Let's assume no metastases are seen, then the authors could further strengthen the case for the value of their hESC model in systematically exploring with functional genomics the requirements to achieve metastases to these other sites.

We have included descriptions of what we found and didn’t find at other potential sites of metastasis in the results section, with the following sentences: 

“In animals administered DOX, histological examinations showed that approximately half developed metastases in distant organs, including the liver or lung (Figure 1D). No metastases were observed in the bone, brain, or lymph nodes. For a more detailed assessment, future studies could employ more sensitive imaging methods, such as luciferase imaging.”

(5) Related to this, we have no idea if the mice that developed liver metastases (or the one mouse with lung metastasis) had more than one metastatic site. They will know this and should report it. Again, my guess is that these were isolated metastases in each mouse. Again, they can indicate the value of their model in searching for programs that would increase the number of the various organs. 

We appreciate the suggestion. We observed that one of the mice developed metastatic tumors in both the liver and lungs. This information has been incorporated into the Results section.

(6) While renal capsule implantation for testing growth and metastatic behavior is reasonable and based on substantial literature using this site for implantation of patient tumor specimens, what would have increased the value of the paper is knowing the results from orthotopic (lung implantation). Whatever the results were (they occurred or did not occur) they will be important to know. I understand the "future experiments" argument, but in reading the manuscript this jumped out at me as an obvious thing for the authors to try. 

We conducted orthotopic implantation several ways, including via intra-tracheal instillation of 0.5 million RP or RPM cells in PBS per mouse. However, none of the subjects (0/5 mice) developed tumor-like growths and the number of animals used was small. Further, this outcome could be attributed to biological or physical factors. For instance, the conducting airway is coated with secretory cells producing protective mucins and may not have retained the 0.5 million cells. This is one example that may have hindered effective colonization. Future adjustments, such as increasing the number of cells, embedding them in Matrigel, or damaging the airway to denude secretory cells and trigger regeneration might alter the outcomes. These ideas might guide future work to strengthen the utility of the models.

(7) Another obvious piece of data that would have improved the value of this manuscript would be to know whether the RPM tumors responded to platin-etoposide chemotherapy. Such data was not presented in their first RP hESC notch inhibition paper (which we now know generated what the authors call "benign" tumors). While I realize chemotherapy responses represent other types of experiments, as the authors point out one of the main reasons they developed their new human model was for therapy testing. Two papers in and we are all still asking - does their model respond or not respond dramatically to platin-etoposide therapy? Whatever the results are they are a vital next step in considering the use of their model. 

Please see the comments above regarding our decision not to include data from a clinical trial that lacked appropriate controls.

(8) The finding of RPM cells that expressed NEUROD1, ASCL1, or both was interesting. From the way the data were presented, I don't have a clear idea which of these lineage oncogenes the metastatic lesions from ~11 different mice expressed. Whatever the result is it would be useful to know - all NEUROD1, some ASCL1, some mixed etc.

Based on the bulk RNA-sequencing of a few metastatic sites (Figure 4H), what we can demonstrate is that all sites were NEUROD1 and expressed low or no detectable  ASCL1.

(9) While several H&E histologic images were presented, even when I enlarged them to 400% I couldn't clearly see most of them. For future reference, I think it would be important to have several high-quality images of the RP, RPM, RPMT58A subcutaneous tumors, sub-renal capsule tumors, and liver and lung metastatic lesions. If there is heterogeneity in the primary tumors or the metastases it would be important to show this. The quality of the images they have in the pdf file is suboptimal. If they have already provided higher-quality images - great. If not, I think in the long run as people come back to this paper, it will help both the field and the authors to have really great images of their tumors and metastases. 

We have attempted to improve the quality of the embedded images. Digital resolution is a tradeoff with data size – higher resolution images are always available upon request, but may not be suitable  for generation of figures in a manuscript viewed on-line.

Author response:

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

Reviewer 1 (Public Review):

Summary:

Here the authors convincingly identify and characterize the SERBP1 interactome and further define its role in the nucleus, where it is associated with complexes involved in splicing, cell division, chromosome structure, and ribosome biogenesis. Many of the SERBP1-associated proteins are RNA-binding proteins and SERBP1 exerts its impact, at least in part, through these players. SERBP1 is mostly disordered but along with its associated proteins displays a preference for G4 binding and can bind to PAR and be PARylated. They present data that strongly suggest that complexes in which SERBP1 participates are assembled through G4 or PAR binding. The authors suggest that because SERBP1 lacks traditional functional domains yet is clearly involved in distinct regulatory complexes, SERBP1 likely acts in the early steps of assembly through the recognition of interacting sites present in RNA, DNA, and proteins.

Strengths:

The data is very convincing and demonstrated through multiple approaches.

Weaknesses:

No weaknesses were identified by this reviewer.

Reviewer #2 (Public Review):

Summary:

In this study the authors have used pull-down experiments in a cell line overexpressing tagged SERPINE1 mRNA binding protein 1 (SERBP1) followed by mass spectrometry-based proteomics, to establish its interactome. Extensive analyses are performed to connect the data to published resources. The authors attempt to connect SERBP1 to stress granules and Alzheimer's disease-associated tau pathology. Based on the interactome, the authors propose a cross-talk between SERBP1 and PARP1 functions.

Strengths:

The main strength of this study lies in the proteomics data analysis, and its effort to connect the data to published studies.

Weaknesses:

While the authors propose a feedback regulatory model for SERBP1 and PARP1 functions, strong evidence for PARylation modulating SERBP1 functions is lacking. PARP inhibition decreasing the amount of PARylated proteins associated with SERBP1 and likely all other PARylated proteins is expected. This study is also incomplete in its attempt to establish a connection to Alzheimer's disease related tauopathy. A single AD case is not sufficient, and frozen autopsy tissue shows unexplained punctate staining likely due to poor preservation of cellular structures for immunohistochemistry. There is a lack of essential demographic data, source of the tissue, brain regions shown, and whether there was an IRB protocol for the human brain tissue. The presence of phase-separated transient stress granules in an autopsy brain is unlikely, even if G3BP1 staining is present. Normally, stress granule proteins move to the cytoplasm under cellular stress, whereas SERBP1 becomes nuclear. The co-localization of abundant cytoplasmic G3BP1 and SERBP1 under normal conditions does not indicate an association with stress granules.

Reviewer #3 (Public Review):

Summary:

A survey of SERBP1-associated functions and their impact on the transcriptome upon gene depletion, as well as the identification of chemical inhibitors upon gene over-expression.

Strengths:

(1) Provides a valuable resource for the community, supported by statistical analyses.

(2) Offers a survey of different processes with correlation data, serving as a good starting point for the community to follow up.

Weaknesses:

(1) The authors provided numerous correlations on diverse topics, from cell division to RNA splicing and PARP1 association, but did not follow up their findings with experiments, offering little mechanistic insight into the actual role of SERBP1. The model in Figure 5D is entirely speculative and lacks data support in the manuscript.

Our article includes several pieces of evidence that support SERBP1’s role in splicing, translation, cell division and association with PARP1. We respectfully disagree that the model in Figure 5D is speculative. The goal of our study was to generate initial evidence of SERBP1 involvement in different biological processes based on its interactome. The characterization of molecular mechanisms in all these scenarios requires a substantial amount work and will the topic of follow up manuscripts. 

(2) Following up with experiments to demonstrate that their findings are real (e.g., those related to splicing defects and the PARylation/PAR-binding association) would be beneficial. For example, whether the association between PARP1 and SERBP1 is sensitive to PAR-degrading enzymes is unclear.

We included experiments showing the interaction between endogenous SERBP1 and PARP1. Additionally, we demonstrated that SERBP1 interaction with PARP1 was disrupted when cells are treated with PARP inhibitors.

(3) They did not clearly articulate how experiments were performed. For instance, the drug screen and even the initial experiment involving the pull-down were poorly described. Many in the community may not be familiar with vectors such as pSBP or pUltra without looking up details.

We provided additional details about the vectors and expanded the description of experiments in results and figure legends.

(4) The co-staining of SERBP1 with pTau, PARP1, and G3BP1 in the brain is interesting, but it would be beneficial to follow up with immunoprecipitation in normal and patient samples to confirm the increased physical association.

Thank you for this suggestion. We performed instead a Proximity Ligation Assay (PLA) on human tissue. Data was included in Fig. 7B and C. PLA between pTau and SERBP1 confirmed interaction in AD cortices as well as SERBP1 with PARP1.

(5) The combination index of 0.7-0.9 for PJ34 + siSERBP1 is weak. Could this be due to the non-specific nature of the drug against other PARPs? Have the authors looked into this possibility?

The combination index could be considered weak in the case of U251 cells but not in the case of U343 cells. PJ34 has been shown to be mainly a PARP-1 inhibitor. Different PJ34 concentrations and different drugs will be examined in future studies. It is worth mentioning that in a genetic screening, SERBP1 has been shown to increase sensitivity to different PARP inhibitors (PMID: 37160887). This information is included in the manuscript.

Reviewer #1 (Recommendations For The Authors):

This is a really well-done piece of research that is written very well. The data are very convincing and the conclusions are well supported. Some wording in Figures 2B and D is pixelated and hard to read. All the figure legends could benefit from being expanded but this is especially true for Figures 2, 3, 7, and 8. There is a ton of data being presented and a very limited description of what was done and what is being concluded. Some of the content may not be fully comprehended by some readers with limited descriptions.

We revised all figures to assure images are clear and their resolution is high. We expanded all figure legends to provide a better explanation of the experimental design.

Reviewer #2 (Recommendations For The Authors):

The "merged" pdf file is the same as the "article".

Individual files were uploaded this time.

The abstract should spell out acronyms, such as the name of the protein Serpine1 mRNA-binding protein 1 (SERBP1).

This was not included since the abstract has a word limit.

"SERBP1 (Serpine1 mRNA-binding protein 1) is a unique member of this group of RBPs". In what way is it unique?

The text was modified to better explain SERBP1’s singularities.

"RBPs containing IDRs and RGG motifs are particularly relevant in the nervous system. Their misfolding contributes to the formation of pathological protein aggregates in Alzheimer's disease (AD), Frontotemporal Lobar Dementia (FTLD), Amyotrophic Lateral Sclerosis (ALS), and Parkinson's disease (PD)" -> while TDP-43 and FUS in ALS/FTD may fit this description, it is not true for tau and amyloid-beta (AD) and alpha-synuclein (PD).

"SERBP1 is a unique RBPs containing IDRs and RGG motifs yet lacks other readily recognizable, canonical or structured RNA binding motifs. Moreover, SERBP1 has been observed by our study and others as common Tau interactor in Alzheimer’s Disease (AD) brains. RBPs containing IDRs (e.g. TDP-43, FUS, hnRNPs, TIA1) have been shown self-aggregate and co-aggregate with pathogenic amyloids (Tau, Aβ-amyloid and α-Synuclein)  in AD, Frontotemporal Lobar Dementia (FTLD), Amyotrophic Lateral Sclerosis (ALS), and Parkinson's disease (PD) and this suggest that, like other IDRs RBPs, SERBP1 contributes to RNA dysmetabolism in neurodegenerative diseases”.

While the authors propose a feedback regulatory model for SERBP1 and PARP1 functions, strong evidence for PARylation modulating SERBP1 functions is lacking. The fact that PARP inhibition decreases the amount of PARylated proteins associated with SERBP1 and likely all other PARylated proteins is expected and cannot count as evidence.

We included data showing that treatment with PJ34 (PARP inhibitor) decreases SERBP1 interaction with PARP1 and G3BP1. We are currently conducting a more extensive analysis to identify SERBP1 PAR binding domain and the impact of PARP inhibition on its interactions and functions. These experiments will be included in a new manuscript.

A single AD case is not sufficient.

Sorry for the poor clarity. We included in the study 6 cases from age-matched controls and 6 cases of AD. We summarize all cases demographics, and the experimental application assigned to each case in Table 1. Moreover, we included a paragraph regarding Human tissue harvesting.

Most western blot data are not quantified from multiple replicates, as required.

Quantifications are now provided.

FTLD - frontotemporal lobar degeneration (not dementia).

This was corrected.

Frozen autopsy tissue is problematic due to poor preservation. The staining presented here shows unexplained punctate staining likely due to poor preservation of cellular structures for immunohistochemistry.

We included a paragraph regarding human tissue harvesting. We have successfully used frozen tissues in our previous studies, observing a well preserved neuronal and tissue structure (PMIDs: 32855391, 31532069 and 30367664)

The presence of phase-separated stress granules in tissue is controversial since these are transient structures.

Normally, stress granule proteins move to the cytoplasm under cellular stress, whereas SERBP1 becomes nuclear. The co-localization of abundant (and partially overexposed) cytoplasmic G3BP1 and SERBP1 under normal conditions is not evidence for association with stress granules. Does induction of stress granule formation lead to colocalization in stress granules? The H2O2 experiment suggests otherwise.

RBPs implicated in stress response move to stress granules when cells are exposed to stress. SERBP1 has been shown to shuttle to stress granules and nucleus in stress conditions (PMID: 24205981). Our results are in agreement.

Using co-IF, we observed some overlap between G3BP1 and SERBP1 in AD tissues. As shown in Fig. S6A and B, 50% of stress granules overlap with SERBP1 signal. On the contrary, it is hard to assess their relationship in aged-matched control brains where stress granules form and accumulate with a lower rate than in AD. SERBP1 is not very abundant in normal brains.  It is known that RNA-Binding Proteins aggregation and/or dysfunctional LLPS dysregulate stress granules formation and accumulation in AD and other proteinopathies (PMIDs 30853299, 27256390 and 31911437). However, it is too early to determine the role of SERBP1 and its contribution to stress granules formation and accumulation. We will examine this topic in future studies.

There is a lack of essential demographics data (age, clinical diagnosis, path diagnosis, co-pathologies, Braak stage, etc.), source of the tissue (what brain bank?), brain regions shown, and whether there was informed consent for the collection and use of human brain tissue.

We included the information requested in materials and methods section.

Reviewer #3 (Recommendations For The Authors):

The authors need to better explain their experimental rationale and approach in the main text, not just in the supplementary materials.

We have extensively revised the text to provide a better description of experiments in the results section and figure legends.

Author response:

Reviewer #1 (Public review):

Summary:

In cells undergoing Flavivirus infection, cellular translation is impaired but the viruses themselves escape this inhibition and are efficiently translated. In this study, the authors use very elegant and direct approaches to identify the regions in the 5' and 3' UTRs that are important for this phenomenon and then use them to retrieve two cellular proteins that associate with them and mediate translational shutoff evasion (DDX3 and PABP1). A number of experimental approaches are used with a series of well-controlled experiments that fully support the authors' conclusions.

Strengths:

The work identifies the regions in the 5' and 3' UTRs of the viral genome that mediate the escape of JEV from cellular transcriptional shutoff, they evaluate the infectivity of the mutant viruses bearing or not these structures and even explore their pathogenicity in mice. They then identify the cellular proteins that bind to these regions (DDX3 and PABP1) and determine their role in translation blockade escape, in addition to examining and assessing the conservation of the stem-loop identified in JEV in other Flaviviridae.

In almost all of their systematic analyses, translational effects are put in parallel with the replication kinetics of the different mutant viruses. The experimental thread followed in this study is rigorous and direct, and all experiments are truly well-controlled, fully supporting the authors' conclusions.

We greatly appreciate the reviewer's recognition of this study. We elucidated the role of UTR in translation blockade escape of JEV from the perspective of the RNA structure of the UTR and its interaction with host proteins (DDX3 and PABP1), and we hope that this study could gain wider recognition.

Reviewer #2 (Public review):

Summary:

The authors use a combination of techniques including viral genetics, in vitro reporters, and purified proteins and RNA to interrogate how the Japanese encephalitis virus maintains translation of its RNA to produce viral proteins after the host cell has shut down general translation as a means to block viral replication. They report a role for the RNA helicase DDX3 in promoting virus translation in a cap-independent manner through binding a dumbbell RNA structure in the 3' untranslated region previously reported to drive Japanese encephalitis virus cap-independent translation and a stem-loop at the viral RNA 5' end.

Strengths:

The authors clearly show that the Japanese encephalitis virus does not possess an IRES activity to initiate translation using a range of mono- and bi-cistronic mRNAs. Surprisingly, using a replicon system, the translation of a capped or uncapped viral RNA is reported to have the same translation efficiency when transfected into cells. The authors have applied a broad range of techniques to support their hypotheses.

We are grateful for the reviewer’s recognition of the thoroughness and multi-faceted nature of our study.

Weaknesses:

(1) The authors' original experiments in Figure 1 where the virus is recovered following transfection of in vitro transcribed viral RNA with alternative 5' ends such as capped or uncapped ignore that after a single replication cycle of that transfected RNA, the subsequent viral RNA will be capped by the viral capping proteins making the RNA in all conditions the same.

Thank you for your suggestion. We share the same viewpoint as the reviewer. After the first round of translation of the uncapped viral RNA, the subsequent viral RNA will inevitably be capped by the viral capping proteins. However, there is no doubt that the transfected cells do not contain viral capping proteins in the initial transfection stage, which directly proved that JEV possesses a cap-independent translation initiation mechanism.

(2) The authors report that deletion of the dumbbell and the large 3' stem-loop RNA reduce replication of a Japanese encephalitis virus replicon. These structures have been reported for other flaviviruses to be important respectively for the accumulation of short flaviviral RNAs that can regulate replication and stability of the viral RNA that lacks a polyA tail. The authors don't show any assessment of RNA stability or degradation state.

Thank you for your suggestion. We agree that a rigorous supplementary experiment for the assessment of RNA stability or degradation state is desirable. To address this, the relative amounts of viral RNA with the deletion of DB2 or sHP-SL will be determined by real-time RT-PCR analysis in transfected cells at multiple time points, which will allow us to test whether the deletion of the dumbbell and the large 3' stem-loop RNA reduce the RNA stability of JEV.

(3) The authors propose a model for DDX3 to drive 5'-3' end interaction of the Japanese encephalitis virus viral genome but no direct evidence for this is presented.

Thank you for your suggestion. In this study, we did not have direct evidence to suggest that DDX3 can drive the 5'-3' end interaction of the Japanese encephalitis virus viral genome, which is indeed a limitation of our research. In the revision, we will more explicitly discuss the interrelationship between DDX3 and 5'-3' UTR, as well as incorporate a discussion of these points into the main text, acknowledging the limitations of our current models.

(4) The authors' final model in Figure 10 proposes a switch from a cap-dependent translation system in early infection to cap-independent DDX3-driven translation system late in infection. The replicon data that measures translation directly however shows identical traces for capped and uncapped RNAs in all untreated conditions so that which mechanism is used at different stages of the infection is not clear.

Thank you for your suggestion. The replicon transfection system was used to evaluate the key viral element for cap-independent translation. We only monitored reporter gene expression from 2 hpt to 12 hpt, which can’t fully recapitulate the different stages of JEV infection. In the experimental results Figure 1 and Figure 1-figure supplement 1, we demonstrated that JEV significantly induced the host translational shutoff at 36 hpi, while the expression level of viral protein gradually increased as infection went on, suggesting that JEV translation could evade the shutoff of cap-dependent translation initiation at the late stage of infection. As shown in the growth curves in Figure 5Q, JEV replicated to similar virus titers in WT and DDX3-KO cells from 12 hpi to 36 hpi, but higher level virus yields were observed in WT cells from 48 hpi, suggesting that DDX3 is important for JEV infection at the late stage. DDX3 was demonstrated to be critical for JEV cap-independent translation. Based on these data, we proposed that the DDX3-dependent cap-independent translation is employed by JEV to maintain efficient infection at the late stage when the cap-dependent translation imitation was suppressed.

Reviewer #3 (Public review):

Summary:

This work is a valuable study that aims to decipher the molecular mechanisms underlying the translation process in Japanese encephalitis virus (JEV), a relevant member of the genus Flavivirus. The authors provide evidence that cap-independent translation, which has already been demonstrated for other flaviviruses, could also account in JEV. This process depends on the genomic 3' UTR, as previously demonstrated in other flaviviruses. Further, the authors find that cellular proteins such as DDX3 or PABP1 could contribute to JEV translation in a cap-independent way. Both DDX3 and PABP1 had previously been described to have a role in cellular protein synthesis and also in the translation step of other flaviviruses distinct from JEV; therefore, this work would expand the cap-independent translation in flaviviruses as a general mechanism to bypass the translation repression exerted by the host cell during viral infection. Further, the findings can be relevant for the development of specific drugs that could interfere with flaviviral translation in the future. Nevertheless, the conclusions are not fully supported by the provided results.

Strengths:

The results provide a good starting point to investigate the molecular mechanism underlying the translation in flaviviruses, which even today is an area of knowledge with many limitations.

Thank you to the reviewer for providing positive feedback. The research on the molecular mechanism underlying cap-independent translation is still a limited field in the flaviviruses, and its mechanism has not been well elucidated at present. We only hope that this study could reveal a novel mechanism of translation initiation for flaviviruses.

Weaknesses:

The main limit of the work is related to the fact that the role of the 3' UTR structural elements and DDX3 is not only circumscribed to translation, but also to replication and encapsidation. In fact, some of the provided results suggest this idea. Particularly, it is intriguing why the virus titer can be completely abrogated while the viral protein levels are only partially affected by the knockdown of DDX3. This points to the fact that many of the drawn conclusions could be overestimated or, at least, all the observed effect cannot be attributed only to the DDX3 effect on translation. Finally, it is noteworthy that the use of uncapped transcripts could be misleading, since this is not the natural molecular context of the viral genome.

Thank you for your suggestion. We agree with the reviewer's comments that the role of the 3' UTR structural elements and DDX3 may not only be circumscribed to translation. However, not as described by the reviewer, DDX3 knockdown did not completely abrogate JEV infection. As indicated in Figure 5E-5F, the recombinant virus was successfully rescued at 36 hpt and 48 hpt using the uncapped viral genomic RNA, although the viral titer rescued with the uncapped genomic RNA at 24 hpt was below the limit of detection. We have confirmed that the DB2 and sHP-SL elements in 3' UTR play a decisive role in the replication of viral RNA in our research (Figure 2G and Figure 2-figure supplement 4C), and we will further analyze the role of DDX3 in viral RNA replication and encapsidation, thereby clarifying the multiple functions of DDX3 in JEV life cycle. Meanwhile, we will incorporate a discussion of these points into the main text, acknowledging the limitations of our current research.

To eliminate the misleading effects of using uncapped transcripts, we will use a natural molecular background of the viral genome with cap methylation deficiency. The methyltransferase (MTase) of the flavivirus NS5 protein catalyzes  N-7 and 2’-O methylations in the formation of the 5’-end cap of the genome, and the E218 amino acid of the NS5 protein MTase domain is one of the active sites of flavivirus methyltransferase (PLoS Pathogens. 2012. PMID:22496660; Journal of Virology. 2007. PMID: 1866096). We will construct a mutant virus of the E218A mutation to abolish 2'-O methylation activity and significantly reduce N-7 methylation activity and then analyze the roles of UTR structure and DDX3 in recombinant viruses with the type-I cap structure functional deficiency.

Author response:

Reviewer #1 (Public review):

Summary:

The authors revealed the cellular heterogeneity of companion cells (CCs) and demonstrated that the florigen gene FT is highly expressed in a specific subpopulation of these CCs in Arabidopsis. Through a thorough characterization of this subpopulation, they further identified NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT. Overall, these findings are intriguing and valuable, contributing significantly to our understanding of florigen and the photoperiodic flowering pathway. However, there is still room for improvement in the quality of the data and the depth of the analysis. I have several comments that may be beneficial for the authors.

Strengths:

The usage of snRNA-seq to characterize the FT-expressing companion cells (CCs) is very interesting and important. Two findings are novel: 1) Expression of FT in CCs is not uniform. Only a subcluster of CCs exhibits high expression level of FT. 2) Based on consensus binding motifs enriched in this subcluster, they further identify NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT.

We are pleased to hear that reviewer 1 noted the novelty and importance of our work. As reviewer 1 mentioned, we are also excited about the identification of a subcluster of companion cells with very high FT expression. We believe that this work is an initial step to describe the molecular characteristics of these FT-expressing cells. We are also excited to share our new findings on NIGT1_s as potential _FT regulators. We think that this finding attracts broader audiences, as the molecular factor that coordinates plant nutrition status with flowering time remains largely unknown despite its well-known plant phenomenon.

Weaknesses:

(1) Title: "A florigen-expressing subpopulation of companion cells". It is a bit misleading. The conclusion here is that only a subset of companion cells exhibit high expression of FT, but this does not imply that other companion cells do not express it at all.

We agree with this comment, as we also did not intend to say that FT is not produced in other companion cells than the subpopulation we identified. We will revise the title to more accurately reflect the point.

(2) Data quality: Authors opted for fluorescence-activated nuclei sorting (FANS) instead of traditional cell sorting method. What is the rationale behind this decision? Readers may wonder, especially given that RNA abundance in single nuclei is generally lower than that in single cells. This concern also applies to snRNA-seq data. Specifically, the number of genes captured was quite low, with a median of only 149 genes per nucleus. Additionally, the total number of nuclei analyzed was limited (1,173 for the pFT:NTF and 3,650 for the pSUC2:NTF). These factors suggest that the quality of the snRNA-seq data presented in this study is quite low. In this context, it becomes challenging for the reviewer to accurately assess whether this will impact the subsequent conclusions of the paper. Would it be possible to repeat this experiment and get more nuclei?

We appreciate this comment; we noticed that we did not clearly explain the rationale of using single-nucleus RNA sequencing (snRNA-seq) instead of single-cell RNA-seq (scRNA-seq). As reviewer 1 mentioned, RNA abundance in scRNA-seq is higher than in snRNA-seq. To conduct scRNA-seq using plant cells, protoplasting is the necessary step. However, in our study, protoplasting has many drawbacks in isolating our target cells from the phloem. It is technically challenging to efficiently isolate protoplasts from highly embedded phloem companion cells from plant tissues. Usually, it requires a minimum of several hours of enzymatic incubation to protoplast companion cells and the efficiencies of protoplasting these cells are still low. For our analysis, restoring the time information within a day is also crucial. Therefore, we performed more speedy isolation method. In the revision, we will explain our rationale of choosing snRNA-seq due to the technical limitations.

Here, reviewer 1 raised a concern about the quality of our snRNA-seq data, referring to the relatively low readcounts per nucleus. Although we believe that shallow reads do not necessaryily indicate low quality and are confident in the accuracy of our snRNA-seq data, as supported by the detailed follow-up experiments (e.g., imaging analysis in Fig. 4B), we agree that it is important to address this point in the revision and alleviate readers’ concerns regarding the data quality.

(3) Another disappointment is that the authors did not utilize reporter genes to identify the specific locations of the FT-high expressing cells (cluster 7 cells) within the CC population in vivo. Are there any discernible patterns that can be observed?

As we previously showed only limited spatial images of overlap between FT-expressing cells and other cluster 7 gene-expressing cells in Fig. 4B, this comment is understandable. To respond to it, we will include whole leaf images of FT- and cluster 7 gene-expressing cells to assess the spatial overlaps between FT and cluster 7 genes within a leaf.

(4) The final disappointment is that the authors only compared FT expression between the nigtQ mutants and the wild type. Does this imply that the mutant does not have a flowering time defect particularly under high nitrogen conditions?

To answer this question, we will include the flowering time measurement data of the nigtQ mutants grown on the soil with sufficient nitrogen sources.

Reviewer #2 (Public review):

This manuscript submitted by Takagi et al. details the molecular characterization of the FT-expressing cell at a single-cell level. The authors examined what genes are expressed specifically in FT-expressing cells and other phloem companion cells by exploiting bulk nuclei and single-nuclei RNA-seq and transgenic analysis. The authors found the unique expression profile of FT-expressing cells at a single-cell level and identified new transcriptional repressors of FT such as NIGT1.2 and NIGT1.4.

Although previous researchers have known that FT is expressed in phloem companion cells, they have tended to neglect the molecular characterization of the FT-expressing phloem companion cells. To understand how FT, which is expressed in tiny amounts in phloem companion cells that make up a very small portion of the leaf, can be a key molecule in the regulation of the critical developmental step of floral transition, it is important to understand the molecular features of FT-expressing cells in detail. In this regard, this manuscript provides insight into the understanding of detailed molecular characteristics of the FT-expressing cell. This endeavor will contribute to the research field of flowering time.

We are grateful that reviewer 2 recognizes the importance of transcriptome profiling of FT-expressing cells at the single-cell level.

Here are my comments on how to improve this manuscript.

(1) The most noble finding of this manuscript is the identification of NTGI1.2 as the upstream regulator of FT-expressing cluster 7 gene expression. The flowering phenotypes of the nigtQ mutant and the transgenic plants in which NIGT1.2 was expressed under the SUC2 gene promoter support that NIGT1.2 functions as a floral repressor upstream of the FT gene. Nevertheless, the expression patterns of NIGT1.2 genes do not appear to have much overlap with those of NIGT1.2-downstream genes in the cluster 7 (Figs S14 and F3). An explanation for this should be provided in the discussion section.

We agree reviewer 2 that spatial expression patterns of NIGT1.2 and cluster 7 genes do not overlap much, and some discussion should be provided in the manuscript. Although we do not have a concrete answer for this phenomenon, NIGT1.2 may suppress FT gene expression in non-cluster 7 cells to prevent the misexpression of FT. Another possible explanation is that NIGT1.2 negatively affects the formation of cluster 7 cells. If so, cells with high NIGT1.2 gene expression hardly become cluster 7 cells. We will discuss it further in the discussion section in our revised manuscript.

(2) To investigate gene expression in the nuclei of specific cell populations, the authors generated transgenic plants expressing a fusion gene encoding a Nuclear Targeting Fusion protein (NTF) under the control of various cell type-specific promoters. Since the public audience would not know about NTF without reading reference 16, some explanation of NTF is necessary in the manuscript. Please provide a schematic of constructs the authors used to make the transformants.

As reviewer 2 pointed out, we lacked a clear explanation why we used NTF in this study. NTF is the fusion protein that consists of a nuclear envelope targeting domain, GFP, and biotin acceptor peptide. It was originally designed for the INTACT (isolation of nuclei tagged in specific cell types) method that enables us to isolate bulk nuclei from specific tissues. Although our original intention was profiling the bulk transcriptome of mRNAs that exist in nuclei of the FT-expressing cells using INTACT, we utilized our NTF transgenic lines for snRNA-seq analysis. To explain what NTF is to readers, we will include a schematic diagram of NTF.

Author response:

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

We have carefully addressed all the reviewers' suggestions, and detailed responses are provided at the end of this letter. In summary:

• We conducted two additional replicates of the study to obtain more robust and reliable data.

• The Introduction has been revised for greater clarity and conciseness.

• The Results section was shortened and reorganized to highlight the key findings more effectively.

• The Discussion was modified according to the reviewers' suggestions, with a focus on reorganization and conciseness.

We hope you find this revised version of the manuscript satisfactory.

Reviewer #1 (Public Review):

Summary:

This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.

Strengths:

Host blood meal source, temperature, and photoperiod were all examined together.

Weaknesses:

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.

Comments on the revision: 

Overall, I am not quite convinced about the possible shift in host use in the Argentinian populations of Cx. quinquefasciatus. The evidence from the papers that the authors cite is not strong enough to derive this conclusion. Therefore, I think that the introduction and discussion parts where they talk about host shift in Cx. quinquefasciatus should be removed completely as it misleads the readers. I suggest limiting the manuscript to talking only about the effects of blood meal source and seasonality on the reproductive outcomes of Cx. quinquefasciatus. 

As mentioned in the previous revision, we agree on the reviewer observation about the lack of evidence on seasonal shift in the host use pattern in Cx. quinquefasciatus populations from Argentina. We include this topic in the discussion.

Additionally, we also added a paragraph in the discussion section to include the limitations of our study and conclusions. One of them is the fact that our results are based on controlled conditions experiments. Future studies are needed to elucidate if the same trend is found in the field.

Reviewer #1 (Recommendations for the authors): 

Abstract

Line 73: shift in feeding behavior

Accepted as suggested. 

Discussion

Line 258: addressed that Accepted as suggested.

Line 263: blood is nutritionally richer

Accepted as suggested.

Reviewer #2 (Public Review): 

Summary:

Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness on birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used a generalized linear model to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity, fertility, and hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite from that hypothesized. The authors have done a very good job of addressing many of the reviewer concerns, with several exception that continue to cause concern about the conclusions of the study. 

Strengths:

(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.

(2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field. 

(3) The manuscript has become a lot clearer and easier to read with the revisions - thank you to the authors for working hard to make many of the suggested changes. 

Weaknesses:

(1) The authors have decided not to follow the suggestion of conducting experimental replicates of the study. This is understandable given the significant investment of resources and time necessary, however, it leaves the study lacking support. Experimental replication is an important feature of a strong study and helps to provide confidence that the observed patterns are real and replicable. Without replication, I continue to lack confidence in the conclusions of the study. 

We included replicates as suggested.  

(2) The authors have included some additional discussion about the counterintuitive nature of their results, but the paragraph discussing this in the discussion was confusing. I believe that this should be revised. This is a key point of the paper and needs to be clear to the reader.

Revised as suggested. 

(3) There should be more discussion of the host switching observed in the two studies conducted in Argentina referenced by the authors. Since host switching is the foundation for the hypothesis tested in this paper, it is important to fully explain what is currently known in Argentina. 

Accepted as suggested.

(4) In some cases, the explanations of referenced papers are not entirely accurate. For example, when referencing Erram et al 2022, I think the authors misrepresented the paper's discussion regarding pre-diuresis- Erram et al. are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility (rather than leading to higher fecundity on birds, as stated in this manuscript). The study performed by Erram et al. also didn't prove this phenomenon, they just suggest it as a possible mechanism to explain their results, so that should be made clear when referencing the paper. 

Changed as suggested.

(5) In some cases, the conclusions continue to be too strongly worded for the evidence available. For example, lines 322-324: I don't think the data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness. 

Redaction was modified as suggested to tight our discussion with results.

(6) There is limited mention of the caveat that this experiment performed with simulated seasonality that does not perfectly replicate seasonality in the field. I think this caveat should be discussed in the discussion (e.g. that humidity is held constant).

This topic is now included in the discussion as suggested. 

Reviewer #2 (Recommendations for the authors): 

59-60: These terms should end with -phagic instead of -philic. These papers study blood feeding patterns, not preference. I understand that the Janssen papers calls it "mammalophilic" in their title, but this was an incorrect use of the term in their paper. There are some review papers that explain the difference in this terminology if it's helpful.

Accepted as suggested. 

73: edit to "in" feeding behavior 

Accepted as suggested.

77-78: Given that the premise of your study is based on the phenomenon of host switching, I suggest that you expand your discussion of these two papers. What did they observe? Which hosts did they switch from / to and how dramatic was the shift?

Accepted as suggested. 

79: replace acknowledged with experienced 

Accepted as suggested.

79-80: the way that this is written is misleading. It suggests that Spinsanti showed that seasonal variation in SLEV could be attributed to a host shift, which isn't true. This citation should come before the comma and then you should use more cautious language in the second half. E.g which MIGHT be possible to attribute to .... 

Accepted as suggested.

80-82: this is not convincing. Even if the Robin isn't in Argentina, Argentina does have migrating birds, so couldn't this be the case for other species of birds? Do any of the birds observed in previous blood meal analyses in Argentina migrate? If so, couldn't this hypothesis indeed play a role? 

A paragraph about this topic was added to the discussion as suggested.

90: hypotheses for what? The fall peak in cases? Or host switching? 

Changed to be clearer.

98: where was this mentioned before? I think "as mentioned before" can be removed. 

Accepted as suggested.

101: edit to "whether an interaction effect exists" 

Accepted as suggested.

104: edit to "We hypothesize that..." 

Accepted as suggested.

106: reported host USE changes, not host PREFERENCE changes, right? 

All the terminology was change to host pattern and not preference to avoid confusion.

200: Briefly reading Carsey and Harden, it looks like the methodology was developed for social science. Is there anything you can cite to show this applied to other types of data? If not, I think this requires more explanation in your MS. 

This was removed as replicates were included.

237-239: I think it is best not to make a definitive statement about greater/higher if it isn't statistically significant; I suggest modifying the sentences to state that the differences you are listing were not significantly different up front rather than at the end, otherwise if people aren't reading carefully, they may get the wrong impression. 

Accepted as suggested.

245: you only use the term MS-I once before and I forgot what it meant since it wasn't repeated, so I had to search back through with command-F. I suggest writing this out rather than using the acronym. 

Accepted as suggested.

249: edit to: "an interaction exists between the effect of..." 

Accepted as suggested.

253-254: greater compared to what? 

Change for clearness. 258-260: edit for grammar 

Accepted as suggested.

260-262: edit for grammar; e.g. "However, this assumption lacks solid evidence; there is a scarcity of studies regarding nutritional quality of avian blood and its impact on mosquito fitness." 

Accepted as suggested.

263: edit: blood is nutritionally... 

Accepted as suggested.

264-267: This doesn't sound like an accurate interpretation of what the paper suggests regarding pre-diuresis in their discussion - they are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility. They also don't show this, they just suggest it as a possible mechanism to explain their results. 

This topic was removed given the restructuring of discussion.

253-269: You should tie this paragraph back to your results to explicitly compare/contrast your findings with the previous literature. 

Accepted as suggested.

270-282: This paragraph would be a good place to explain the caveat of working in the laboratory - for example, humidity was the same across the two seasons which I'm guessing isn't the case in the field in Argentina. You can discuss what aspects of laboratory season simulation do not accurately replicate field conditions and how this can impact your findings. You said in your response to the reviewers that you weren't interested in measuring other variables (which is fair, and not expected!), but the beauty of the discussion section is to be able to think about how your experimental design might impact your results - one possibility is that your season simulation may not have produced the results produced by true seasonal shifts. 

Accepted as suggested.

279-281: You say your experiment was conducted within the optimal range, which would suggest that both summer and autumn were within that range, but then you only talk about summer as optimal in the following sentence. 

Changed for clearness.

281-282: You should clarify this sentence - state what the interaction has an effect on. 

Accepted as suggested.

283-291: I appreciate that your discussion now acknowledges the small sample size and the questions that remain unanswered due to the results being opposite to that of the hypothesis, but this paragraph lacks some details and in places doesn't make sense. 

I think you need to emphasize which groups had small sample size and which conclusions that might impact. I also think you need to explain why the sample size was substantially smaller for some groups (e.g. did they refuse to feed on the mouse in the autumn?). I appreciate that sample sizes are hard to keep high across many groups and two gonotrophic periods, but unfortunately, that is why fitness experiments are so hard to do and by their nature, take a long time. I understand that other papers have even lower sample size, but I was not asked to review those papers and would have had the same critique of them. I don't believe that creating simulated data via a Monte Carlo approach can make up for generating real data. As I understand it from your explanation, you are parametrizing the Monte Carlo simulations with your original data, which was small to begin with for autumn mouse. Using this simulation doesn't seem like a satisfactory replacement for an experimental replicate in my opinion. I maintain that at least a second replicate is necessary to see whether the patterns that you have observed hold. 

The performing of a power analysis and addition of more replicates tried to solve the issue of sample size. More about this critic is added in the discussion. The simulation approach was totally removed.

Regarding the directionality of the interaction effect, I think this warrants more discussion. Lines 287-291 don't make sense to me. You suggest that feeding on birds in the autumn may confer a reproductive advantage when conditions are more challenging. But then why wouldn't they preferentially feed on birds in the autumn, rather than mammals? I suggest rewriting this paragraph to make it clearer. 

Accepted as suggested.

297: earlier mentioned treatments? Do you mean compared to the first gonotrophic cycle? This isn't clear. 

Changed for clearness.

302-303: Did you clarify whether you are allowed to reference unpublished data in eLife? 

This was removed to follow the guidelines of eLife.

316-317: "it becomes apparent" sounds awkward, I suggest rewording and also explaining how this conclusion was made. 

Accepted as suggested.

322-324: I think that this statement is too strongly worded. I don't think your data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness. Please modify this and make your conclusions more cautious and closely linked to what you actually demonstrated. 

Accepted as suggested.

325: change will perform to would have 

Accepted as suggested.

326: add to the sentence: "and vice versa in the summer" 

Accepted as suggested.

330: possible explanations, not explaining scenarios. 

Accepted as suggested.

517: I think you should repeat the abbreviation definitions in the caption to make it easier for readers, otherwise they have to flip back and forth which can be difficult depending on formatting.

Accepted as suggested. 

In general, I think that your captions need more information. I think the best captions explain the figure relatively thoroughly such that the reader can look at the figure and caption and understand without reading the paper in depth. (e.g. the statistical test used).

Data availability: The eLife author instructions do say that data must be made available, so there should be a statement on data availability in your MS. I also suggest you make the code available.

Accepted as suggested.

Author response:

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

Reviewer #1 (Public Review):

Summary:

BMP signaling is, arguably, best known for its role in the dorsoventral patterning, but not in nematodes, where it regulates body size. In their paper, Vora et al. analyze ChIP-Seq and RNA-Seq data to identify direct transcriptional targets of SMA-3 (Smad) and SMA-9 (Schnurri) and understand the respective roles of SMA-3 and SMA-9 in the nematode model Caenorhabditis elegans. The authors use publicly available SMA-3 and SMA-9 ChIP-Seq data, own RNA-Seq data from SMA-3 and SMA-9 mutants, and bioinformatic analyses to identify the genes directly controlled by these two transcription factors (TFs) and find approximately 350 such targets for each. They show that all SMA-3-controlled targets are positively controlled by SMA-3 binding, while SMA-9-controlled targets can be either up or downregulated by SMA-9. 129 direct targets were shared by SMA-3 and SMA-9, and, curiously, the expression of 15 of them was activated by SMA-3 but repressed by SMA-9. Since genes responsible for cuticle collagen production were eminent among the SMA-3 targets, the authors focused on trying to understand the body size defect known to be elicited by the modulation of BMP signaling. Vora et al. provide compelling evidence that this defect is likely to be due to problems with the BMP signaling-dependent collagen secretion necessary for cuticle formation.

We thank the reviewer for this supportive summary. We would like to clarify the status of the publicly available ChIP-seq data. We generated the GFP tagged SMA-3 and SMA‑9 strains and submitted them to be entered into the queue for ChIP-seq processing by the modENCODE (later modERN) consortium. Thus, the publicly available SMA-3 and SMA-9 ChIP-seq datasets used here were derived from our efforts.  Due to the nature of the consortium’s funding, the data were required to be released publicly upon completion. Nevertheless, our current manuscript provides the first comprehensive analysis of these datasets. We have updated the text to clarify this point.

Strengths:

Vora et al. provide a valuable analysis of ChIP-Seq and RNA-Seq datasets, which will be very useful for the community. They also shed light on the mechanism of the BMP-dependent body size control by identifying SMA-3 target genes regulating cuticle collagen synthesis and by showing that downregulation of these genes affects body size in C. elegans.

Weaknesses:

(1) Although the analysis of the SMA-3 and SMA-9 ChIP-Seq and RNA-Seq data is extremely useful, the goal "to untangle the roles of Smad and Schnurri transcription factors in the developing C. elegans larva", has not been reached. While the role of SMA-3 as a transcriptional activator appears to be quite straightforward, the function of SMA-9 in the BMP signaling remains obscure. The authors write that in SMA-9 mutants, body size is affected, but they do not show any data on the mechanism of this effect.

We thank the reviewer for directing our attention to the lack of clarity about SMA-9’s function. We have revised the text to highlight what this study and others demonstrate about SMA-9’s role in body size. Simply stated, SMA-9 is needed together with SMA-3 to promote the expression of genes involved in one-carbon metabolism, collagens, and chaperones, all of which are required for body size. SMA-3 has additional, SMA-9-independent transcriptional targets, including chaperones and ER secretion factors, that also contribute to body size. Finally, SMA-9 regulates additional targets independent of SMA-3 that likely have a minimal role in body size. We have adjusted Figure 5 with new graphs of the original data to make these points more clear.

(2) The authors clearly show that both TFs can bind independently of each other, however, by using distances between SMA-3 and SMA-9 ChIP peaks, they claim that when the peaks are close these two TFs act as complexes. In the absence of proof that SMA-3 and SMA-9 physically interact (e.g. that they co-immunoprecipitate - as they do in Drosophila), this is an unfounded claim, which should either be experimentally substantiated or toned down.

We acknowledge that we have not demonstrated a physical interaction between SMA-3 and SMA-9 through a co-immunoprecipitation, and we have indicated in the text that a formal biochemical demonstration would be required to make this point. Moreover, we toned down the text by stating that our results suggest that either SMA-3 and SMA-9 frequently bind as either subunits in a complex or in close vicinity to each other along the DNA. As the reviewer has indicated, a physical interaction between Smads and Schnurris has been amply demonstrated in other systems. A limitation in these previous studies is that only a small number of target genes were analyzed. Our goal in this study was to determine how widespread this interaction is on a genomic scale. Our analyses demonstrate for the first time that a Schnurri transcription factor has significant numbers of both Smad-dependent and Smad-independent target genes. We have revised the text to clarify this point.

(3) The second part of the paper (the collagen story) is very loosely connected to the first part. dpy-11 encodes an enzyme important for cuticle development, and it is a differentially expressed direct target of SMA-3. dpy-11 can be bound by SMA-9, but it is not affected by this binding according to RNA-Seq. Thus, technically, this part of the paper does not require any information about SMA-9. However, this can likely be improved by addressing the function of the 15 genes, with the opposing mode of regulation by SMA-3 and SMA-9.

We appreciate this suggestion and have clarified in the text how SMA-9 contributes to collagen organization and body size regulation.

(4) The Discussion does not add much to the paper - it simply repeats the results in a more streamlined fashion.

We thank the reviewer for this suggestion. We have added more context to the Discussion.

Reviewer #2 (Public Review):

In the present study, Vora et al. elucidated the transcription factors downstream of the BMP pathway components Smad and Schnurri in C. elegans and their effects on body size. Using a combination of a broad range of techniques, they compiled a comprehensive list of genome-wide downstream targets of the Smads SMA-3 and SMA-9. They found that both proteins have an overlapping spectrum of transcriptional target sites they control, but also unique ones. Thereby, they also identified genes involved in one-carbon metabolism or the endoplasmic reticulum (ER) secretory pathway. In an elaborate effort, the authors set out to characterize the effects of numerous of these targets on the regulation of body size in vivo as the BMP pathway is involved in this process. Using the reporter ROL-6::wrmScarlet, they further revealed that not only collagen production, as previously shown, but also collagen secretion into the cuticle is controlled by SMA-3 and SMA-9. The data presented by Vora et al. provide in-depth insight into the means by which the BMP pathway regulates body size, thus offering a whole new set of downstream mechanisms that are potentially interesting to a broad field of researchers.

The paper is mostly well-researched, and the conclusions are comprehensive and supported by the data presented. However, certain aspects need clarification and potentially extended data.

(1) The BMP pathway is active during development and growth. Thus, it is logical that the data shown in the study by Vora et al. is based on L2 worms. However, it raises the question of if and how the pattern of transcriptional targets of SMA-3 and SMA-9 changes with age or in the male tail, where the BMP pathway also has been shown to play a role. Is there any data to shed light on this matter or are there any speculations or hypotheses?

We agree that these are intriguing questions, and we are interested in the roles of transcriptional targets at other developmental stages and in other physiological functions, but these analyses are beyond the scope of the current study.

(2) As it was shown that SMA-3 and SMA-9 potentially act in a complex to regulate the transcription of several genes, it would be interesting to know whether the two interact with each other or if the cooperation is more indirect.

A physical interaction between Smads and Schnurri has been amply demonstrated in other systems. Our goal in this study was not to validate this physical interaction, but to analyze functional interactions on a genome-wide scale.

(3) It would help the understanding of the data even more if the authors could specifically state if there were collagens among the genes regulated by SMA-3 and SMA-9 and which.

We thank the reviewer for this suggestion. col-94 and col-153 were identified as direct targets of both SMA-3 and SMA-9. We noted this in the Discussion.

(4) The data on the role of SMA-3 and SMA-9 in the regulation of the secretion of collagens from the hypodermis is highly intriguing. The authors use ROL-6 as a reporter for the secretion of collagens. Is ROL-6 a target of SMA-9 or SMA-3? Even if this is not the case, the data would gain even more strength if a comparable quantification of the cuticular levels of ROL-6 were shown in Figure 6, and potentially a ratio of cuticular versus hypodermal levels. By that, the levels of secretion versus production can be better appreciated.

We previously showed that rol-6 mRNA levels are reduced in dbl-1 mutants at L2, but RNA-seq analysis did not find enough of a statistically significant change in rol-6 to qualify it as a transcriptional target and total levels of protein are also not significantly reduced in mutants. We added this information in the text.

(5) It is known that the BMP pathway controls several processes besides body size. The discussion would benefit from a broader overview of how the identified genes could contribute to body size. The focus of the study is on collagen production and secretion, but it would be interesting to have some insights into whether and how other identified proteins could play a role or whether they are likely to not be involved here (such as the ones normally associated with lipid metabolism, etc.).

We have added more information to the Discussion.

Reviewer #1 (Recommendations For The Authors):

Figure 1 - Figure 3: The authors might want to think about condensing this into two figures.

To avoid confusion with the different workflows, we prefer to keep these as three separate figures.

Figure 1a-b: Measurement unit missing on X.

We added the unit “bps” to these graphs.

Line 244-246: The authors should stress in the Results that they analyzed publicly available ChIP-Seq data, which was not generated by them, - not just by providing a reference to Kudron et al., 2018. As far as I understood, ChIP was performed with an anti-GFP antibody. Please mention this, and specify the information about the vendor and the catalog number in the Methods.

We would like to clarify the status of the publicly available ChIP-seq data. We generated the GFP tagged SMA-3 and SMA‑9 strains and submitted them to be entered into the queue for ChIP-seq processing by the modENCODE (later modERN) consortium. Thus, the publicly available SMA-3 and SMA-9 ChIP-seq datasets used here were derived from our efforts.  Due to the nature of the consortium’s funding, the data were required to be released publicly upon completion. Nevertheless, our current manuscript provides the first comprehensive analysis of these datasets. We have clarified these issues in the text.  We have also added information regarding the anti-GFP antibody to the Methods.

Line 267-270: The authors should either provide experimental evidence that SMA-3 and SMA-9 form complexes or write something like "significant overlap between SMA-3 and SMA-9 peaks may indicate complex formation between these two transcription factors as shown in Drosophila" - but in the absence of proof, this must be a point for the Discussion, not for the Results. Moreover, similar behavior of fat-6 (overlapping ChIP peaks) and nhr-114 (non-overlapping ChIP peaks) in SMA-3 and SMA-9 mutants may be interpreted as a circumstantial argument against SMA-3/SMA-9 complex formation (see Lines 342-348). Importantly, since ChIP-Seq data are available for a wide array of C. elegans TFs, it would be very useful to have an estimate of whether SMA-3/SMA-9 peak overlap is significantly higher than the peak overlap between SMA-3 and several other TFs expressed at the same L2 stage.

We have clarified our goals regarding SMA-3 and SMA-9 interactions and softened our conclusions by indicating in the text that a formal biochemical demonstration would be required to demonstrate a physical interaction. Moreover, we toned down the text by stating that our results suggest that either SMA-3 and SMA-9 frequently bind as either subunits in a complex or in close vicinity to each other along the DNA. We have added an analysis of HOT sites to address overlap of binding with other transcription factors. We disagree with the interpretation that transcription factors with non-overlapping sites cannot act together to regulate gene expression; however, nhr-114 also has an overlapping SMA-3 and SMA-9 site, so this point becomes less relevant. We have clarified the categorization of nhr-114 in the text.

Lines 272-292: The authors do not comment on the seemingly quite small overlap between the RNA-Seq and the ChIP-Seq dataset, but I think they should. They have 3205 SMA-3 ChIP peaks and 1867 SMA-3 DEGs, but the amount of directly regulated targets is 367. It is important that the authors provide information on the number of genes to which their peaks have been assigned. Clearly, this will not be one gene per peak, but if it were, this would mean that just 11.5% of bound targets are really affected by the binding. The same number would be 4.7% for the SMA-9 peaks.

We have added a discussion of the discrepancy between binding sites and DEGs. The high number of additional sites classified as non-functional could represent the detection of weak affinity targets that do not have an actual biological purpose. Alternatively, these sites could have an additional role in DBL-1 signaling besides transcriptional regulation of nearby genes, or they could be regulating the expression of target genes at a far enough distance to not be detected by our BETA analysis as per the constraints chosen for the analysis. The difference between total binding sites and those associated with changes in gene expression underscores the importance of combining RNA-seq with ChIP-seq to identify the most biologically relevant targets. And as the reviewer indicated, more than one gene can be assigned to a single neighboring peak.

Lines 294-323: I feel like there is a terminology problem, which makes reading very difficult. The authors use "direct targets" as bound genes with significant expression change, but then run into a problem when the gene is bound by SMA-9 and SMA-3, but significant expression change is only associated with one of the two factors. I am not sure this is consistent with the idea of the SMA3/SMA9 complex. Also, different modalities of the SMA3 and SMA9 effect in 15 cases can be explained by co-factors. Reading would be also simplified if the order of the panels in Figure 3 were different. Currently, the authors start their explanation by referring to the shared SMA-3/SMA-9 targets (Figures 3c-d), and only later come to Figure 3b. In general, the authors should start with a clear explanation of what is on the figure (currently starting on Line 313), otherwise, it is unclear why, if the authors only discuss common targets, it is not just 114+15=129 targets, but more.

We have re-ordered the columns in Figure 3 to match the order discussed in the text. We also incorporated more precise language about regulation by SMA-3 and/or SMA-9 in the text.

Lines 325-355: The chapter has a rather unfortunate name "Mechanisms of integration of SMA-3 and SMA-9 function", although the authors do not provide any mechanism. Using 3 target genes, they show that if the regulatory modality of SMA-3 and SMA-9 is the same (2 examples), there is no difference in the expression of the targets, but if the modalities are opposing (1 example), SMA-9 repressive action is epistatic to the SMA-3 activating action. Can this be generalized? The authors should test all their 15 targets with opposite regulations. Moreover, it seems obvious to ask whether the intermediate phenotype of the double-mutants can be attributed to the action of these 15 genes activated by SMA-3 and repressed by SMA-9. I would suggest testing this by RNAi. I would also suggest renaming the chapter to something better reflecting its content.

We have removed the word “mechanism” from the title of this section. We also performed additional RT-PCR experiments on another 5 targets with opposing directions of regulation. The results from these genes are consistent with the result from C54E4.5, demonstrating that the epistasis of sma-9 is generalizable.

Figure 4b: Why was a two-way ANOVA performed here? With the small number of measurements, I would consider using a non-parametric test.

These data are parametric and the distribution of the data is normal, so we chose to use a parametric test (ANOVA).

Lines 354-355. The authors offer two suggestions for the mechanism of the epistatic action of SMA-9 on SMA-3 in the case of C54E4.5, but this is something for the Discussion. If they want to keep it in the Results they should address this experimentally by performing SMA-3 ChIP-seq in the SMA-9 mutants and SMA-9 ChIP-Seq in the SMA-3 mutants.

We moved these models to the discussion as suggested.

Lines 365-367: "We expect that clusters of genes involved in fatty acid metabolism and innate immunity mediate the physiological functions of BMP signaling in fat storage and pathogen resistance, respectively." - This is pretty confusing since the Authors claim in the previous sentence that regulation of immunity by SMA-9 is TGF-beta independent.

Co-regulation of immunity by BMP signaling and SMA-9 is already known. The novel insight is that SMA-9 may have an additional independent role in immunity. We have clarified the language to address this confusion.

Lines 377, and 380: Please explain in non-C. elegans-specific terminology, what rrf-3 and LON-2 are (e.g. write "glypican LON-2" instead of just "LON-2") and add relevant references.

We added information on the proteins encoded by these genes.

Lines 382-384: I am not sure what the Authors mean here by "more limiting".

We substituted the phrase “might have a more prominent requirement in mediating the exaggerated growth defect of a lon-2 mutant”.

Lines 388-392: I found this very confusing. What were these 36 genes? Were these direct targets of SMA-3, SMA-9, or both? Top 36 targets? 36 targets for which mutants are available?

The new Figure 5 clarifies whether target genes are SMA-3-exclusive, SMA-9-exclusive, or co-regulated. The text was also updated for clarity.

Line 397: This is the first time the authors mention dpy-11 but they do not say what it is until later, and they do not say whether it is a target of SMA3/SMA9. Checking Figure 3, I found that it is among the 238 genes bound by both but upregulated only by SMA3. The authors need to explicitly state this - from this point on, they have a section for which SMA-9 appears to be irrelevant.

We added the molecular function of dpy-11 at its first mention. Furthermore, we included the hypothesis that SMA-3 may regulate collagen secretion independently of SMA-9. Our subsequent results with sma-9 mutants disprove this hypothesis.

Line 402: Is ROL-6 a SMA-3/SMA-9 target or just a marker gene?

We previously showed that rol-6 mRNA levels are reduced in dbl-1 mutants at L2, but RNA-seq analysis did not find enough of a statistically significant change in rol-6 to qualify it as a transcriptional target and total levels of protein are also not significantly reduced in mutants. We added this information in the text.

Line 421: I am not sure what "more skeletonized" means.

Replaced with “thinner and skeletonized”

Figure 2b and 2d legends: "Non-target genes nevertheless showing differential expression are indicated with green squares." (l. 581-582 and again l. 588-589) I think should be "Non-direct target genes...".

Changed to “non-direct target genes”

Figure 7 legend: Please indicate the scale bar size in the legend.

Indicated the scale bar size in the legend.

Figure 7: The ER marker is referred to as "ssGFP::KDEL" (in the image and Line 700), however in the text it is called "KDEL::oxGFP" (Line 419). Please use consistent naming.

We fixed the inconsistent naming.

All the experiment suggestions made are optional and can, in principle, be ignored if the authors tone down their claims (for example, the SMA-3/SMA-9 complex formation).

Reviewer #2 (Recommendations For The Authors):

(1) As a control: Have the authors found the known regulated genes among the differentially regulated ones?

Previously known target genes such as fat-6 and zip-10 were identified here. We have added this information in the text.

(2) How many repetitions were performed in Figure 4b? I am wondering as the deviation for C54E4.5 is quite large and that makes me worry that the significant differences stated are not robust.

There were two biologically independent collections from which three cDNA syntheses were analyzed using two technical replicates per point.

(3) Lines 333-336: Can you really make this claim that the antagonistic effects seen in the regulation of body size can be correlated with some targets being regulated in the opposite direction? I would assume that the situation is far more complex as SMADs also regulate other processes.

We agree with the reviewer that multiple models could explain this antagonism, and we have added distinct alternatives in the text.

(4) Lines 367-369: Add the respective reference please.

We have added the relevant references.

Author response:

We are both honored and humbled by the high praise our work received from all three reviewers. Below, we address the common comments made by the reviewers:

(1) Value and Impact of the Resource: We are grateful for the recognition of our dataset as a valuable and high-quality resource. Our primary goal was to generate a comprehensive dataset on protein abundance and phosphorylation dynamics during Xenopus oocyte maturation. We are pleased that this work has been seen as a solid foundation for future studies in Xenopus research and beyond, with broader implications for oocyte and cell cycle biology.

(2) Focus on Functional Validation and Contextualization with Prior Studies: The manuscript was submitted as a Tools and Resources article, a format that emphasizes the creation and presentation of datasets, tools, and methodological advances to facilitate future discoveries. In alignment with this format, we ensured that the information is accessible and deployable for the broader scientific community. While we did not include functional validation of specific pathways, the dataset provides a robust framework for generating numerous testable hypotheses. We plan to pursue some of these follow-up studies in our labs and encourage the community to explore these further.

(3) Contextualization with Prior Studies: We appreciate the recognition of our efforts to integrate our findings with the existing body of literature. In conclusion, we would like to thank the reviewers for their evaluation and thoughtful suggestions. We look forward to seeing how this dataset contributes to future discoveries in the field.

Author response:

eLife Assessment:

In this important study, the authors combine innovative experimental approaches, including direct compressibility measurements and traction force analyses, with theoretical modeling to propose that wild-type cells exert compressive forces on softer HRasV12-transformed cells, influencing competition outcomes. The data generally provide solid evidence that transformed epithelial cells exhibit higher compressibility than wild-type cells, a property linked to their compaction during mechanical cell competition. However, the study would benefit from further characterization of how compression affects the behavior of HRasV12 cells and clearer causal links between compressibility and competition outcomes.

We thank the reviewers and the editor for their thoughtful and encouraging feedback on our study and for appreciating the innovation in our experimental and theoretical approaches. We acknowledge the importance of further clarifying the mechanistic links between the compressibility of HRas^V12-transformed cells, their compaction, and the outcomes of mechanical cell competition. In the revised manuscript, we will include additional experiments and analyses to assess how compression influences the cellular behavior and fate of HRas^V12-transformed cells during competition. In addition, to strengthen the connection between collective compressibility and competition outcomes, we will integrate quantitative analyses of cell dynamics and additional modeling to explicitly correlate the mechanical properties with the spatial and temporal aspects of cell elimination. These additions will address the reviewer’s concerns comprehensively, further enriching the mechanistic understanding presented in the manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this article, Gupta and colleagues explore the parameters that could promote the elimination of active Ras cells when surrounded by WT cells. The elimination of active Ras cells by surrounding WT cells was previously described extensively and associated with a process named cell competition, a context dependant elimination of cells. Several mechanisms have been associated with competition, including more recently elimination processes based on mechanical stress. This was explored theoretically and experimentally and was either associated with differential growth and sensitivity to pressure and/or differences in homeostatic density/pressure. This was extensively validated for the case of Scribble mutant cells which are eliminated by WT MDCK cells due to their higher homeostatic density. However, there has been so far very little systematic characterisation of the mechanical parameters and properties of these different cell types and how this could contribute to mechanical competition.

Here, the authors used the context of active Ras cells in MDCK cells (with some observations in vivo in mice gut which are a bit more anecdotal) to explore the parameters causal to Ras cell elimination. Using for the first time traction force microscopy, stress microscopy combined with Bayesian inference, they first show that clusters of active Ras cells experience higher pressure compared to WT. Interestingly, this occurs in absence of differences in growth rate, and while Ras cells seems to have lower homeostatic density, in contractions with the previous models associated with mechanical cell competition. Using a self-propelled Voronoi model, they explored more systematically the conditions that will promote the compression of transformed cells, showing globally that higher Area compressibility and/or lower junctional tension are associated with higher compressibility. Using then an original and novel experimental method to measure bulk compressibility of cell populations, they confirmed that active Ras cells are globally twice more compressible than WT cells. This compressibility correlates with a disruption of adherens junctions. Accordingly, the higher pressure near transformed Ras cells can be completely rescued by increasing cell-cell adhesion through E-cad overexpression, which also reduces the compressibility of the transformed cells. Altogether, these results go along the lines of a previous theoretical work (Gradeci et al. eLife 2021) which was suggesting that reduced stiffness/higher compressibility was essential to promote loser cell elimination. Here, the authors provide for the first time a very convincing experimental measurement and validation of this prediction. Moreover, their modelling approach goes far beyond what was performed before in terms of exploration of conditions promoting compressibility, and their experimental data point at alternative mechanisms that may contribute to mechanical competition.

Strengths:

- Original methodologies to perform systematic characterisation of mechanical properties of Ras cells during cell competition, which include a novel method to measure bulk compressibility.<br /> - A very extensive theoretical exploration of the parameters promoting cell compaction in the context of competition.

We thank the reviewer for their detailed and thoughtful assessment of our study and for recognizing the originality of our methodologies, including the novel bulk compressibility measurement technique and the extensive theoretical exploration of parameters influencing mechanical competition. We are pleased that the reviewer finds our experimental validation and modeling approach convincing and acknowledges the relevance of our findings in advancing the understanding of mechanical cell competition. We will carefully address all the points raised to further clarify and strengthen the manuscript.

Weaknesses:

- Most of the theoretical focus is centred on the bulk compressibility, but so far does not really explain the final fate of the transformed cells. Classic cell competition scenario (including the one involving active Ras cells) lead to the elimination of one cell population either by cell extrusion/cell death or global delamination. This aspect is absolutely not explored in this article, experimentally or theoretically, and as such it is difficult to connect all the observables with the final outcome of cell competition. For instance, higher compressibility may not lead to loser status if the cells can withstand high density without extruding compared to the WT cells (and could even completely invert the final outcome of the competition). Down the line, and as suggested in most of the previous models/experiments, the relationship between pressure/density and extrusion/death will be the key factor that determine the final outcome of competition. However, there is absolutely no characterisation of cell death/cell extrusion in the article so far.

We thank the reviewer for highlighting this important point. We agree that understanding the relationship between pressure, density, and the final outcomes of cell competition, such as extrusion and cell death, is crucial to connecting the mechanical properties to competition outcomes. While extrusion and cell death have been extensively characterized in previous works (e.g., https://www.nature.com/articles/s41467-021-27896-z; https://www.nature.com/articles/ncb1853), we nevertheless recognize the need to address this aspect more explicitly in our study. To this end, we have indeed performed experiments to characterize cell extrusion and cell death under varying conditions of pressure and density. We will incorporate these data into the revised manuscript. These additions will provide a more comprehensive understanding of how mechanical imbalance drives cell competition and determine the final fate of transformed cells.

- While the compressibility measurement are very original and interesting, this bulk measurement could be explained by very different cellular processes, from modulation of cell shape, to cell extrusion and tissue multilayering (which by the way was already observed for active Ras cells, see for instance https://pubmed.ncbi.nlm.nih.gov/34644109/). This could change a lot the interpretation of this measurement and to which extend it can explain the compression observed in mixed culture. This compressibility measurement could be much more informative if coupled with an estimation of the change of cell aspect ratio and the rough evaluation of the contribution of cell shape changes versus alternative mechanisms.

We thank the reviewer for raising this important concern. In our model system and within the experimental timescale of our studies involving gel compression microscopy (GCM) experiments, we do not observe tissue multilayering and cell extrusion, as these measurements are performed on homogeneous populations (pure wild-type or pure transformed cell monolayer). However, to address the reviewer’s suggestion, we will include measurements of cell aspect ratio as well as images eliminating the possibility of multilayering/extrusion in the revised manuscript. These results will provide additional insights into the plausible contributions of cell shape changes. Furthermore, our newer results indicate that the compressibility differences arise from variations in the intracellular organization (changed in nuclear and cytoskeletal organization) between wild-type and transformed cells. While a detailed molecular characterization of these underlying mechanisms is beyond the scope of the current manuscript, we acknowledge its importance and plan to explore it in a future study. These revisions will clarify and strengthen the interpretation of our findings.

- So far, there is no clear explanation of why transformed Ras cells get more compacted in the context of mixed culture compared to pure Ras culture. Previously, the compaction of mutant Scribble cells could be explained by the higher homeostatic density of WT cells which impose their prefered higher density to Scribble mutant (see Wagstaff et al. 2016 or Gradeci et al 2021), however that is not the case of the Ras cells (which have even slightly higher density at confluency). If I understood properly, the Voronoid model assumes some directional movement of WT cell toward transformed which will actively compact the Ras cells through self-propelled forces (see supplementary methods), but this is never clearly discussed/described in the results section, while potentially being one essential ingredient for observing compaction of transformed cells. In fact, this was already described experimentally in the case of Scribble competition and associated with chemoattractant secretion from the mutant cells promoting directed migration of the WT (https://pubmed.ncbi.nlm.nih.gov/33357449/). It would be essential to show what happens in absence of directional propelled movement in the model and validate experimentally whether there is indeed directional movement of the WT toward the transformed cells. Without this, the current data does not really explain the competition process.

We introduced directional movement of wild-type cells towards neighbouring transformed cells (and a form of active force to be exerted by them), motivated by the tissue compressibility measurements from the Gel Compression Microscopy experiments (Fig. 4E-L). This allowed us to devise an equivalent method of measuring the material response to isotropic compression within the SPV model framework. While the role of directional propelled movement is an area of ongoing investigation and has not been explored extensively within the current study, we emphasize that even without directional propulsion in the model, our results demonstrate compressive stress or elevated pressure, and increased compaction within the transformed population under suitable conditions reported in this work (when k<1), exhibiting a greater tissue-level compressibility in the transformed cells compared to WT cells (Figs. 4C-D), thereby laying the ground for competition. To clarify these concerns, we will provide additional results as well as detailed discussions on the effect of cell movements in compression.

- Some of the data lack a bit of information on statistic, especially for all the stress microscopy and traction forces where we do no really know how representative at the stress patterns (how many experiment, are they average of several movies ? integrated on which temporal window ?)

We thank the reviewer for highlighting the need for additional details regarding the statistical representation of our stress microscopy and traction force data. We will address these concerns in the revised manuscript by providing clear descriptions of the number of experiments, the averaging methodology, and the temporal windows used for analysis. Currently, Figs. 2A and 2C represent data from single time points, as the traction and stress landscapes evolve dynamically as transformed cells begin extruding (as shown in Supplementary movie 1). In contrast, Fig. 2H represents data collected from several samples across three independent experiments, all measured at the 3-hour time point following doxycycline induction. This specific time point is critical because it captures the emergence of compressive stresses before extrusion begins, simplifying the analysis and ensuring consistency. We will ensure these details are clearly articulated in the revised text and figure legends.

Reviewer #2 (Public review):

The work by Gupta et al. addresses the role of tissue compressibility as a driver of cell competition. The authors use a planar epithelial monolayer system to study cell competition between wild type and transformed epithelial cells expressing HRasV12. They combine imaging and traction force measurements from which the authors propose that wild type cells generate compressive forces on transformed epithelial cells. The authors further present a novel setup to directly measure the compressibility of adherent epithelial tissues. These measurements suggest a higher compressibility of transformed epithelial cells, which is causally linked to a reduction in cell-cell adhesion in transformed cells. The authors support their conclusions by theoretical modelling using a self-Propelled Voronoi model that supports differences in tissue compressibility can lead to compression of the softer tissue type.

The experimental framework to measure tissue compressibility of adherent epithelial monolayers establishes a novel tool, however additional controls of this measurement appear required. Moreover, the experimental support of this study is mostly based on single representative images and would greatly benefit from additional data and their quantitative analysis to support the authors' conclusions. Specific comments are also listed in the following:

Major points:

It is not evident in Fig2A that traction forces increase along the interface between wild type and transformed populations and stresses in Fig2C also seem to be similar at the interface and surrounding cell layer. Only representative examples are provided and a quantification of sigma_m needs to be provided.

In Figure 1-3 only panel 2G and 2H provide a quantitative analysis, but it is not clear how many regions of interest and clusters of transform cells were quantified.

We thank the reviewer for their detailed comments and for highlighting the importance of additional quantitative analyses to support our conclusions. We appreciate their recognition of our novel experimental framework to measure tissue compressibility and the overall approach of our study. Regarding Fig. 2A and Fig. 2C, we acknowledge the need for further clarity. While the traction forces and stress patterns may not appear uniformly distinct at the interface in the representative images, these differences are more evident at specific time points before extrusion begins. Please note that the traction and stress landscapes evolve dynamically as transformed cells begin extruding (as shown in Supplementary movie 1). We will include a quantification of σ_m​ and additional data from multiple experiments to substantiate the observations and address this concern in the revised manuscript. Currently, the data in Fig. 2G and Fig. 2H represent several regions of interest and transformed cell clusters collected from three independent experiments, all analyzed at the 3-hour time point after doxycycline induction. This time point was chosen because it captures the compressive stress emergence without interference from extrusion processes, simplifying the analysis. We will expand these sections with detailed descriptions of the sample sizes and statistical analyses to ensure greater transparency and reproducibility. These revisions will provide a stronger quantitative foundation for our findings and address the reviewer's concerns.

Several statements appear to be not sufficiently justified and supported by data.<br /> For example the statement on pg 3. line 38 seems to lack supportive data 'This comparison revealed that the thickness of HRasV12-expressing cells was reduced by more than 1.7-fold when they were surrounded by wild type cells. These observations pointed towards a selective, competition-dependent compaction of HRasV12-expressing transformed cells but not control cells, in the intestinal villi of mice.'  Similarly, the statement about a cell area change of 2.7 fold (pg 3 line 47) lacks support by measurements.

We thank the reviewer for pointing out the need for more supportive data to justify several statements in the manuscript. Specifically, the observation regarding the reduction in the thickness of HRas^V12-expressing cells by more than 1.7-fold when surrounded by wild-type cells, and the statement about a 2.7-fold change in cell area, will be supported by detailed measurements. In the revised manuscript, we will include quantitative analyses with additional figures that clearly document these changes. These figures will provide representative images, statistical summaries, and detailed descriptions of the measurements to substantiate these claims. We appreciate the reviewer highlighting these areas and will ensure that all statements are robustly backed by data.

What is the rationale for setting 𝐾p = 1 in the model assumptions if clear differences in junctional membranes of transformed versus wild type cells occur, including dynamic ruffling? This assumption does not seem to be in line with biological observations.

While the specific role of K_p in the differences observed in the junctional membranes of transformed versus WT cells, including dynamical ruffling, is not directly studied in this work, our findings indicate that the lower junctional tension (weaker and less stable cellular junctions) in mutant cells is influenced primarily by competition in the dimensionless cell shape index within the model. This also suggests a larger preferred cell perimeter (P₀) for mutant cells, corresponding to their softer, unjammed state. Huang et al. (https://doi.org/10.1039/d3sm00327b) have previously argued that a high P₀ may, in some cases, result from elevated cortical tension along cell edges, or reflect weak membrane elasticity, implying a smaller K_p. While this connection could be an intriguing avenue for future exploration, we emphasize that K_p is not expected to alter any of the key findings or conclusions reported in this work. We will include any required analysis and corresponding discussions in the revised manuscript.

The novel approach to measure tissue compressibility is based on pH dependent hydrogels. As the pH responsive hydrogel pillar is placed into a culture medium with different conditions, an important control would be if the insertion of this hydrogel itself would change the pH or conditions of the culture assays and whether this alters tissue compressibility or cell adhesion. The authors could for example insert a hydrogel pillar of a smaller diameter that would not lead to compression or culture cells in a larger ring to assess the influence of the pillar itself.

We appreciate the reviewer’s insightful comment regarding the potential effects of the pH-responsive hydrogel pillar on the culture conditions and tissue compressibility. In our experiments, the expandable hydrogels are kept separate from the cells until the pH of the hydrogel is elevated to 7.4, ensuring that the hydrogel does not impact the culture environment. However, we acknowledge the concern and will include additional controls in the revised manuscript. Specifically, we will insert a hydrogel pillar with a smaller diameter that would not induce compression on culture cells in a larger ring to assess any potential influence of the hydrogel pillar itself. This will help to further validate our experimental setup.

The authors focus on the study of cell compaction of the transformed cells, but how does this ultimately lead to a competitive benefit of wild type cells? Is a higher rate of extrusion observed and associated with the compaction of transformed cells or is their cell death rate increased? While transformed cells seem to maintain a proliferative advantage it is not clear which consequences of tissue compression ultimately drive cell competition between wild type and transformed cells.

We thank the reviewer for highlighting this important point. We agree that understanding how tissue compression leads to a competitive advantage for wild type cells is crucial. While our current study focuses on the mechanical properties of transformed cells leading to the compaction and subsequent extrusion of the transformed cells, we recognize the need to explicitly connect these properties to the final outcomes of cell competition, such as extrusion or cell death. Although extrusion and cell death have been extensively characterized in previous studies (e.g., https://www.nature.com/articles/s41467-021-27896-z; https://www.nature.com/articles/ncb1853), we have indeed performed additional experiments to investigate the relationship between pressure, density, and these processes in our system. In the revised manuscript, we will include these new data, which will help to clarify how mechanical stress, driven by tissue compression, contributes to the competition between wild type and transformed cells and influences their eventual fate.

The argumentation that softer tissues would be more easily compressed is plausible. However, which mechanism do the authors suggest is generating the actual compressive stress to drive the compaction of transformed cells? They exclude a proliferative advantage of wild type cells, which other mechanisms will generate the compressive forces by wild type cells?

We thank the reviewer for raising this important question. As rightly pointed out by the reviewer indeed in our model system, we do not observe a proliferative advantage for the wild-type cells, and the compressive forces exerted by the wild-type cells are due to their intrinsic mechanical properties, such as lesser compressibility compared to the transformed cells. This difference in compressibility results in wild-type cells generating compressive stress at the interface with the transformed cells. Regarding the mechanism underlying the increased compressibility of the transformed cells, our newer findings indicate that the differences in compressibility arise from variations in the intracellular organization, specifically changes in nuclear and cytoskeletal organization between wild-type and transformed cells. While a detailed molecular characterization of these mechanisms is beyond the scope of the current manuscript, we acknowledge its significance and plan to investigate it in future work. We will, nevertheless, include a detailed discussion on the mechanism underlying the differential compressibility of wild-type and transformed cells in the revised manuscript.

Author response:

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

The revised manuscript contains new results and additional text. Major revisions:

(1) Additional simulations and analyses of networks with different biophysical parameters and with identical time constants for E and I neurons (Methods, Supplementary Fig. 5).

(2) Additional simulations and analyses of networks with modifications of connectivity parameters to further analyze effects of E/I assemblies on manifold geometry (Supplementary Fig. 6).

(3) Analysis of synaptic current components (Figure 3 D-F; to analyze mechanism of modest amplification in Tuned networks). 

(4) More detailed explanation of pattern completion analysis (Results).

(5) Analysis of classification performance of Scaled networks (Supplementary Fig.8).

(6) Additional analysis (Figure 5D-F) and discussion (particularly section “Computational functions of networks with E/I assemblies”) of functional benefits of continuous representations in networks with E-I assemblies. 

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing. 

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks. 

Strengths: 

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models. 

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation. 

(2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.  (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model. 

Weaknesses: 

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model. 

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper. 

We agree that further mechanistic insights would be of interest and addressed this issue at different levels:

(1) Biophysical parameters: to determine whether network behavior depends on specific choices of biophysical parameters in E and I neurons we equalized biophysical parameters across neuron types. The main observations are unchanged, suggesting that the observed effects depend primarily on network connectivity (see also response to comment [2]).

(2) Mechanism of modest amplification in E/I assemblies: analyzing the different components of the synaptic currents demonstrate that the modest amplification of activity in Tuned networks results from an “imperfect” balance of recurrent excitation and inhibition within assemblies (see new Figures 3D-F and text p.7). Hence, E/I co-tuning substantially reduces the net amplification in Tuned networks as compared to Scaled networks, thus preventing discrete attractor dynamics and stabilizing network activity, but a modest amplification still occurs, consistent with biological observations.

(3) Representational geometry: to obtain insights into the network mechanisms underlying effects of E/I assemblies on the geometry of population activity we tested the hypothesis that geometrical changes depend, at least in part, on the modest amplification of activity within E/I assemblies (see Supplementary Figure 6). We changed model parameters to either prevent the modest amplification in Tuned networks (increasing I-to-E connectivity within assemblies) or introduce a modest amplification in subsets of neurons by other mechanisms (concentration-dependent increase in the excitability of pseudo-assembly neurons; Scaled I networks with reduced connectivity within assemblies). Manipulations that introduced a modest, input-dependent amplification in neuronal subsets had geometrical effects similar to those observed in Tuned networks, whereas manipulations that prevented a modest amplification abolished these effects (Supplementary Figure 6). Note however that these manipulations generated different firing rate distributions. These results provide a starting point for more detailed analyses of the relationship between network connectivity and representational geometry (see p.12).

In summary, our additional analyses indicate that effects of E/I assemblies on representational geometry depend primarily on network connectivity, rather than specific biophysical parameters, and that the resulting modest amplification of activity within assemblies makes an important contribution. Further analyses may reveal more specific relationships between E/I assemblies and representational geometry, but such analyses are beyond the scope of this study.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.  

We thank the reviewer for raising this point. We chose a relatively slow time constant for excitatory synapses because experimental data indicate that excitatory synaptic currents in Dp and piriform cortex contain a prominent NMDA component. Nevertheless, to assess whether network behavior depends on specific choices of biophysical parameters in E and I neurons, we have performed additional simulations with equal synaptic time constants and equal biophysical parameters for all neurons. Each neuron also received the same number of inputs from each population (see revised Methods). Results were similar to those observed previously (Supplementary Fig.5 and p.9 of main text). We therefore conclude that the main effects observed in Tuned networks cannot be explained by differences in biophysical parameters between E and I neurons but is primarily a consequence of network connectivity.

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning. 

One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function. 

In the previous manuscript, the analysis of potential computational benefits other than pattern classification was limited and the discussion of this issue was condensed into a single itemized paragraph to avoid excessive speculation. Although a thorough analysis of potential computational benefits exceeds the scope of a single paper, we agree with the reviewer that this issue is of interest and therefore added additional analyses and discussion.

In the initial manuscript we analyzed pattern classification primarily to investigate whether Tuned networks can support this function at all, given that they do not exhibit discrete attractor states. We found this to be the case, which we consider a first important result.

Furthermore, we found that precise balance of E/I assemblies can protect networks against catastrophic firing rate instabilities when assemblies are added sequentially, as in continual learning. Results from these simulations are now described and discussed in more detail (see Results p.11 and Discussion p.13).

In the revised manuscript, we now also examine additional potential benefits of Tuned networks and discuss them in more detail (see new Figure 5D-F and text p.11). One hypothesis is that continuous representations provide a distance metric between a given input and relevant (learned) stimuli. To address this hypothesis, we (1) performed regression analysis and (2) trained support vector machines (SVMs) to predict the concentration of a given odor in a mixture based on population activity. In both cases, Tuned E+I networks outperformed Scaled and _rand n_etworks in predicting the concentration of learned odors across a wide range mixtures (Figure 5D-F).  E/I assemblies therefore support the quantification of learned odors within mixtures or, more generally, assessments of how strongly a (potentially complex) input is related to relevant odors stored in memory. Such a metric assessment of stimulus quality is not well supported by discrete attractor networks because inputs are mapped onto discrete network states.

The observation that Tuned networks do not map inputs onto discrete outputs indicates that such networks do not classify inputs as distinct items. Nonetheless, the observed geometrical modifications of continuous representations support the classification of learned inputs or the assessment of metric relationships by hypothetical readout neurons. Geometrical modifications of odor representations may therefore serve as one of multiple steps in multi-layer computations for pattern classification (and/or other computations). In this scenario, the transformation of odor representations in Dp may be seen as related to transformations of representations between different layers in artificial networks, which collectively perform a given task (notwithstanding obvious structural and mechanistic differences between artificial and biological networks). In other words, geometrical transformations of representations in Tuned networks may overrepresent learned (relevant) information at the expense of other information and thereby support further learning processes in other brain areas. An obvious corollary of this scenario is that Dp does not perform odor classification per se based on inputs from the olfactory bulb but reformats representations of odor space based on experience to support computational tasks as part of a larger system. This scenario is now explicitly discussed (p.14).

Reviewer #2 (Public Review): 

Summary: 

The authors conducted a comparative analysis of four networks, varying in the presence of excitatory assemblies and the architecture of inhibitory cell assembly connectivity. They found that co-tuned E-I assemblies provide network stability and a continuous representation of input patterns (on locally constrained manifolds), contrasting with networks with global inhibition that result in attractor networks. 

Strengths: 

The findings presented in this paper are very interesting and cutting-edge. The manuscript effectively conveys the message and presents a creative way to represent high-dimensional inputs and network responses. Particularly, the result regarding the projection of input patterns onto local manifolds and continuous representation of input/memory is very Intriguing and novel. Both computational and experimental neuroscientists would find value in reading the paper. 

Weaknesses: 

that have continuous representations. This could also be shown in Figure 5B, along with the performance of the random and tuned E-I networks. The latter networks have the advantage of providing network stability compared to the Scaled I network, but at the cost of reduced network salience and, therefore, reduced input decodability. The authors may consider designing a decoder to quantify and compare the classification performance of all four networks. 

We have now quantified classification by networks with discrete attractor dynamics (Scaled) along with other networks. However, because the neuronal covariance matrix for such networks is low rank and not invertible, pattern classification cannot be analyzed by QDA as in Figure 5B. We therefore classified patterns from the odor subspace by template matching, assigning test patterns to one of the four classes based on correlations (see Supplementary Figure 8). As expected, Scaled networks performed well, but they did not outperform Tuned networks. Moreover, the performance of Scaled networks, but not Tuned networks, depended on the order in which odors were presented to the network. This hysteresis effect is a direct consequence of persistent attractor states and decreased the general classification performance of Scaled networks (see Supplementary Figure 8 for details). These results confirm the prediction that networks with discrete attractor states can efficiently classify inputs, but also reveal disadvantages arising from attractor dynamics. Moreover, the results indicate that the classification performance of Tuned networks is also high under the given task conditions, which simulate a biologically realistic scenario.

We would also like to emphasize that classification may not be the only task, and perhaps not even a main task, of Dp/piriform cortex or other memory networks with E/I assemblies. Conceivably, other computations could include metric assessments of inputs relative to learned inputs or additional learning-related computations. Please see our response to comment (3) of reviewer 1 for a further discussion of this issue. 

Networks featuring E/I assemblies could potentially represent multistable attractors by exploring the parameter space for their reciprocal connectivity and connectivity with the rest of the network. However, for co-tuned E-I networks, the scope for achieving multistability is relatively constrained compared to networks employing global or lateral inhibition between assemblies. It would be good if the authors mentioned this in the discussion. Also, the fact that reciprocal inhibition increases network stability has been shown before and should be cited in the statements addressing network stability (e.g., some of the citations in the manuscript, including Rost et al. 2018, Lagzi & Fairhall 2022, and Vogels et al. 2011 have shown this).  

We thank the reviewer for this comment. We now explicitly discuss multistability (see p. 12) and refer to additional references in the statements addressing network stability.

Providing raster plots of the pDp network for familiar and novel inputs would help with understanding the claims regarding continuous versus discrete representation of inputs, allowing readers to visualize the activity patterns of the four different networks. (similar to Figure 1B). 

We thank the reviewer for this suggestion. We have added raster plots of responses to both familiar and novel inputs in the revised manuscript (Figure 2D and Supplementary Figure 4A).

Reviewer #3 (Public Review): 

Summary: 

This work investigates the computational consequences of assemblies containing both excitatory and inhibitory neurons (E/I assembly) in a model with parameters constrained by experimental data from the telencephalic area Dp of zebrafish. The authors show how this precise E/I balance shapes the geometry of neuronal dynamics in comparison to unstructured networks and networks with more global inhibitory balance. Specifically, E/I assemblies lead to the activity being locally restricted onto manifolds - a dynamical structure in between high-dimensional representations in unstructured networks and discrete attractors in networks with global inhibitory balance. Furthermore, E/I assemblies lead to smoother representations of mixtures of stimuli while those stimuli can still be reliably classified, and allow for more robust learning of additional stimuli. 

Strengths: 

Since experimental studies do suggest that E/I balance is very precise and E/I assemblies exist, it is important to study the consequences of those connectivity structures on network dynamics. The authors convincingly show that E/I assemblies lead to different geometries of stimulus representation compared to unstructured networks and networks with global inhibition. This finding might open the door for future studies for exploring the functional advantage of these locally defined manifolds, and how other network properties allow to shape those manifolds. 

The authors also make sure that their spiking model is well-constrained by experimental data from the zebrafish pDp. Both spontaneous and odor stimulus triggered spiking activity is within the range of experimental measurements. But the model is also general enough to be potentially applied to findings in other animal models and brain regions. 

Weaknesses: 

I find the point about pattern completion a bit confusing. In Fig. 3 the authors argue that only the Scaled I network can lead to pattern completion for morphed inputs since the output correlations are higher than the input correlations. For me, this sounds less like the network can perform pattern completion but it can nonlinearly increase the output correlations. Furthermore, in Suppl. Fig. 3 the authors show that activating half the assembly does lead to pattern completion in the sense that also non-activated assembly cells become highly active and that this pattern completion can be seen for Scaled I, Tuned E+I, and Tuned I networks. These two results seem a bit contradictory to me and require further clarification, and the authors might want to clarify how exactly they define pattern completion. 

We believe that this comment concerns a semantic misunderstanding and apologize for any lack of clarity. We added a definition of pattern completion in the text: “…the retrieval of the whole memory from noisy or corrupted versions of the learned input.”. Pattern completion may be assessed using different procedures. In computational studies, it is often analyzed by delivering input to a subset of the assembly neurons which store a given memory (partial activation). Under these conditions, we find recruitment of the entire assembly in all structured networks, as demonstrated in Supplementary Figure 3. However, these conditions are unlikely to occur during odor presentation because the majority of neurons do not receive any input.

Another more biologically motivated approach to assess pattern completion is to gradually modify a realistic odor input into a learned input, thereby gradually increasing the overlap between the two inputs. This approach had been used previously in experimental studies (references added to the text p.6). In the presence of assemblies, recurrent connectivity is expected to recruit assembly neurons (and thus retrieve the stored pattern) more efficiently as the learned pattern is approached. This should result in a nonlinear increase in the similarity between the evoked and the learned activity pattern. This signature was prominent in Scaled networks but not in Tuned or rand networks. Obviously, the underlying procedure is different from the partial activation of the assembly described above because input patterns target many neurons (including neurons outside assemblies) and exhibit a biologically realistic distribution of activity. However, this approach has also been referred to as “pattern completion” in the neuroscience literature, which may be the source of semantic confusion here. To clarify the difference between these approaches we have now revised the text and explicitly described each procedure in more detail (see p.6). 

The authors argue that Tuned E+I networks have several advantages over Scaled I networks. While I agree with the authors that in some cases adding this localized E/I balance is beneficial, I believe that a more rigorous comparison between Tuned E+I networks and Scaled I networks is needed: quantification of variance (Fig. 4G) and angle distributions (Fig. 4H) should also be shown for the Scaled I network. Similarly in Fig. 5, what is the Mahalanobis distance for Scaled I networks and how well can the Scaled I network be classified compared to the Tuned E+I network? I suspect that the Scaled I network will actually be better at classifying odors compared to the E+I network. The authors might want to speculate about the benefit of having networks with both sources of inhibition (local and global) and hence being able to switch between locally defined manifolds and discrete attractor states. 

We agree that a more rigorous comparison of Tuned and Scaled networks would be of interest. We have added the variance analysis (Fig 4G) and angle distributions (Fig. 4H) for both Tuned I and Scaled networks. However, the Mahalanobis distances and Quadratic Discriminant Analysis cannot be applied to Scaled networks because their neuronal covariance matrix is low rank and not invertible_. To nevertheless compare these networks, we performed template matching by assigning test patterns to one of the four odor classes based on correlations to template patterns (Supplementary Figure 8; see also response to the first comment of reviewer 2). Interestingly, _Scaled networks performed well at classification but did not outperform Tuned networks, and exhibited disadvantages arising from attractor dynamics (Supplementary Figure 8; see also response to the first comment of reviewer 2). Furthermore, in further analyses we found that continuous representational manifolds support metric assessments of inputs relative to learned odors, which cannot be achieved by discrete representations. These results are now shown in Figure 5D-E and discussed explicitly in the text on p.11 (see also response to comment 3 of reviewer 1).

We preferred not to add a sentence in the Discussion about benefits of networks having both sources of inhibition_,_ as we find this a bit too speculative.

At a few points in the manuscript, the authors use statements without actually providing evidence in terms of a Figure. Often the authors themselves acknowledge this, by adding the term "not shown" to the end of the sentence. I believe it will be helpful to the reader to be provided with figures or panels in support of the statements.  

Thank you for this comment. We have provided additional data figures to support the following statements:

“d_M was again increased upon learning, particularly between learned odors and reference classes representing other odors (Supplementary Figure 9)”

“decreasing amplification in assemblies of Scaled networks changed transformations towards the intermediate behavior, albeit with broader firing rate distributions than in Tuned networks (Supplementary Figure 6 B)”  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing. 

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks. 

The paper is generally well-written, the figures are informative and of good quality, and multiple approaches and metrics have been used to test and support the main results of the paper. 

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models. 

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation. 

(2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.   (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model. 

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model. 

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper. 

Precise balancing of excitation and inhibition in subnetworks would lead to the cancellation of specific dynamical modes responsible for the amplification of responses (hence, deviating from the attractor dynamics with an unstable specific mode). What is the key difference in the specific E/I networks here (tuned I or/and tuned E+I) which make them stand between random and attractor networks? Excitatory and inhibitory neurons have different parameters in the model (Table 1). Time constants of inhibitory and excitatory synapses are also different (P. 13). Are these parameters causing networks to be effectively more excitation dominated (hence deviating from a random spectrum which would be expected from a precisely balanced E/I network, with exactly the same parameters of E and I neurons)? It is necessary to analyse the network models, describe the key mechanism for their amplification, and pinpoint the key differences between E and I neurons which are crucial for this. 

To address these comments we performed additional simulations and analyses at different levels. Please see our reply to comment (1) of the public review (reviewer 1) for a detailed description. We thank the reviewer for these constructive comments.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.  

We thank the reviewer for this comment. We have now carried out additional simulations with equal time constants for all neurons. Please see our reply to the public review for more details (comment 2 of reviewer 1).

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning. 

One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function.

Please see our reply to the public review (comment 3 of reviewer 1).

Specific comments: 

Abstract: "resulting in continuous representations that reflected both relatedness of inputs and *an individual's experience*" 

It didn't become apparent from the text or the model where the role of "individual's experience" component (or "internal representations" - in the next line) was introduced or shown (apart from a couple of lines in the Discussion) 

We consider the scenario that that assemblies are the outcome of an experience-dependent plasticity process. To clarify this, we have now made a small addition to the text: “Biological memory networks are thought to store information by experience-dependent changes in the synaptic connectivity between assemblies of neurons.”.

P. 2: "The resulting state of "precise" synaptic balance stabilizes firing rates because inhomogeneities or fluctuations in excitation are tracked by correlated inhibition" 

It is not clear what the "inhomogeneities" specifically refers to - they can be temporal, or they can refer to the quenched noise of connectivity, for instance. Please clarify what you mean. 

The statement has been modified to be more precise: “…“precise” synaptic balance stabilizes firing rates because inhomogeneities in excitation across the population or temporal variations in excitation are tracked by correlated inhibition…”.

P. 3 (and Methods): When odour stimulus is simulated in the OB, the activity of a fraction of mitral cells is increased (10% to 15 Hz) - but also a fraction of mitral cells is suppressed (5% to 2 Hz). What is the biological motivation or reference for this? It is not provided. Is it needed for the results? Also, it is not explained how the suppressed 5% are chosen (e.g. randomly, without any relation to the increased cells?). 

We thank the reviewer for this comment. These changes in activity directly reflect experimental observations. We apologize that we forgot to include the references reporting these observations (Friedrich and Laurent, 2001 and 2004); this is now fixed.

In our simulation, OB neurons do not interact with each other, and the suppressed 5% were indeed randomly selected. We changed the text in Methods accordingly to read: “An additional 75 randomly selected mitral cells were inhibited” 

P. 4, L. 1-2: "... sparsely connected integrate-and-fire neurons with conductance-based synapses (connection probability {less than or equal to}5%)." 

Specify the connection probability of specific subtypes (EE, EI, IE, II).  

We now refer to the Methods section, where this information can be found. 

“... conductance-based synapses (connection probability ≤5%, Methods)”  

P. 4, L. 6-7: "Population activity was odor-specific and activity patterns evoked by uncorrelated OB inputs remained uncorrelated in Dp (Figure 1H)" 

What would happen to correlated OB inputs (e.g. as a result of mixture of two overlapping odours) in this baseline state of the network (before memories being introduced to it)? It would be good to know this, as it sheds light on the initial operating regime of the network in terms of E/I balance and decorrelation of inputs.  

This information was present in the original manuscript at (Figure 3) but we improved the writing to further clarify this issue: “ (…) we morphed a novel odor into a learned odor (Figure 3A), or a learned odor into another learned odor (Supplementary Figure 3B), and quantified the similarity between morphed and learned odors by the Pearson correlation of the OB activity patterns (input correlation). We then compared input correlations to the corresponding pattern correlations among E neurons in Dp (output correlation). In rand networks, output correlations increased linearly with input correlations but did not exceed them (Figure 3B and Supplementary Figure 3B)”

P. 4, L. 12-13: "Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of ~80%, .."   Where is this shown? 

(There are other occasions too in the paper where references to the supporting figures are missing). 

We now provide the statistics: “Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20”

P. 4: "In each network, we created 15 assemblies representing uncorrelated odors. As a consequence, ~30% of E neurons were part of an assembly ..." 

15 x 100 / 4000 = 37.5% - so it's closer to 40% than 30%. Unless there is some overlap? 

Yes: despite odors being uncorrelated and connectivity being random, some neurons (6 % of E neurons) belong to more than one assembly.

P. 4: "When a reached a critical value of ~6, networks became unstable and generated runaway activity (Figure 2B)." 

Can this transition point be calculated or estimated from the network parameters, and linked to the underlying mechanisms causing it? 

We thank the reviewer for this interesting question. The unstability arises when inhibitions fails to counterbalance efficiently the increased recurrent excitation within Dp. The transition point is difficult to estimate, as it can depend on several parameters, including the probability of E to E connections, their strength, assembly size, and others. We have therefore not attempted to estimate it analytically.

P. 4: "Hence, non-specific scaling of inhibition resulted in a divergence of firing rates that exhausted the dynamic range of individual neurons in the population, implying that homeostatic   global inhibition is insufficient to maintain a stable firing rate distribution." 

I don't think this is justified based on the results and figures presented here (Fig. 2E) - the interpretation is a bit strong and biased towards the conclusions the authors want to draw. 

To more clearly illustrate the finding that in Scaled networks, assembly neurons are highly active (close to maximal realistic firing rates) whereas non-assembly neurons are nearly silent we have now added Supplementary Fig. 2B. Moreover, we have toned down the text: “Hence, non-specific scaling of inhibition resulted in a large and biologically unrealistic divergence of firing rates (Supplementary Figure 2B) that nearly exhausted the dynamic range of individual neurons in the population, indicating that homeostatic global inhibition is insufficient to maintain a stable firing rate distribution”

P. 5, third paragraph: Description of Figure 2I, inset is needed, either in the text or caption. 

The inset is now referred to in the text: ”we projected synaptic conductances of each neuron onto a line representing the E/I ratio expected in a balanced network (“balanced axis”) and onto an orthogonal line (“counter-balanced axis”; Figure 2I inset, Methods).”

P. 5, last paragraph: another example of writing about results without showing/referring to the corresponding figures: 

"In rand networks, firing rates increased after stimulus onset and rapidly returned to a low baseline after stimulus offset. Correlations between activity patterns evoked by the same odor at different time points and in different trials were positive but substantially lower than unity, indicating high variability ..." 

And the continuation with similar lack of references on P. 6: 

"Scaled networks responded to learned odors with persistent firing of assembly neurons and high pattern correlations across trials and time, implying attractor dynamics (Hopfield, 1982; Khona and Fiete, 2022), whereas Tuned networks exhibited transient responses and modest pattern correlations similar to rand networks." 

Please go through the Results and fix the references to the corresponding figures on all instances. 

We thank the reviewer for pointing out these overlooked figure references, which are now fixed.

P. 8: "These observations further support the conclusion that E/I assemblies locally constrain neuronal dynamics onto manifolds." 

As discussed in the general major points, mechanistic explanation in terms of how the interaction of E/I dynamics leads to this is missing. 

As discussed in the reply to the public review (comment 3 of reviewer 1), we have now provided more mechanistic analyses of our observations.

P. 9: "Hence, E/I assemblies enhanced the classification of inputs related to learned patterns."   The effect seems to be very small. Also, any explanation for why for low test-target correlation the effect is negative (random doing better than tuned E/I)? 

The size of the effect (plearned – pnovel = 0.074; difference of means; Figure 5C) may appear small in terms of absolute probability, but it is substantial relative to the maximum possible increase (1 – p_novel =  0.133; Figure 5C). The fact that for low test-target correlations the effect is negative is a direct consequence of the positive effect for high test-target correlations and the presence of 2 learned odors in the 4-way forced choice task. 

P. 9: "In Scaled I networks, creating two additional memories resulted in a substantial increase   in firing rates, particularly in response to the learned and related odors"   Where is this shown? Please refer to the figure. 

We thank the reviewer again for pointing this out. We forgot to include a reference to the relevant figure which has now been added in the revised manuscript (Figure 6C).

P. 10: "The resulting Tuned networks reproduced additional experimental observations that were not used as constraints including irregular firing patterns, lower output than input correlations, and the absence of persistent activity" 

It is difficult to present these as "additional experimental observations", as all of them are negative, and can exist in random networks too - hence cannot be used as biological evidence in favour of specific E/I networks when compared to random networks. 

We agree with the reviewer that these additional experimental observations cannot be used as biological evidence favouring Tuned E+I networks over random networks. We here just wanted to point out that additional observations which we did not take into account to fit the model are not invalidating the existence of E-I assemblies in biological networks. As assemblies tend to result in persistent activity in other types of networks, we feel that this observation is worth pointing out.

Methods: 

P. 13: Describe the parameters of Eq. 2 after the equation. 

Done.

P. 13: "The time constants of inhibitory and excitatory synapses were 10 ms and 30 ms, respectively." 

What is the (biological) justification for the choice of these parameters? 

How would varying them affect the main results (e.g. local manifolds)? 

We chose a relatively slow time constant for excitatory synapses because experimental data indicate that excitatory synaptic currents in Dp and piriform cortex contain a prominent NMDA component. We have now also simulated networks with equal time constants for excitatory and inhibitory synapses and equal biophysical parameters for excitatory and inhibitory neurons, which did not affect the main results (see also reply to the public review: comment 2 of reviewer 1).

P. 14: "Care was also taken to ensure that the variation in the number of output connections was low across neurons"   How exactly?

More detailed explanations have now been added in the Methods section: “connections of a presynaptic neuron y to postsynaptic neurons x were randomly deleted when their total number exceeded the average number of output connections by ≥5%, or added when they were lower by ≥5%.“

Reviewer #2 (Recommendations For The Authors): 

Congratulations on the great and interesting work! The results were nicely presented and the idea of continuous encoding on manifolds is very interesting. To improve the quality of the paper, in addition to the major points raised in the public review, here are some more detailed comments for the paper: 

(1) Generally, citations have to improve. Spiking networks with excitatory assemblies and different architectures of inhibitory populations have been studied before, and the claim about improved network stability in co-tuned E-I networks has been made in the following papers that need to be correctly cited: 

• Vogels TP, Sprekeler H, Zenke F, Clopath C, Gerstner W. 2011. Inhibitory Plasticity Balances Excitation and Inhibition in Sensory Pathways and Memory Networks. Science 334:1-7. doi:10.1126/science.1212991 (mentions that emerging precise balance on the synaptic weights can result in the overall network stability) 

• Lagzi F, Bustos MC, Oswald AM, Doiron B. 2021. Assembly formation is stabilized by Parvalbumin neurons and accelerated by Somatostatin neurons. bioRxiv doi: https://doi.org/10.1101/2021.09.06.459211 (among other things, contrasts stability and competition which arises from multistable networks with global inhibition and reciprocal inhibition)   • Rost T, Deger M, Nawrot MP. 2018. Winnerless competition in clustered balanced networks: inhibitory assemblies do the trick. Biol Cybern 112:81-98. doi:10.1007/s00422-017-0737-7 (compares different architectures of inhibition and their effects on network dynamics) 

• Lagzi F, Fairhall A. 2022. Tuned inhibitory firing rate and connection weights as emergent network properties. bioRxiv 2022.04.12.488114. doi:10.1101/2022.04.12.488114 (here, see the eigenvalue and UMAP analysis for a network with global inhibition and E/I assemblies) 

Additionally, there are lots of pioneering work about tracking of excitatory synaptic inputs by inhibitory populations, that are missing in references. Also, experimental work that show existence of cell assemblies in the brain are largely missing. On the other hand, some references that do not fit the focus of the statements have been incorrectly cited. 

The authors may consider referencing the following more pertinent studies on spiking networks to support the statement regarding attractor dynamics in the first paragraph in the Introduction (the current citations of Hopfield and Kohonen are for rate-based networks): 

• Wong, K.-F., & Wang, X.-J. (2006). A recurrent network mechanism of time integration in perceptual decisions. Journal of Neuroscience, 26(4), 1314-1328. https://doi.org/10.1523/JNEUROSCI.3733-05.2006 

• Wang, X.-J. (2008). Decision making in recurrent neuronal circuits. Neuron, 60(2), 215-234. https://doi.org/10.1016/j.neuron.2008.09.034  

• F. Lagzi, & S. Rotter. (2015). Dynamics of competition between subnetworks of spiking neuronal networks in the balanced state. PloS One. 

• Goldman-Rakic, P. S. (1995). Cellular basis of working memory. Neuron, 14(3), 477-485. 

• Rost T, Deger M, Nawrot MP. 2018. Winnerless competition in clustered balanced networks: inhibitory assemblies do the trick. Biol Cybern 112:81-98. doi:10.1007/s00422-017-0737-7. 

• Amit DJ, Tsodyks M (1991) Quantitative study of attractor neural network retrieving at low spike rates: I. substrate-spikes, rates and neuronal gain. Network 2:259-273. 

• Mazzucato, L., Fontanini, A., & La Camera, G. (2015). Dynamics of Multistable States during Ongoing and Evoked Cortical Activity. Journal of Neuroscience, 35(21), 8214-8231. 

We thank the reviewer for the references suggestions. We have carefully reviewed the reference list and made the following changes, which we hope address the reviewer’s concerns:

(1) We adjusted References about network stability in co-tuned E-I networks.

(2) We added the Lagzi & Rotter (2015), Amit et al. (1991), Mazzucato et al. (2015) and GoldmanRakic (1995) papers in the Introduction as studies on attractor dynamics in spiking neural networks. We preferred to omit the two X.J Wang papers, as they describe attractors in decision making rather than memory processes.

(3) We added the Ko et al. 2011 paper as experimental evidence for assemblies in the brain. In our view, there are few experimental studies showing the existence of cell assemblies in the brain, which we distinguish from cell ensembles, group of coactive neurons. 

(4) We also included Hennequin 2018, Brunel 2000, Lagzi et al. 2021 and Eckmann et al. 2024, which we had not cited in the initial manuscript.

(5) We removed the Wiechert et al. 2010 reference as it does not support the statement about geometry-preserving transformation by random networks.

(2) The gist of the paper is about how the architecture of inhibition (reciprocal vs. global in this case) can determine network stability and salient responses (related to multistable attractors and variations) for classification purposes. It would improve the narrative of the paper if this point is raised in the Introduction and Discussion section. Also see a relevant paper that addresses this point here: 

Lagzi F, Bustos MC, Oswald AM, Doiron B. 2021. Assembly formation is stabilized by Parvalbumin neurons and accelerated by Somatostatin neurons. bioRxiv doi: https://doi.org/10.1101/2021.09.06.459211 

Classification has long been proposed to be a function of piriform cortex and autoassociative memory networks in general, and we consider it important. However, the computational function of Dp or piriform cortex is still poorly understood, and we do not focus only on odor classification as a possibility. In fact, continuous representational manifolds also support other functions such as the quantification of distance relationships of an input to previously memorized stimuli, or multi-layer network computations (including classification). In the revised manuscript, we have performed additional analyses to explore these notions in more detail, as explained above (response to public reviews, comment 3 of reviewer 1). Furthermore, we have now expanded the discussion of potential computational functions of Tuned networks and explicitly discuss classification but also other potential functions. 

(3) A plot for the values of the inhibitory conductances in Figure 1 would complete the analysis for that section. 

In Figure 1, we decided to only show the conductances that we use to fit our model, namely the afferent and total synaptic conductances. As the values of the inhibitory conductances can be derived from panel E, we refrained from plotting them separately for the sake of simplicity. 

(4) How did the authors calculate correlations between activity patterns as a function of time in Figure 2E, bottom row? Does the color represent correlation coefficient (which should not be time dependent) or is it a correlation function? This should be explained in the Methods section. 

The color represents the Pearson correlation coefficient between activity patterns within a narrow time window (100 ms). We updated the Figure legend to clarify this: “Mean correlation between activity patterns evoked by a learned odor at different time points during odor presentation. Correlation coefficients were calculated between pairs of activity vectors composed of the mean firing rates of E neurons in 100 ms time bins. Activity vectors were taken from the same or different trials, except for the diagonal, where only patterns from different trials were considered.”

(5) Figure 3 needs more clarification (both in the main text and the figure caption). It is not clear what the axes are exactly, and why the network responses for familiar and novel inputs are different. The gray shaded area in panel B needs more explanation as well.  

We thank the reviewer for the comment. We have improved Figure 3A, the figure caption, as well as the text (see p.6). We hope that the figure is now clearer.

(6) The "scaled I" network, known for representing input patterns in discrete attractors, should exhibit clear separation between network responses in the 2D PC space in the PCA plots. However, Figure 4D and Figure 6D do not reflect this, as all network responses are overlapped. Can the authors explain the overlap in Figure 4D? 

In Figure 4D, activity of Scaled networks is distributed between three subregions in state space that are separated by the first 2 PCs. Two of them indeed correspond to attractor states representing the two learned odors while the third represents inputs that are not associated with these attractor states. To clarify this, please see also the density plot in Figure 4E. The few datapoints between these three subregions are likely outliers generated by the sequential change in inputs, as described in Supplementary Figure 8C.

(7) The reason for writing about the ISN networks is not clear. Co-tuned E-I assemblies do not necessarily have to operate in this regime. Also, the results of the paper do not rely on any of the properties of ISNs, but they are more general. Authors should either show the paradoxical effect associated with ISN (i.e., if increasing input to I neurons decreases their responses) or show ISN properties using stability analysis (See computational research conducted at the Allen Institute, namely Millman et al. 2020, eLife ). Currently, the paper reads as if being in the ISN regime is a necessary requirement, which is not true. Also, the arguments do not connect with the rest of the paper and never show up again. Since we know it is not a requirement, there is no need to have those few sentences in the Results section. Also, the choice of alpha=5.0 is extreme, and therefore, it would help to judge the biological realism if the raster plots for Figs 2-6 are shown.

We have toned down the part on ISN and reduced it to one sentence for readers who might be interested in knowing whether activity is inhibition-stabilized or not. We have also added the reference to the Tsodyks et al. 1997 paper from which we derive our stability analysis. The text now reads “Hence, pDp_sim entered a balanced state during odor stimulation (Figure 1D, E) with recurrent input dominating over afferent input, as observed in pDp (Rupprecht and Friedrich, 2018). Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20, demonstrating that activity was inhibition-stabilized (Sadeh and Clopath, 2020b, Tsodyks et al., 1997).”  

We have now also added the raster plots as suggested by the reviewer (see Figure 2D, Supplementary Figure 1 G, Supplementary Figure 4). We thank the reviewer for this comment.

(8) In the abstract, authors mention "fast pattern classification" and "continual learning," but in the paper, those issues have not been addressed. The study does not include any synaptic plasticity. 

Concerning “continual learning” we agree that we do not simulate the learning process itself. However, Figure 6 show results of a simulation where two additional patterns were stored in a network that already contained assemblies representing other odors. We consider this a crude way of exploring the end result of a “continual learning” process. “Fast pattern classification” is mentioned because activity in balanced networks can follow fluctuating inputs with high temporal resolution, while networks with stable attractor states tend to be slow. This is likely to account for the occurrence of hysteresis effects in Scaled but not Tuned networks as shown in Supplementary

Fig. 8.

(9) In the Introduction, the first sentence in the second paragraph reads: "... when neurons receive strong excitatory and inhibitory synaptic input ...". The word strong should be changed to "weak".

Also, see the pioneering work of Brunel 2000. 

In classical balanced networks, strong excitatory inputs are counterbalanced by strong inhibitory inputs, leading to a fluctuation-driven regime. We have added Brunel 2000.

(10) In the second paragraph of the introduction, the authors refer to studies about structural co-tuning (e.g., where "precise" synaptic balance is mentioned, and Vogels et al. 2011 should be cited there) and functional co-tuning (which is, in fact, different than tracking of excitation by inhibition, but the authors refer to that as co-tuning). It makes it easier to understand which studies talk about structural co-tuning and which ones are about functional co-tuning. The paper by Znamenski 2018, which showed both structural and functional tuning in experiments, is missing here. 

We added the citation to the now published paper by Znamenskyi et al. (2024).  

(11) The third paragraph in the Introduction misses some references that address network dynamics that are shaped by the inhibitory architecture in E/I assemblies in spiking networks, like Rost et al 2018 and Lagzi et al 2021. 

These references have been added.

(12) The last sentence of the fourth paragraph in the Introduction implies that functional co-tuning is due to structural co-tuning, which is not necessarily true. While structural co-tuning results in functional co-tuning, functional co-tuning does not require structural co-tuning because it could arise from shared correlated input or heterogeneity in synaptic connections from E to I cells.  

We generally agree with the reviewer, but we are uncertain which sentence the reviewer refers to.

We assume the reviewer refers to the last sentence of the second (rather than the fourth paragraph), which explicitly mentions the “…structural basis of E/I co-tuning…”. If so, we consider this sentence still correct because the “structural basis” refers not specifically to E/I assemblies, but also includes any other connectivity that may produce co-tuning, including the connectivity underlying the alternative possibilities mentioned by the reviewer (shared correlated input or heterogeneity of synaptic connections).

(13) In order to ensure that the comparison between network dynamics is legit, authors should mention up front that for all networks, the average firing rates for the excitatory cells were kept at 1 Hz, and the background input was identical for all E and I cells across different networks.

We slightly revised the text to make this more clear “We (…) uniformly scaled I-to-E connection weights by a factor of χ until E population firing rates in response to learned odors matched the corresponding firing rates in rand networks, i.e., 1 Hz”

(14) In the last paragraph on page 5, my understanding was that an individual odor could target different cells within an assembly in different trials to generate trial to trail variability. If this is correct, this needs to be mentioned clearly. 

This is not correct, an odor consists of 150 activated mitral cells with defined firing rates. As now mentioned in the Methods, “Spikes were then generated from a Poisson distribution, and this process was repeated to create trial-to-trial variability.”

(15) The last paragraph on page 6 mentions that the four OB activity patterns were uncorrelated but if they were designed as in Figure 4A, dues to the existing overlap between the patterns, they cannot be uncorrelated. 

This appears to be a misunderstanding. We mention in the text (and show in Figure 4B) that the four odors which “… were assigned to the corners of a square…” are uncorrelated.  The intermediate odors are of course not uncorrelated. We slightly modified the corresponding paragraph (now on page 7) to clarify this: “The subspace consisted of a set of OB activity patterns representing four uncorrelated pure odors and mixtures of these pure odors. Pure odors were assigned to the corners of a square and mixtures were generated by selecting active mitral cells from each of the pure odors with probabilities depending on the relative distances from the corners (Figure 4A, Methods).”

(16) The notion of "learned" and "novel" odors may be misleading as there was no plasticity in the network to acquire an input representation. It would be beneficial for the authors to clarify that by "learned," they imply the presence of the corresponding E assembly for the odor in the network, with the input solely impacting that assembly. Conversely, for "novel" inputs, the input does not target a predefined assembly. In Figure 2 and Figure 4, it would be especially helpful to have the spiking raster plots of some sample E and I cells.  

As suggested by the reviewer, we have modified the existing spiking raster plots in Figure 2, such that they include examples of responses to both learned and novel odors. We added spiking raster plots showing responses of I neurons to the same odors in Supplementary Figure 1F, as well as spiking raster plots of E neurons in Supplementary Figure 4A. To clarify the usage of “learned” and “novel”, we have added a sentence in the Results section: “We thus refer to an odor as “learned” when a network contains a corresponding assembly, and as “novel” when no such assembly is present.”.

(17) In the last paragraph of page 8, can the authors explain where the asymmetry comes from? 

As mentioned in the text, the asymmetry comes from the difference in the covariance structure of different classes. To clarify, we have rephrased the sentence defining the Mahalanobis distance: 

“This measure quantifies the distance between the pattern and the class center, taking into account covariation of neuronal activity within the class. In bidirectional comparisons between patterns from different classes, the mean dM may be asymmetric if neural covariance differs between classes.”

(18) The first paragraph of page 9: random networks are not expected to perform pattern classification, but just pattern representation. It would have been better if the authors compared Scaled I network with E/I co-tuned network. Regardless of the expected poorer performance of the E/I co-tuned networks, the result would have been interesting. 

Please see our reply to the public review (reviewer 2).

(19) Second paragraph on page 9, the authors should provide statistical significance test analysis for the statement "... was significantly higher ...". 

We have performed a Wilcoxon signed-rank test, and reported the p-value in the revised manuscript (p < 0.01). 

(20) The last sentence in the first paragraph on page 11 is not clear. What do the authors mean by "linearize input-output functions", and how does it support their claim? 

We have now amended this sentence to clarify what we mean: “…linearize the relationship between the mean input and output firing rates of neuronal populations…”.

(21) In the first sentence of the last paragraph on page 11, the authors mentioned “high variability”, but it is not clear compared with which of the other 3 networks they observed high variability.

Structurally co-tuned E/I networks are expected to diminish network-level variability. 

“High variability” refers to the variability of spike trains, which is now mentioned explicity in the text. We hope this more precise statement clarifies this point.

(22) Methods section, page 14: "firing rates decreased with a time constant of 1, 2 or 4 s". How did they decrease? Was it an implementation algorithm? The time scale of input presentation is 2 s and it overlaps with the decay time constant (particularly with the one with 4 s decrease).  

Firing rates decreased exponentially. We have added this information in the Methods section.

Reviewer #3 (Recommendations For The Authors): 

In the following, I suggest minor corrections to each section which I believe can improve the manuscript. 

- There was no github link to the code in the manuscript. The code should be made available with a link to github in the final manuscript. 

The code can be found here: https://github.com/clairemb90/pDp-model. The link has been added in the Methods section.

Figure 1: 

- Fig. 1A: call it pDp not Dp. Please check if this name is consistent in every figure and the text. 

Thank you for catching this. Now corrected in Figure 1, Figure 2 and in the text.

- The authors write: "Hence, pDpsim entered an inhibition-stabilized balanced state (Sadeh and Clopath, 2020b) during odor stimulation (Figure 1D, E)." and then later "Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of ~80%, demonstrating that activity was indeed inhibition-stabilized. These results were robust against parameter variations (Methods)." I would suggest moving the second sentence before the first sentence, because the fact that the network is in the ISN regime follows from the shuffled spike timing result. 

Also, I'd suggest showing this as a supplementary figure. 

We thank the reviewer for this comment. We have removed “inhibition-stabilized” in the first sentence as there is no strong evidence of this in Rupprecht and Friedrich, 2018. And removed “indeed” in the second sentence. We also provided more detailed statistics. The text now reads “Hence, pDpsim entered a balanced state during odor stimulation (Figure 1D, E) with recurrent input dominating over afferent input, as observed in pDp (Rupprecht and Friedrich, 2018). Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20, demonstrating that activity was inhibition-stabilized (Sadeh and Clopath, 2020b).”

Figure 2: 

- "... Scaled I networks (Figure 2H." Missing ) 

Corrected.

- The authors write "Unlike in Scaled I networks, mean firing rates evoked by novel odors were indistinguishable from those evoked by learned odors and from mean firing rates in rand networks (Figure 2F)." 

Why is this something you want to see? Isn't it that novel stimuli usually lead to high responses? Eg in the paper Schulz et al., 2021 (eLife) which is also cited by the authors it is shown that novel responses have high onset firing rates. I suggest clarifying this (same in the context of Fig. 3C). 

In Dp and piriform cortex, firing rates evoked by learned odors are not substantially different from firing rates evoked by novel odors. While small differences between responses to learned versus novel odors cannot be excluded, substantial learning-related differences in firing rates, as observed in other brain areas, have not been described in Dp or piriform cortex. We added references in the last paragraph of p.5. Note that the paper by Schulz et al. (2021) models a different type of circuit.  

- Fig. 2B: Indicate in figure caption that this is the case "Scaled I" 

This is not exactly the case “Scaled I”, as the parameter 𝝌𝝌 (increased I to E strength) is set to 1.

- Suppl Fig. 2I: Is E&F ever used in the manuscript? I couldn't find a reference. I suggest removing it if not needed. 

Suppl. Fig 2I E&F is now Suppl Fig.1G&H. We now refer to it in the text: “Activity of networks with E assemblies could not be stabilized around 1 Hz by increasing connectivity from subsets of I neurons receiving dense feed-forward input from activated mitral cells (Supplementary Figure 1GH; Sadeh and Clopath, 2020).”

Figure 3: 

- As mentioned in my comment in the public review section, I find the arguments about pattern completion a little bit confusing. For me it's not clear why an increase of output correlations over input correlations is considered "pattern completion" (this is not to say that I don't find the nonlinear increase of output correlations interesting). For me, to test pattern completion with second-order statistics one would need to do a similar separation as in Suppl Fig. 3, ie measuring the pairwise correlation at cells in the assembly L that get direct input from L OB with cells in the assembly L that do not get direct input from OB. If the pairwise correlations of assembly cells which do not get direct input from OB increase in correlations, I would consider this as pattern completion (similar to the argument that increase in firing rate in cells which are not directly driven by OB are considered a sign of pattern completion). 

Also, for me it now seems like that there are contradictory results, in Fig. 3 only Scaled I can lead to pattern completion while in the context of Suppl. Fig. 3 the authors write "We found that assemblies were recruited by partial inputs in all structured pDpsim networks (Scaled and Tuned) without a significant increase in the overall population activity (Supplementary Figure 3A)."   I suggest clarifying what the authors exactly mean by pattern completion, why the increase of output correlations above input correlations can be considered as pattern completion, and why the results differs when looking at firing rates versus correlations. 

Please see our reply to the public review (reviewer 3).

- I actually would suggest adding Suppl. Fig. 3 to the main figure. It shows a more intuitive form of pattern completion and in the text there is a lot of back and forth between Fig. 3 and Suppl. Fig. 3 

We feel that the additional explanations and panels in Fig.3 should clarify this issue and therefore prefer to keep Supplementary Figure 3 as part of the Supplementary Figures for simplicity.  

- In the whole section "We next explored effects of assemblies ... prevented strong recurrent amplification within E/I assemblies." the authors could provide a link to the respective panel in Fig. 2 after each statement. This would help the reader follow your arguments. 

We thank the reviewer for pointing this out. The references to the appropriate panels have been added. 

- Fig. 3A: I guess the x-axis has been shifted upwards? Should be at zero. 

We have modified the x-axis to make it consistent with panels B and C.  

- Fig. 3B: In the figure caption, the dotted line is described as the novel odor but it is actually the unit line. The dashed lines represent the reference to the novel odor. 

Fixed.

- Fig. 3C: The " is missing for Pseudo-Assembly N

Fixed.

- "...or a learned odor into another learned odor." Have here a ref to the Supplementary Figure 3B.

Added.

Figure 4:   

- "This geometry was largely maintained in the output of rand networks, consistent with the notion that random networks tend to preserve similarity relationships between input patterns (Babadi and Sompolinsky, 2014; Marr, 1969; Schaffer et al., 2018; Wiechert et al., 2010)." I suggest adding here reference to Fig. 4D (left). 

Added.

- Please add a definition of E/I assemblies. How do the authors define E/I assemblies? I think they consider both, Tuned I and Tuned E+I as E/I assemblies? In Suppl. Fig. 2I E it looks like tuned feedforward input is defined as E/I assemblies. 

We thank the reviewer for pointing this out. E/I assemblies are groups of E and I neurons with enhanced connectivity. In other words, in E/I assemblies, connectivity is enhanced not only between subsets of E neurons, but also between these E neurons and a subset of I neurons. This is now clarified in the text: “We first selected the 25 I neurons that received the largest number of connections from the 100 E neurons of an assembly. To generate E/I assemblies, the connectivity between these two sets of neurons was then enhanced by two procedures.”. We removed “E/I assemblies” in Suppl. Fig.2, where the term was not used correctly, and apologize for the confusion.

- Suppl. Fig. 4: Could the authors please define what they mean by "Loadings" 

The loadings indicate the contribution of each neuron to each principal component, see adjusted legend of Suppl. Fig. 4: “G. Loading plot: contribution of neurons to the first two PCs of a rand and a Tuned E+I network (Figure 4D).”

- Fig. 4F: The authors might want to normalize the participation ratio by the number of neurons (see e.g. Dahmen et al., 2023 bioRxiv, "relative PR"), so the PR is bound between 0 and 1 and the dependence on N is removed. 

We thank the reviewer for the suggestion, but we prefer to use the non-normalized PR as we find it more easily interpretable (e.g. number of attractor states in Scaled networks).

- Fig. 4G&H: as mentioned in the public review, I'd add the case of Scaled I to be able to compare it to the Tuned E+I case. 

As already mentioned in the public review, we thank the reviewer for this suggestion, which we have implemented.

- Figure caption Fig. 4H "Similar results were obtained in the full-dimensional space." I suggest showing this as a supplemental panel. 

Since this only adds little information, we have chosen not to include it as a supplemental panel to avoid overloading the paper with figures.

Figure 5: 

- As mentioned in the public review, I suggest that the authors add the Scaled I case to Fig. 5 (it's shown in all figures and also in Fig. 6 again). I guess for Scaled I the separation between L and M will be very good? 

Please see our reply to the public review (reviewer 3).

- Fig. 5A&B: I am a bit confused about which neurons are drawn to calculate the Mahalanobis distance. In Fig. 5A, the schematic indicates that the vector B from which the neurons are drawn is distinct from the distribution Q. For the example of odor L, the distribution Q consists of pure odor L with odors that have little mixtures with the other odors. But the vector v for odor L seems to be drawn only from odors that have slightly higher mixtures (as shown in the schematic in Fig. 5A). Is there a reason to choose the vector v from different odors than the distribution Q? 

The distribution Q and the vector v consist of activity patterns across the same neurons in response to different odors. The reason to choose a different odor for v was to avoid having this test datapoint being included in the distribution Q. We also wanted Q to be the same for all test datapoints. 

What does "drawn from whole population" mean? Does this mean that the vectors are drawn from any neuron in pDp? If yes, then I don't understand how the authors can distinguish between different odors (L,M,O,N) on the y-axis. Or does "whole population" mean that the vector is drawn across all assemblies as shown in the schematic in Fig. 5A and the case "neurons drawn from (pseudo-) assembly" means that the authors choose only one specific assembly? In any case, the description here is a bit confusing, I think it would help the reader to clarify those terms better.  

Yes, “drawn from whole population” means that we randomly draw 80 neurons from the 4000 E neurons in pDp. The y-axis means that we use the activity patterns of these neurons evoked by one of the 4 odors (L, M, N, O) as reference. We have modified the Figure legend to clarify this: “d_M was computed based on the activity patterns of 80 E neurons drawn from the four (pseudo-) assemblies (top) or from the whole population of 4000 E neurons (bottom). Average of 50 draws.”

- Suppl Fig. 5A: In the schematic the distance is called d_E(\bar{Q},\bar{V}) while the colorbar has d_E(\bar{Q},\bar{Q}) with the Qs in different color. The green Q should be a V. 

We thank the reviewer for spotting this mistake, it is now fixed.

- Fig. 5: Could the authors comment on the fact that a random network seems to be very good in classifying patterns on it's own. Maybe in the Discussion? 

The task shown in Figure 5 is a relatively easy one, a forced-choice between four classes which are uncorrelated. In Supplementary Figure 9, we now show classification for correlated classes, which is already much harder.

Figure 6: 

- Is the correlation induced by creating mixtures like in the other Figures? Please clarify how the correlations were induced. 

We clarified this point in the Methods section: “The pixel at each vertex corresponded to one pure odor with 150 activated and 75 inhibited mitral cells (…) and the remaining pixels corresponded to mixtures. In the case of correlated pure odors (Figure 6), adjacent pure odors shared half of their activated and half of their inhibited cells.”. An explicit reference to the Methods section has also been added to the figure legend.

- Fig. 6C (right): why don't we see the clear separation in PC space as shown in Fig. 4? Is this related to the existence of correlations? Please clarify. 

Yes. The assemblies corresponding to the correlated odors X and Y overlap significantly, and therefore responses to these odors cannot be well separated, especially for Scaled networks. We added the overlap quantification in the Results section to make this clear. “These two additional assemblies had on average 16% of neurons in common due to the similarity of the odors.”

- "Furthermore, in this regime of higher pattern similarity, dM was again increased upon learning, particularly between learned odors and reference classes representing other odors (not shown)." Please show this (maybe as a supplemental figure). 

We now show the data in Supplementary Figure 9.

Discussion: 

- The authors write: "We found that transformations became more discrete map-like when amplification within assemblies was increased and precision of synaptic balance was reduced. Likewise, decreasing amplification in assemblies of Scaled networks changed transformations towards the intermediate behavior, albeit with broader firing rate distributions than in Tuned networks (not shown)." 

Where do I see the first point? I guess when I compare in Fig. 4D the case of Scaled I vs Tuned E+I, but the sentence above sounds like the authors showed this in a more step-wise way eg by changing the strength of \alpha or \beta (as defined in Fig. 1). 

Also I think if the authors want to make the point that decreasing amplification in assemblies changes transformation with a different rate distribution in scaled vs tuned networks, the authors should show it (eg adding a supplemental figure). 

The first point is indeed supported by data from different figures. Please note that the revised manuscript now contains further simulations that reinforce this statement, particularly those shown in Supplementary Figure 6, and that this point is now discussed more extensively in the Discussion. We hope that these revisions clarify this general point.

The data showing effects of decreasing amplification in assemblies is now shown in Supplementary Figure 6 (Scaled[adjust])

- I suggest adding the citation Znamenskiy et al., 2024 (Neuron; https://doi.org/10.1016/j.neuron.2023.12.013), which shows that excitatory and inhibitory (PV) neurons with functional similarities are indeed strongly connected in mouse V1, suggesting the existence of E/I assembly structure also in mammals.

Done.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

It is evident that studying leukocyte extravasation in vitro is a challenge. One needs to include physiological flow, culture cells and isolate primary immune cells. Timing is of utmost importance and a reproducible setup essential. Extra challenges are met when extravasation kinetics in different vascular beds is required, e.g., across the blood-brain barrier. In this study, the authors describe a reliable and reproducible method to analyze leukocyte TEM under physiological flow conditions, including this analysis. That the software can also detect reverse TEM is a plus.

Strengths:

It is quite a challenge to get this assay reproducible and stable, in particular as there is flow included. Also for the analysis, there is currently no clear software analysis program, and many labs have their own methods. This paper gives the opportunity to unify the data and results obtained with this assay under label-free conditions. This should eventually lead to more solid and reproducible results.

Also, the comparison between manual and software analysis is appreciated.

Weaknesses:

The authors stress that it can be done in BBB models, but I would argue that it is much more broadly applicable. This is not necessarily a weakness of the study but more an opportunity to strengthen the method. So I would encourage the authors to rewrite some parts and make it more broadly applicable.

We thank the Reviewer for this suggestion. The barrier properties of the BBB influence the dynamic behavior of T cells during their multi-step extravasation cascade. The crawling of CD4 T cells against the direction of blood-flow is e.g. a unique behavior of T cells on the BBB  that is also observed in vivo(1-3). Nevertheless we fully agree that in principle UFMTrack is usable for studying in general immune cell interactions with endothelial monolayers under physiological flow. We have thus added a statement in the abstract and expanded the discussion to highlight availability of the framework and the potential necessary adaptations required when using UFMTrack for analyzing different experimental setups. Please also note, UFMTrack has been established as basic framework using the example of brain endothelial monolayers and one flow chamber devices while studying different immune cell subsets. The purpose of the publication is to make UFMTrack available to the community to address their specific questions.

(1) Kawakami, N., Bartholomäus, I., Pesic, M. & Kyratsous, N. I. Intravital Imaging of Autoreactive T Cells in Living Animals. Methods Cell Biol. 113, 149–168 (2013).

(2) Schläger, C., Litke, T., Flügel, A. & Odoardi, F. In Vivo Visualization of (Auto)Immune Processes in the Central Nervous System of Rodents. in 117–129 (Humana Press, New York, NY, 2014). doi:10.1007/7651_2014_150

(3) Haghayegh Jahromi, N. et al. Intercellular Adhesion Molecule-1 (ICAM-1) and ICAM-2 Differentially Contribute to Peripheral Activation and CNS Entry of Autoaggressive Th1 and Th17 Cells in Experimental Autoimmune Encephalomyelitis. Front. Immunol. 10, 3056 (2020).

Author response:

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

eLife assessment:

Developing a reliable method to record ancestry and distinguish between human somatic cells presents significant challenges. I fully acknowledge that my current evidence supporting the claim of lineage tracing with fCpG barcodes is inadequate. I agree with Reviewer 1 that fCpG barcodes are essentially a cellular division clock that diverges over time. A division clock could potentially document when cells cease to divide during development, with immediate daughter cells likely exhibiting more similar barcodes than those that are less related. Although it remains uncertain whether the current fCpG barcodes capture useful biological information, refinement of this type of tool could complement other approaches that reconstruct human brain function, development, and aging.

Due to my lack of clarity, the fCpG barcode was perceived to be a new type of cell classifier. However, it is fundamentally different. fCpG sites are selected based on their differences between cells of the same type, while traditional cell classifiers focus on sites with consistent methylation patterns in cells of the same type. Despite these opposing criteria, fCpG barcodes and traditional cell classifiers may align because neuron subtypes often share common progenitors. As a result, cells of the same phenotype are also closely related by ancestry, and ex post facto, have similar fCpG barcodes. fCpG barcodes are complementary to cell type classifiers, and potentially provide insights into aspects such as mitotic ages, diversity within a clade, and migration of immediate daughters---information which is otherwise difficult to obtain. The title has been modified to “Human Brain Ancestral Barcodes” to better reflect the function of the fCpG barcodes. The manuscript is edited to correct errors, and a new Supplement is added to further explain fCpG barcode mechanics and present new supporting data.

Reviewer #1 (Public review):

I thank Reviewer 1 for his constructive comments. Major noted weaknesses were 1) insufficient clarity and brevity of the methodology, 2) inconsistent or erroneous use of neurodevelopmental concepts, and 3) lack of consideration for alternative explanations.

(1) The methodology is now outlined in detailed in a new Supplement, including simulations that indicate that the error rate consistent with the experimental data is about 0.01 changes in methylation per fCpG site per division.

(2) Conceptual and terminology errors noted by the Reviewers are corrected in the manuscript.

(3) I agree completely with the alternative explanation of Reviewer 1 that fCpGs are “a cellular division clock that diverges over 'time'”. Differences between more traditional cell type classifiers and fCpG barcodes are more fully outlined in the new Supplement.  Ancestry recorded by fCpGs and cell type classifiers are confounded because cells of the same phenotype typically have common progenitors---cells within a clade have similar fCpG barcodes because they are closely related. fCpG barcodes can compliment cell type classifiers with additional information such as mitotic ages, ancestry within a clade, and daughter cell migration.

Reviewer #1 (Recommendations for the authors):

(1) A lot of the interpretations suffer from an extremely loose/erroneous use of developmental concepts and a lack of transparency. For instance:

a) The thalamus is not part of the brain stem

Corrected.

b) The pons contains cells other than inhibitory neurons in the data; the same is true for the hippocampus which contains multiple cell types

Corrected to refer to the specific cell types in these regions.

c) The author talks about the rostral-caudal timing a lot which is not really discussed to this degree in the cited references. Thus, it is also unclear how interneurons fit in this model as they are distinguished by a ventral-dorsal difference from excitatory neurons. Also, it is unclear whether the timing is really as distinct as claimed. For instance, inhibitory neurons and excitatory neurons significantly overlap in their birth timing. Finally, conceptually, it does not make sense to go by developmental timing as the author proposes that it is the number of divisions that is relevant. While they are somewhat correlated there are potentially stark differences.

The manuscript attempts to describe what might be broadly expected when barcodes are sampled from different cell types and locations. As a proposed mitotic clock, the fCpG barcode methylation level could time when each neuron ceased division and differentiated. The wide ranges of fCpG barcode methylation of each cell type (Fig 2A) would be consistent with significant overlap between cell types. The manuscript is edited to emphasize overlapping rather than distinct sequential differentiation of the cell types.

d) Neocortical astrocytes and some oligodendrocytes share a lineage, whereas a subset of oligodendrocytes in the cortex shares an origin with interneurons. This could confound results but is never discussed.

The manuscript does not assess glial lineages in detail because neurons were preferentially included in the sampling whereas glial cells were non-systematically excluded. This sampling information is now included in the section “fCpG barcode identification”.

e) Neocortical interneurons should be more closely related in terms of lineage-to-excitatory neurons than other inhibitory neurons of, for instance, the pons. This is not clearly discussed and delineated.

This is not discussed. It may not be possible analyze these details with the current data. The ancestral tree reconstructions indicate that excitatory neurons that appear earlier in development (and are more methylated) are more often more closely related to inhibitory neurons.

f) While there is some spread of excitatory neurons tangentially, there is no tangential migration at the scale of interneurons as (somewhat) suggested/implied here.

The abstract and results have been modified to indicate greater inhibitory than excitatory neuron tangential migration, but that the extent of excitatory neuron tangential migration cannot be determined because of the sparse sampling and that barcodes may be similar by chance.

g) The nature of the NN cells is quite important as cells not derived from the neocortical anlage are unlikely to share a developmental origin (e.g., microglia, endothelial cells). This should be clarified and clearly stated.

The manuscript is modified to indicate that NN cells are microglial and endothelial cells. These cells have different developmental origins, and their data are present in Fig 2A, but are not further used for ancestral analysis.  

(2) The presentation is often somewhat confusing to me and lacks detail. For instance:

a) The methods are extremely short and I was unable to find a reference for a full pipeline, so other researchers can replicate the work and learn how to use the pipeline.

The pipeline including python code is outlined in the new Supplement

b) Often numbers are given as ~XX when the actual number with some indication of confidence or spread would be more appropriate.

Data ranges are often indicated with the violin plots.

c) Many figure legends are exceedingly short and do not provide an appropriate level of detail.

Figure legends have been modified to include more detail

d) Not defining groups in the figure legends or a table is quite unacceptable to me. I do not think that referring to a prior publication (that does not consistently use these groups anyway) is sufficient.

The cell groups are based on the annotations provided with each single cell in the public databases.

e) The used data should be better defined and introduced (number of cells, different subtypes across areas, which cells were excluded; I assume the latter as pons and hippocampus are only mentioned for one type of neuronal cells, see also above).

The data used are present in Supplemental File 2 under the tab “cell summary H01, H02, H04”.

f) Why were different upper bounds used for filtering for H01 and H02, and H04 is not mentioned? Why are inhibitory and excitatory neurons specifically mentioned (Lines 61-66)?

The filtering is used to eliminate, as much as possible, cell type specific methylation, or CpG sites with skewed neuron methylation. The filtering eliminates CpG sites with high or low methylation within each of the three brains, and within the two major neuron subtypes. The goal is to enrich for CpG sites with polymorphic but not cell type specific methylation. This process is ad hoc as success criteria are currently uncertain. The extent of filtering is balanced by the need to retain sufficient numbers of fCpGs to allow comparisons between the neurons.

g) What 'progenitor' does the author refer to? The Zygote? If yes, can the methylation status be tested directly from a zygote? There is no single progenitor for these cells other than the zygote. Does the assumption hold true when taking this into account? See, for instance, PMID 33737485 for some estimation of lineage bottlenecks.

A brain progenitor cell can be defined as the common ancestor of all adult neurons, and is the first cell where each of its immediate daughter cell lineages yield adult neurons. The zygote is a progenitor cell to all adult cells, and barcode methylation at the start of conception, from the oocyte to the ICM, was analyzed in the new Supplement. The proposed brain progenitor cell with a fully methylated barcode was not yet evident even in the ICM.

(3) I am generally not convinced that the fCpGs represent anything but a molecular clock of cell divisions and that many of the similarities are a function of lower division numbers where the state might be more homogenous. This mainly derives from the issues cited above, the lack of convincing evidence to the contrary, and the sparsity of the assessed data.

Agree that the fCpG barcode is a mitotic clock that becomes polymorphic with divisions. As outlined in the new Supplement, ancestry and cell type are confounded because cells of the same type typically have a common progenitor.

a) There appears little consideration or modeling of what the ability to switch back does to the lineage reconstruction.

fCpG methylation flipping is further analyzed and discussed in the new Supplement.

b) None of the data convinced me that the observations cannot be explained by the aforementioned molecular clock and systematic methylation similarities of cell types due to their cell state.

See above

(4) Uncategorized minor issues:

a) The author should explain concepts like 'molecular clock hypothesis' (line 27) or 'radial unit hypothesis' (line 154), as they are somewhat complex and might not be intuitive to readers.

The molecular clock hypothesis is deleted and the radial unit hypothesis is explained in more detail in the manuscript.

b) Line 32: '[...] replication errors are much higher compared to base replication [...]'. I think this is central to the method and should be better explained and referenced. Maybe even through a schematic, as this is a central concept for the entire manuscript.

The fCpG barcode mechanics are better explained in the new Supplement. With simulations, the fCpG flip rate is about 0.01 per division per fCpG.

c) Line 41: 'neonatal'. Does the author mean to say prenatal? Most of the cells discussed are postmitotic before birth.

Corrected to prenatal.

d) Line 96: what does 'flip' mean in this context? Please also see the comment on Figure 2C.

Edited to “chage”

e) Lines 134-135: I am not sure whether the author claims to provide evidence for this question, and I would be careful with claims that this work does resolve the question here.

Have toned down claims as evidence for my analysis is currently inadequate.

f) Lines 192-193: I disagree as the fCpGs can switch back and the current data does not convince me that this is an improvement upon mosaic mutation analysis. In my mind, the main advantage is the re-analysis of existing data and the parallel functional insights that can be obtained.

Lineage analysis is more straightforward with DNA sequencing, but with an error rate of ~10-9 per base per division, one needs to sequence a billion base pairs to distinguish between immediate daughter cells. By contrast, with an inferred error rate of ~10-2 per fCpG per division, much less sequencing (about a million-fold less) is needed to find differences between daughter cells.

g) Lines 208-209: I would be careful with claims of complexity resolution given many of the limitations and inherent systematic similarities, as well as the potential of fCpGs to change back to an ancestral state later in the lineage.

Have modified the manuscript to indicate the analysis would be more challenging due to back changes.

h) There seem to be few figures that assess phenomena across the three brains. Even when they exist there is no attempt to provide any statistical analyses to support the conclusions or permutations to assess outlier status relative to expectations.

The analysis could be more extensive, but with only three brains, any results, like this study itself, would be rightly judged inadequate.

Figure 2B: there appears to be a higher number of '0s' for, for instance, inhibitory neurons compared to excitatory neurons. Is that correct and worth mentioning? The changing axes scales also make it hard to assess.

Inhibitory neurons do appear to have more unmethylated fCpGs compared to excitatory neurons, but in general, most inhibitory fCpGs are methylated with a skew to fully methylated fCpGs, consistent with the barcode starting predominately methylated and inhibitory neurons generally appearing earlier in development relative to excitatory neurons.

j) Figure 2C: I have several issues with this. A minor one is the use of 'Glial' which, I believe, does not appear anywhere else before this, so I am unclear what this curve represents. Generally, however, I am not sure what the y-axis represents, as it is not described in the methods or figure legend. I initially thought it was the cumulative frequency, but I do not think that this squares with the data shown in B. I appreciate the overall idea of having 'earlier'/samples with fewer divisions being shifted to the left, but it is very confusing to me when I try to understand the details of the plot.

This graph is now better described in the legend. “Glial” cells are defined as oligodendrocytes and astrocytes. Other non-neuronal cells (such a microglial cells) have now been removed from the graph.

This graph attempts to illustrate how it may be possible to reconstruct brain development from adult neurons, assuming barcodes are mitotic clocks that become polymorphic with cell division. The X axis is “time”, and the Y axis indicates when different cell types reach their adult levels. The cartoon indicates what is visually present along the X axis during development--- brainstem, then ganglionic eminences with a thin cortex, and finally the mature brain with a robust cortex. Time for the X axis is barcode methylation and starts at 100% and ends at 50% or greater methylation. The fCpG barcode methylation of each cell places it on this timeline and indicates when it ceased dividing and differentiated.

The Y axis indicates the progressive accumulation of the final adult contents of each cell type during this timeline. Early in development, the brain is rudimentary and adult cells are absent. At 90% methylation, only the inhibitory neurons in the pons are present. At 80% methylation, some excitatory neurons are beginning to appear. Inhibitory neurons in the pons have reached their final adult levels and many other inhibitory neuron types are reaching adult levels. By 70% methylation, most inhibitory neurons have reached their adult levels, and more adult excitatory neurons (mainly low cortical neurons, L4-6) and glial cells are beginning to appear. By 60% methylation, inhibitory neurogenesis has largely finished. Adult excitatory neurons and glial cells are more abundant and reach their adult levels by 50% or greater cell barcode methylation levels.

The graph illustrates a rough alignment between mitotic ages inferred by barcode methylation levels and the physical appearances of different neuronal types during development. Many neurons die during development, and this graph, if valid, indicates when neurons that survive to adulthood appear during development.

k) Figure 4Bff: it is confusing to me that the text jumps to these panels after introducing Figure 5. This makes it very hard to read this section of the text.

The Figures appear in the order they are first referred to in the text.

l) Figure 5A: could any of this difference be explained by the shared lineage of excitatory neurons and dorsal neocortical glia?

Not sure

m) Figure 5B: after stating that interneurons have a higher lineage fidelity, the figure legend here states the opposite and I am somewhat confused by this statement.

The legend and text have been clarified. Fig 5A restricts fidelity to within inhibitory cell types. Fig 5B compares between neuron subtypes, and illustrates more apparent inhibitory subtype switching, albeit there are more interneuron subtypes than excitatory subtypes.

n) Figure 5E: generally, the use of tSNE for large pairwise distance analysis is often frowned upon (e.g., PMID 37590228), and I would reconsider this argument.

This analysis was an attempt to illustrate that cells of the same phenotype based on their tSNE metrics can be either closely or more distantly related. Although the tSNE comparisons were restricted to subtypes (and not to the entire tSNE graph), tSNE are not designed for such comparisons. This graph and discussion are deleted. 

Reviewer #2 (Public review):

The manuscript by Shibata proposed a potentially interesting idea that variation in methylcytosine across cells can inform cellular lineage in a way similar to single nucleotide variants (SNVs). The work builds on the hypothesis that the "replication" of methylcytosine, presumably by DNMT1, is inaccurate and produces stochastic methylation variants that are inherited in a cellular lineage. Although this notion can be correct to some extent, it does not account for other mechanisms that modulate methylcytosines, such as active gain of methylation mediated by DNMT3A/B activity and activity demethylation mediated by TET activity. In some cases, it is known that the modulation of methylation is targeted by sequence-specific transcription factors. In other words, inaccurate DNMT1 activity is only one of the many potential ways that can lead to methylation variants, which fundamentally weakens the hypothesis that methylation variants can serve as a reliable lineage marker. With that being said (being skeptical of the fundamental hypothesis), I want to be as open-minded as possible and try to propose some specific analyses that might better convince me that the author is correct. However, I suspect that the concept of methylation-based lineage tracing cannot be validated without some kind of lineage tracing experiment, which has been successfully demonstrated for scRNA-seq profiling but not yet for methylation profiling (one example is Delgado et al., nature. 2022).

I thank Reviewer 2 for the careful evaluation. The validation experiment example (Delgado et al.) introduced sequence barcodes in mice, which is not generally feasible for human studies.

(1) The manuscript reported that fCpG sites are predominantly intergenic. The author should also score the overlap between fCpG sites and putative regulatory elements and report p-values. If fCpG sites commonly overlap with regulatory elements, that would increase the possibility that these sites being actively regulated by enhancer mechanisms other than maintenance methyltransferase activity.

As mentioned for Reviewer 1, fCpGs are filtered to eliminate cell type specific methylation.

(2) The overlap between fCpG and regulatory sequence is a major alternative explanation for many of the observations regarding the effectiveness of using fCpG sites to classify cell types correctly. One would expect the methylation level of thousands of enhancers to be quite effective in distinguishing cell types based on the published single-cell brain methylome works.

As mentioned above, the manuscript did not clearly indicate that the fCpG barcode is not a cell type classifier. The distinctions between fCpG barcodes and cell type classifiers are better explained in the new Supplement.

(3) The methylation level of fCpG sites is higher in hindbrain structures and lower in forebrain regions. This observation was interpreted as the hindbrain being the "root" of the methylation barcodes and, through "progressive demethylation" produced the methylation states in the forebrain. This interpretation does not match what is known about methylation dynamics in mammalian brains, in particular, there is no data supporting the process of "progressive demethylation". In fact, it is known that with the activation of DNMT3A during early postnatal development in mice or humans (Lister et al., 2013. Science), there is a global gain of methylation in both CH and CG contexts. This is part of the broader issue I see in this manuscript, which is that the model might be correct if "inaccurate mC replication" is the only force that drives methylation dynamics. But in reality, active enzymatic processes such as the activation of DNMT3A have a global impact on the methylome, and it is unclear if any signature for "inaccurate mC replication" survives the de novo methylation wave caused by DNMT3A activity.

Reviewer 2 highlights a critical potential flaw in that any ancestral signal recorded by random replication errors could be overwritten by other active methylation processes. I cannot present data that indicates fCpG replication errors are never overwritten, but new data indicate barcode reproducibility and stability with aging.

New data are also present where barcodes are compared between daughter cells (zygote to ICM) in the setting of active and passive demethylation, when germline methylation is erased. This new analysis shows that daughter cells in 2 to 8 cell embryos have more related barcodes than morula or ICM cells. The subsequent active remethylation by a wave of DNMT3A activity may underlie the observation that the barcode appears to start predominately methylated in brain progenitors.

(3) Perhaps one way the author could address comment 3 is to analyze methylome data across several developmental stages in the same brain region, to first establish that the signal of "inaccurate mC replication" is robust and does not get erased during early postnatal development when DNMT3A deposits a large amount of de novo methylation.

See above

(4) The hypothesis that methylation barcodes are homogeneous among progenitor cells and more polymorphic in derived cells is an interesting one. However, in this study, the observation was likely an artifact caused by the more granular cell types in the brain stem, intermediate granularity in inhibitory cells, and highly continuous cell types in cortical excitatory cells. So, in other words, single-cell studies typically classify hindbrain cell types that are more homogenous, and cortical excitatory cells that are much more heterogeneous. The difference in cell type granularity across brain structures is documented in several whole-brain atlas papers such as Yao et al. 2023 Nature part of the BICCN paper package.

As noted above, fCpG barcode polymorphisms and cell type differentiation are confounded because cells of the same phenotype tend to have common progenitors. The fCpG barcode is not a cell type classifier but more a cell division clock that becomes polymorphic with time. Although fCpG barcodes could be more polymorphic in cortical excitatory cells because there are many more types, fCpG barcodes would inherently become more polymorphic in excitatory cells because they appear later in development.

(5) As discussed in comment 2, the author needs to assess whether the successful classification of cell types (brain lineage) using fCpG was, in fact, driven by fCpG sites overlapping with cell-type specific regulatory elements.

Although unclear in the manuscript, the fCpG is not a cell classifier and the barcode is polymorphic between cells of the same type. fCpG barcodes can appear to be cell classifiers because cell types appear at different times during development, and therefore different cell types have characteristic average barcode methylation levels.

(6) In Figure 5E, the author tried to address the question of whether methylation barcodes inform lineage or post-mitotic methylation remodeling. The Y-axis corresponds to distances in tSNE. However, tSNE involves non-linear scaling, and the distances cannot be interpreted as biological distances. PCA distances or other types of distances computed from high-dimensional data would be more appropriate.

The Figure and discussion are deleted (similar comment by Reviewer 1)

Reviewer #3 (Public review):

Summary:

In the manuscript entitled "Human Brain Barcodes", the author sought to use single-cell CpG methylation information to trace cell lineages in the human brain.

Strengths:

Tracing cell lineages in the human brain is important but technically challenging. Lineage tracing with single-cell CpG methylation would be interesting if convincing evidence exists.

Weaknesses:

As the author noted, "DNA methylation patterns are usually copied between cell division, but the replication errors are much higher compared to base replication". This unstable nature of CpG methylation would introduce significant problems in inferring the true cell lineage. The unreliable CpG methylation status also raises the question of what the "Barcodes" refer to in the title and across this study. Barcodes should be stable in principle and not dynamic across cell generations, as defined in Reference#1. It is not convincing that the "dynamic" CpG methylation fits the "barcodes" terminology. This problem is even more concerning in the last section of results, where CpG would fluctuate in post-mitotic cells.

I thank Reviewer 3 for his thoughtful and careful evaluation. I think the “barcode” terminology is appropriate. Dynamic engineered barcodes such as CRISPR/Cas9 mutable barcodes are used in biology to record changes over time. The fCpG barcode appears to start with a single state in a progenitor cell and changes with cell division to become polymorphic in adult cells. Therefore, I think the description of a dynamic fCpG barcode is appropriate.

Reviewer #3 (Recommendations for the authors):

(1) As the author noted, "DNA methylation patterns are usually copied between cell division, but the replication errors are much higher compared to base replication". This unstable nature of CpG methylation would introduce significant problems in inferring the true cell lineage. To establish DNA methylation as a means for lineage tracing, one control experiment would be testing whether the DNA methylation patterns can faithfully track cell lineages for in vitro differentiated & visibly tracked cell lineages. Has this kind of experiment been done in the field?

These types of experiments have not been performed to my knowledge and an appropriate tissue culture model is uncertain. New single cell WGBS data from the zygote to ICM indicate that more immediate daughter cells have more related barcodes even in the setting of active DNA demethylation.

(2) The study includes assumptions that should be backed with solid rationale, supporting evidence, or reference. Here are a couple of examples:

a) the author discarded stable CpG sites with <0.2 or >0.8 average methylation without a clear rationale in H02, and then used <0.3 and >0.7 for a specific sample H01.

The filtering was ad hoc and was used to remove, as much as possible, CpG sites with cell type specific or patient specific methylation. CpG sites with skewed methylation are more likely cell type specific, whereas X chromosome CpG sites with methylation closer to 0.5 in male cells are more likely to be unstable. The ad hoc filtering attempted to remove cell specific CpGs sites while still retaining enough CpG sites to allow comparisons between cells.

b) The author assumed that the early-formed brain stem would resemble progenitors better and have a higher average methylation level than the forebrain. However, this difference in DNA methylation status could reflect developmental timing or cell type-specific gene expression changes.

This observation that brain stem neurons that appear early in development have highly methylated fCpG barcodes in all 3 brains supports the idea that the fCpG barcode starts predominately methylated. Alternative explanations are possible.

(3) The conclusion that excitatory neurons undergo tangential migration is unclear - how far away did the author mean for the tangential direction? Lateral dispersion is known, but it would be striking that the excitatory neurons travel across different brain regions. The question is, how would the author interpret shared or divergent methylation for the same cell type across different brain regions?

As noted with Reviewer 1, this analysis is modified to indicate that evidence of tangential migration is greater for inhibitory than excitatory neurons, but the extent of excitatory neuron migration is uncertain because of sparse sampling, and because fCpG barcodes can be similar by chance.

(4) The sparsity and resolution of the single-cell DNA methylation data. The methylation status is detected in only a small fraction (~500/31,000 = 1.6%) of fCpGs per cell, with only 48 common sites identified between cell pairs. Given that the human genome contains over 28 million CpG sites, it is important to evaluate whether these fCpGs are truly representative. How many of these sites were considered "barcodes"?

fCpG barcodes are distinct from traditional cell type classifiers, and how fCpGs are identified are better outlined in the new Supplement.

(5) While focusing on the X-chromosome may simplify the identification of polymorphic fCpGs, the confidence in determining its methylation status (0 or 1) is questionable when a CpG site is covered by only one read. Did the author consider the read number of detected fCpGs in each cell when calculating methylation levels? Certain CpG sites on autosomes may also have sufficient coverage and high variability across cells, meeting the selection criteria applied to X-chromosome CpGs.

In most cases, a fCpG site was covered by only a single read

(6) The overall writing in the Title, the Main text, Figure legends, and Methods sections are overly simplified, making it difficult to follow. For instance, how did the author perform PWD analysis? How did they handle missing values when constructing lineage trees?

There is not much introduction to lineage tracing in the human brain or the use of DNA methylation to trace cell lineage.

These shortcomings are improved in the manuscript and with the new Supplement. The analysis pipeline including the Python programs are outlined and included as new Supplemental materials. IQ tree can handle the binary fCpG barcode data and skips missing values with its standard settings.

Line 80: it is unclear: "Brain patterns were similar"

Clarified

Line 98: The meaning is unclear here: "Outer excitatory and glial progenitor cells are present" What are these glial progenitor cells and when/how they stop dividing?

The glial cells are the oligodendrocytes and astrocytes. The main take away point is that these glial cells have low barcode methylation, consistent with their appearances later in development.

Line 104: It is unclear if this is a conclusion or assumption -- "A progenitor cell barcode should become increasingly polymorphic with subsequent divisions." The "polymorphic" happens within the progenitors, their progenies, or their progenies at different time points.

The statement is now clarified as an assumption in the manuscript.

Similarly line 134 "Barcodes would record neuronal differentiation and migration." Is this a conclusion from this study or a citation? How is the migration part supported?

The reasoning is better explained in the manuscript.  Migration can be documented if immediate daughter cells with similar barcodes are found in different parts of the adult brain, albeit analysis is confounded by sparse sampling and because barcodes may be similar by chance.

Line 148 and 150: "Nearest neighbor ... neuron pairs" in DNA methylation status would conceivably reflect their cell type-specific gene expression, how did the author distinguish this from cell lineage?

As noted above, because cells with similar phenotypes usually arise from common progenitors, cells within a clade are also usually related. However, the barcodes are still polymorphic within a clade and potentially add complementary information on mitotic ages, ancestry within a clade, and possible cell migration.

Figure 3C: "Cells that emerge early in development" Where are they on the figure?

Hindbrain neurons differentiate early in development and their barcodes are more methylated. The figure has been modified to label some of the values with their neuron types. Also, the older figure mistakenly included data from all 3 brains and now the data are only from brain H01.

Figures 4D and 4E, distinguishing cell subtypes is challenging, as the same color palette is used for both excitatory and inhibitory neurons.

Unfortunate limitations due to complexity and color limitations

Figures 4 and 5, what are these abbreviations?

The abbreviations are presented in Figure 1 and maintained in subsequent figures.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors intended to investigate the earliest mechanisms enabling self-prioritization, especially in the attention. Combining a temporal order judgement task with computational modelling based on the Theory of Visual Attention (TVA), the authors suggested that the shapes associated with the self can fundamentally alter the attentional selection of sensory information into awareness. This self-prioritization in attentional selection occurs automatically at early perceptual stages. Furthermore, the processing benefits obtained from attentional selection via self-relatedness and physical salience were separated from each other.

Strengths:

The manuscript is written in a way that is easy to follow. The methods of the paper are very clear and appropriate.

Thank you for your valuable feedback and helpful suggestions. Please see specific answers below.

Weaknesses:

There are two main concerns:

(1) The authors had a too strong pre-hypothesis that self-prioritization was associated with attention. They used the prior entry to consciousness (awareness) as an index of attention, which is not appropriate. There may be other processing that makes the stimulus prior to entry to consciousness (e.g. high arousal, high sensitivity), but not attention. The self-related/associated stimulus may be involved in such processing but not attention to make the stimulus easily caught. Perhaps the authors could include other methods such as EEG or MEG to answer this question.

We found the possibility of other mechanisms to be responsible for “prior entry” interesting too, but believe there are solid grounds for the hypothesis that it is indicative of attention:

First, prior entry has a long-standing history as in index of attention (e.g., Titchener, 1903; Shore et al., 2001; Yates and Nicholls, 2009; Olivers et al. 2011; see Spence & Parise, 2010, for a review.) Of course, other factors (like the ones mentioned) can contribute to encoding speed. However, for the perceptual condition, we systematically varied a stimulus feature that is associated with selective attention (salience, see e.g. Wolfe, 2021) and kept other features that are known to be associated with other factors such as arousal and sensitivity constant across the two variants (e.g. clear over threshold visibility) or varied them between participants (e.g. the colours / shapes used).

Second, in the social salience condition we used a manipulation that has repeatedly been used to establish social salience effects in other paradigms (e.g., Li et al., 2022; Liu & Sui, 2016; Scheller et al., 2024; Sui et al., 2015; see Humphreys & Sui, 2016, for a review). We assume that the reviewer’s comment suggests that changes in arousal or sensitivity may be responsible for social salience effects, specifically. We have several reasons to interpret the social salience effects as an alteration in attentional selection, rather than a result of arousal or sensitivity:

Arousal and attention are closely linked. However, within the present model, arousal is more likely linked to the availability of processing resources (capacity parameter C). That is, enhanced arousal is typically not stimulus-specific, and therefore unlikely affects the *relative* advantage in processing weights/rates of the self-associated (vs other-associated) stimuli. Indeed, a recent study showed that arousal does not modulate the relative division of attentional resources (as modelled by the Theory of Visual Attention; Asgeirsson & Nieuwenhuis, 2017). As such, it is unlikely that arousal can explain the observed results in relative processing changes for the self and other identities.

Further, there is little reason to assume that presenting a different shape enhances perceptual sensitivity. Firstly, all stimuli were presented well above threshold, which would shrink any effects that were resulting from increases in sensitivity alone. Secondly, shape-associations were counterbalanced across participants, reducing the possibility that specific features, present in the stimulus display, lead to the measurable change in processing rates as a result of enhanced shape-sensitivity.

Taken together, both, the wealth of literature that suggests prior entry to index attention and the specific design choices within our study, strongly support the notion that the observed changes in processing rates are indicative of changes in attentional selection, rather than other mechanisms (e.g. arousal, sensitivity).

(2) The authors suggested that there are two independent attention processes. I suspect that the brain needs two attention systems. Is there a probability that the social and perceptual (physical properties of the stimulus) salience fired the same attention processing through different processing?

We appreciate this thought-provoking comment. We conceptualize attention as a process that can facilitate different levels of representation, rather than as separate systems tuned to specific types of information. Different forms of representation, such as the perceptual shape, or the associated social identity, may be impacted by the same attentional process at different levels of representation. Indeed, our findings suggest that both social and perceptual salience effects may result from the same attentional system, albeit at different levels of representation. This is further supported by the additivity of perceptual and social salience effects and the negative correlation of processing facilitations between perceptually and socially salient cues. These results may reflect a trade-off in how attentional resources are distributed between either perceptually or socially salient stimuli.

Reviewer #2 (Public review):

Summary:

The main aim of this research was to explore whether and how self-associations (as opposed to other associations) bias early attentional selection, and whether this can explain well-known self-prioritization phenomena, such as the self-advantage in perceptual matching tasks. The authors adopted the Visual Attention Theory (VAT) by estimating VAT parameters using a hierarchical Bayesian model from the field of attention and applied it to investigate the mechanisms underlying self-prioritization. They also discussed the constraints on the self-prioritization effect in attentional selection. The key conclusions reported were:

(1) Self-association enhances both attentional weights and processing capacity

(2) Self-prioritization in attentional selection occurs automatically but diminishes when active social decoding is required, and

(3) Social and perceptual salience capture attention through distinct mechanisms.

Strengths:

Transferring the Theory of Visual Attention parameters estimated by a hierarchical Bayesian model to investigate self-prioritization in attentional selection was a smart approach. This method provides a valuable tool for accessing the very early stages of self-processing, i.e., attention selection. The authors conclude that self-associations can bias visual attention by enhancing both attentional weights and processing capacity and that this process occurs automatically. These findings offer new insights into self-prioritization from the perspective of the early stage of attentional selection.

Thank you for your valuable feedback and helpful suggestions. Please see specific answers below.

Weaknesses:

(1) The results are not convincing enough to definitively support their conclusions. This is due to inconsistent findings (e.g., the model selection suggested condition-specific c parameters, but the increase in processing capacity was only slight; the correlations between attentional selection bias and SPE were inconsistent across experiments), unexpected results (e.g., when examining the impact of social association on processing rates, the other-associated stimuli were processed faster after social association, while the self-associated stimuli were processed more slowly), and weak correlations between attentional bias and behavioral SPE, which were reported without any p-value corrections. Additionally, the reasons why the attentional bias of self-association occurs automatically but disappears during active social decoding remain difficult to explain. It is also possible that the self-association with shapes was not strong enough to demonstrate attention bias, rather than the automatic processes as the authors suggest. Although these inconsistencies and unexpected results were discussed, all were post hoc explanations. To convince readers, empirical evidence is needed to support these unexpected findings.

Thank you for outlining the specific points that raise your concern. We were happy to address these points as follows:

a. Replications and Consistency: In our study, we consistently observed trends (relative reduction in processing speed of the self-associated stimulus) in the social salience conditions across experiments. While Experiment 2 demonstrated a significant reduction in processing rate towards self-stimuli, there was a notable trend in Experiment 1 as well.

b. Condition-specific parameters: The condition-specific C parameters, though presenting a small effect size, significantly improved model fit. Inspecting the HDI ranges of our estimated C parameters indicates a high probability (85-89%) that processing capacity increased due to social associations, suggesting that even small changes (~2Hz) can hold meaningful implications within the context attentional selection.

Please also note that the main conclusions about relative salience (self/other, salient/non-salient) are based on the relative processing rates. Processing rates are the product of the processing capacity (condition- but not stimulus dependent) and the attentional weight (condition and stimulus dependent). The latter is crucial to judge the *relative* advantage of the salient stimulus. Hence, the self-/salient stimulus advantage that is reflected in the ‘processing rate difference’ is automatically also reflected in the relative attentional weights attributed to the self/other and salient/non-salient stimuli. As such, the overall results of an automatic relative advantage of self-associated stimuli hold, independently of the change in overall processing capacity.

c. Correlations: Regarding the correlations the reviewer noted, we wish to clarify that these were exploratory, and not the primary focus of our research. The aim of these exploratory analyses was to gauge the contribution of attentional selection to matching-based SPEs. As SPEs measured via the matching task are typically based on multiple different levels of processing, the contribution of early attentional selection to their overall magnitude was unclear. Without being able to gauge the possible effect sizes, corrected analyses may prevent detecting small but meaningful effects. As such, the effect sizes reported serve future studies to estimate power a priori and conduct well-powered replications of such exploratory effects. Additionally, Bayes factors were provided to give an appreciation of the strength of the evidence, all suggesting at least moderate evidence in favour of a correlation. Lastly, please note that effects that were measured within individuals and task (processing rate increase in social and perceptual decision dimensions in the TOJ task) showed consistent patterns, suggesting that the modulations within tasks were highly predictive of each other, while the modulations between tasks were not as clearly linked. We will add this clarification to the revised manuscript.

d. Unexpected results: The unexpected results concerning the processing rates of other-associated versus self-associated stimuli certainly warrant further discussion. We believe that the additional processing steps required for social judgments, reflected in enhanced reaction times, may explain the slower processing of self-associated stimuli in that dimension. We agree that not all findings will align with initial hypotheses, and this variability presents avenues for further research. We have added this to the discussion of social salience effects.

e. Whether association strength can account for the findings: We appreciate the scepticism regarding the strength of self-association with shapes. However, our within-participant design and control matching task indicate that the relative processing advantage for self-associated stimuli holds across conditions. This makes the scenario that “the self-association with shapes was not strong enough to demonstrate attention bias” very unlikely. Firstly, the relative processing advantage of self-associated stimuli in the perceptual decision condition, and the absence of such advantage in the social decision condition, were evidenced in the same participants. Hence, the strength of association between shapes and social identities was the same for both conditions. However, we only find an advantage for the self-associated shape when participants make perceptual (shape) judgements. It is therefore highly unlikely that the “association strength” can account for the difference in the outcomes between the conditions in experiment 1. Also, note that the order in which these conditions were presented was counter-balanced across participants, reducing the possibility that the automatic self-advantage was merely a result of learning or fatigue. Secondly, all participants completed the standard matching task to ascertain that the association between shapes and identities did indeed lead to processing advantages (across different levels).

In summary, we believe that the evidence we provide supports the final conclusions. We do, of course, welcome any further empirical evidence that could enhance our understanding of the contribution of different processing levels to the SPE and are committed to exploring these areas in future work.

(2) The generalization of the findings needs further examination. The current results seem to rely heavily on the perceptual matching task. Whether this attentional selection mechanism of self-prioritization can be generalized to other stimuli, such as self-name, self-face, or other domains of self-association advantages, remains to be tested. In other words, more converging evidence is needed.

The reviewer indicates that the current findings heavily rely on the perceptual matching task, and it would be more convincing to include other paradigm(s) and different types of stimuli. We are happy to address these points here: first, we specifically used a temporal order paradigm to tap into specific processes, rather than merely relying on the matching task. Attentional selection is, along with other processes, involved in matching, but the TOJ-TVA approach allows tapping into attentional selection specifically.  Second, self-prioritization effects have been replicated across a wide range of stimuli (e.g. faces: Wozniak et al., 2018; names or owned objects: Scheller & Sui, 2022a, or even fully unfamiliar stimuli: Wozniak & Knoblich, 2019) and paradigms (e.g. matching task: Sui et al., 2012; cross-modal cue integration: e.g. Scheller & Sui, 2022b; Scheller et al., 2023; continuous flash suppression: Macrae et al., 2017; temporal order judgment: Constable et al., 2019; Truong et al., 2017). Using neutral geometric shapes, rather than faces and names, addresses a key challenge in self research: mitigating the influence of stimulus familiarity on results. In addition, these newly learned, simple stimuli can be combined with other paradigms, such as the TOJ paradigm in the current study, to investigate the broader impact of self-processing on perception and cognition.

To the best of our knowledge, this is the first study showing evidence about the mechanisms that are involved in early attentional selection of socially salient stimuli. Future replications and extensions would certainly be useful, as with any experimental paradigm.

(3) The comparison between the "social" and "perceptual" tasks remains debatable, as it is challenging to equate the levels of social salience and perceptual salience. In addition, these two tasks differ not only in terms of social decoding processes but also in other aspects such as task difficulty. Whether the observed differences between the tasks can definitively suggest the specificity of social decoding, as the authors claim, needs further confirmation.

Equating the levels of social and perceptual salience is indeed challenging, but not an aim of the present study. Instead, the present study directly compares the mechanisms and effects of social and perceptual salience, specifically experiment 2. By manipulating perceptual salience (relative colour) and social salience (relative shape association) independently and jointly, and quantifying the effects on processing rates, our study allows to directly delineate the contributions of each of these types of salience. The results suggest additive effects (see also Figure 7). Indeed, the possibility remains that these effects are additive because of the use of different perceptual features, so it would be helpful for future studies to explore whether similar perceptual features lead to (supra-/sub-) additive effects. In either case, the study design allows to directly compare the effects and mechanisms of social and perceptual salience.

Regarding the social and perceptual decision dimensions, they were not expected to be equated. Indeed, the social decision dimension requires additional retrieval of the associated identity, making it likely more challenging. This additional retrieval is also likely responsible for the slower responses towards the social association compared to the shape itself. However, the motivation to compare the effects of these two decisional dimensions lies in the assumption that the self needs to be task relevant. Some evidence suggests that the self needs to be task-relevant to induce self-prioritization effects (e.g., Woźniak & Knoblich, 2022). However, these studies typically used matching tasks and were powered to detect large effects only (e.g. f = 0.4, n = 18). As it is likely that lacking contribution of decisional processing levels (which interact with task-relevance) will reduce the SPE, smaller self-prioritization effects that result from earlier processing levels may not be detected with sufficient statistical power. Targeting specific processing levels, especially those with relatively early contributions or small effect sizes, requires larger samples (here: n = 70) to provide sufficient power. Indeed, by contrasting the relative attentional selection effects in the present study we find that the self does not need to be task-relevant to produce self-prioritization effects. This is in line with recent findings of prior entry of self-faces (Jubile & Kumar, 2021)

Reviewer #2 (Recommendations for the authors):

Suggestions:

(1) The research questions should be revised to better align with the conclusions. For example, Q2 is phrased as "Does self-relatedness bias attentional selection at the level of the perceptual feature representation (shape) or at the level of the associated identity (social association)," which is unclear in its reference to "levels." A more appropriate phrasing would be whether the self-association bias occurs automatically or whether it depends on explicit social decoding.

Thank you for this suggestion – we have revised the phrasing accordingly: “Does self-relatedness bias attentional selection automatically or does it require explicit social decoding?”

(2) After presenting the data, it would be helpful to include one or two sentences summarizing the conclusions drawn from the data and how they relate to the research questions. Currently, readers are left to guess whether the results are consistent with the hypotheses.

Thank you for this suggestion, which we think will enhance the clarity of the manuscript – we have added summary sentences when presenting the results:<br /> “This cross-experimental parameter inspection revealed that participants exhibited an attentional selection bias towards socially associated information. Interestingly, enhanced processing speed was observed for other-associated rather than self-associated information, a pattern that diverged from our prediction.”

(1) “Results from experiment 2 demonstrated a faster, more automatic attentional selection for self-associated information when the decision did not require explicit social decoding. When the social identity had to be judged, processing speed for self-associated information decreased. Contrary to the hypothesis that social decoding is necessary for self-prioritization to emerge, these findings suggest that attentional selection can operate automatically to prioritize self-associated information. “

(2) “Taken together, as also confirmed in the cross-experimental analysis, attentional selection favoured the other-related information when social identity had to be judged. In contrast, perceptual salience, as predicted, led to increased processing speed for the more salient stimulus. “

(3) The identity of the "other" used in the experiments is unclear, making it uncertain whether the results are self-specific. It would be beneficial to compare the self condition with a control condition, such as a close friend vs. an unfamiliar other. Alternatively, the results may reflect attentional bias for familiar vs. unfamiliar individuals rather than self-specific bias.

Thank you for this comment. Firstly, we would like to clarify that we have provided participants with a description of who the “other” is (see methods: “At the beginning of this task, participants were told that one of the two geometric shapes that was used in the TOJ task has been assigned to them, and the other shape has been assigned to another participant in the experiment – someone they did not know, but who was of similar age and gender”). We aimed to make the ‘other’ as concrete as possible, while maintaining a ‘stranger’ identity.

Secondly, this specification is in line with the vast majority of the literature, which typically measures the effects of self-prioritization relative to the association with an unfamiliar other (stranger), or an unfamiliar and familiar other (e.g. friend, family member). They find that processing advantages that affect friend-related stimuli (friend-stimuli being processed faster than stranger-associated stimuli) are likely mediated by self-extension, that is, an association of the friend with the self. As such, SPEs, relative to familiar others, are typically smaller in size (see, e.g., Sui et al., 2012). They, however, are less stable and more variable than the self-prioritization effects measured relative to a stranger (see Scheller & Sui, 2022 JEP:HPP). Importantly, this is driven by the variability of the friend-associated stimulus, rather than the self or other-associated stimulus (see Figure 4 in main text and S5 in supplementary material in Scheller & Sui, 2022: https://durham-repository.worktribe.com/output/1210478/the-power-of-the-self-anchoring-information-processing-across-contexts). Effectively, this would suggest that choosing a familiar other as a reference would not only (a) lead to a smaller effect size, but also (b) be a less stable effect, which likely depends on the association the individual has to the other familiar person. In contrast, by associating the other shape with another participant in this experiment, we provide participants not only with a concrete representation of a stranger, but also maximise our ability to detect true effects, as these are likely to be larger and more stable.

(4) The key aspects of the procedure (e.g., the order of different conditions) and its rationale need to be clearly explained before or during the presentation of the results. Currently, readers are left to infer certain details.

Thank you for pointing this out. The methods that provide these details are outlined at the end of the document, however, we agree it would be useful to bring some of these details up. We have therefore revised the methods figure (Figure 3) to include an outline of the task type, order, and trial numbers. Task boxes are colour coded by the conditions that are listed in the results figures of the manuscript. We also added these details to the caption of Figure 3.

“Task structures of Experiments 1 and 2. Both experiments started with a TOJ baseline task. In Experiment 1, only non-salient targets were presented, while in Experiment 2, perceptually salient and non-salient trials were included. These were presented in randomly intermixed order. Next, targets were associated with social identities. Associations were practiced using the matching task. Following association learning, which attaches social salience to the shapes, participants completed the same TOJ task as before. In Experiment 1, they completed one block using a social decision dimension, and one block using a perceptual decision dimension. The order of these blocks was counterbalanced across participants to reduce the influence of order effects in the results. In Experiment 2, perceptually salient and non-salient stimuli were presented in an intermixed fashion, and participants responded within the social decision dimension. Each task block was preceded by 8 (matching) to 14 (TOJ) practice trials.”

(5) Certain imprecise terms used to describe the results, such as "slightly," "roughly," and "loosely," create confusion for the readers. The authors should take a clearer stance on the results and provide an explanation for why the data only "slightly," "roughly," or "loosely" support the findings.

Thank you for highlighting this. We have provided a more concrete wording and details throughout (e.g., “target shapes’ were 30% bigger than the ‘background shapes”).

Lastly, we have updated the formatting of the manuscript to provide higher fidelity figures, which were previously compromised by file conversion.

Author response:

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

eLife Assessment

This provocative manuscript from presents valuable comparisons of the morphologies of Archaean bacterial microfossils to those of microbes transformed under environmental conditions that mimic those present on Earth during the same Eon, although the evidence in support of the conclusions is currently incomplete. The reasons include that taphonomy is not presently considered, and a greater diversity of experimental environmental conditions is not evaluated -- which is important because we ultimately do not know much about Earth's early environments. The authors may want to reframe their conclusions to reflect this work as a first step towards an interpretation of some microfossils as 'proto-cells,' and less so as providing strong support for this hypothesis. 

Regarding the taphonomic alterations: The editor and reviewers are correct in pointing out this issue. Taphonomic alteration of the microfossils attains special significance in the case of microorganisms, as they lack rigid structures and are prone to morphological alterations during or after their fossilization. We are acutely aware of this issue and have conducted long-term experiments (lasting two years) to observe how cells die, decay, and get preserved. A large section of the manuscript (pages 11 to 20) and a substantial portion of the supplementary information is dedicated to understanding the taphonomic alterations. To the best of our knowledge, these are among the longest experiments done to understand the taphonomic alterations of the cells within laboratory conditions. 

Recent reports by Orange et al. (1,2)  showed that under favorable environmental conditions, cells could be fossilized rather rapidly with little morphological modifications. We observed a similar phenomenon in this work. Cells in our study underwent rapid encrustation with cations from the growth media. We have analyzed the morphological changes over a period of 18 months. After 18 months, the softer biofilms got encrusted entirely in salt and turned solid (Fig. ). Despite this transformation, morphologically intact cells could still be observed within these structures. This suggests that the cells inhabiting Archaean coastal marine environments could undergo rather rapid encrustation, and their morphological features could be preserved in the geological record with little taphonomic alteration.    

Regarding the environmental conditions: We are in total agreement with the reviewers that much is unknown about Archaean geology and its environmental conditions. Like the present-day Earth, Archaean Earth certainly had regions that greatly differed in their environmental conditions—volcanic freshwater ponds, brines, mildly halophilic coastal marine environments, and geothermal and hydrothermal vents, to name a few. Our experimental design focuses on one environment we have a relatively good understanding of rather than the rest of the planet, of which we know little. Below, we list our reasons for restricting to coastal marine environments and studying cells under mildly halophilic experimental conditions.  

(1) Very little continental crust from Haden and early Archaean Eon exists on the presentday Earth. Much of our geochemical understanding of this time period was a result of studying the Pilbara Iron Formations and the Barberton Greenstone Belt. Geological investigations suggest that these sites were coastal marine environments. The salinity of coastal marine environments is higher than that of open oceans due to the greater water evaporation within these environments. Moreover, brines were discovered within pillow basalts within the Barberton greenstone belt, suggesting that the salinity within these sites is higher or similar to marine environments. 

(2) We are not certain about the environmental conditions that could have supported the origin of life. However, all currently known Archaean microfossils were reported from coastal marine environments (3.8-2.4Ga). This suggests that proto-life likely flourished in mildly halophilic environments, similar to the experimental conditions employed in our study. 

(3) The chemical analysis of Archaean microfossils also suggests that they lived in saltrich environments, as most, if not all, microfossils are closely associated, often encrusted in a thin layer of salt.  

However, we concur with the reviewers that our interpretations should be reassessed if Archaean microfossils that greatly differ from the currently known microfossils are to be discovered or if new microfossils are to be reported from environments other than coastal marine sites.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Microfossils from the Paleoarchean Eon represent the oldest evidence of life, but their nature has been strongly debated among scientists. To resolve this, the authors reconstructed the lifecycles of Archaean organisms by transforming a Gram-positive bacterium into a primitive lipid vesicle-like state and simulating early Earth conditions. They successfully replicated all morphologies and life cycles of Archaean microfossils and studied cell degradation processes over several years, finding that encrustation with minerals like salt preserved these cells as fossilized organic carbon. Their findings suggest that microfossils from 3.8 to 2.5 billion years ago were likely liposome-like protocells with energy conservation pathways but without regulated morphology. 

Strengths: 

The authors have crafted a compelling narrative about the morphological similarities between microfossils from various sites and proliferating wall-deficient bacterial cells, providing detailed comparisons that have never been demonstrated in this detail before. The extensive number of supporting figures is impressive, highlighting numerous similarities. While conclusively proving that these microfossils are proliferating protocells morphologically akin to those studied here is challenging, we applaud this effort as the first detailed comparison between microfossils and morphologically primitive cells. 

Weaknesses: 

Although the species used in this study closely resembles the fossils morphologically, it would be beneficial to provide a clearer explanation for its selection. The literature indicates that many bacteria, if not all, can be rendered cell wall-deficient, making the rationale for choosing this specific species somewhat unclear. While this manuscript includes clear morphological comparisons, we believe the authors do not adequately address the limitations of using modern bacterial species in their study. All contemporary bacteria have undergone extensive evolutionary changes, developing complex and intertwined genetic pathways unlike those of early life forms. Consequently, comparing existing bacteria with fossilized life forms is largely hypothetical, a point that should be more thoroughly emphasized in the discussion. 

Another weak aspect of the study is the absence of any quantitative data. While we understand that obtaining such data for microfossils may be challenging, it would be helpful to present the frequencies of different proliferative events observed in the bacterium used. Additionally, reflecting on the chemical factors in early life that might cause these distinct proliferation modes would provide valuable context. 

Regarding our choice of using modern organisms or this particular bacterial species: 

Based on current scientific knowledge, it is logical to infer that cellular life originated as protocells; nevertheless, there has been no direct geological evidence for the existence of such cells on early Earth. Hence, protocells remain an entirely theoretical concept. Moreover, protocells are considered to have been far more primitive than present-day cells. Surprisingly, this lack of sophistication was the biggest challenge in understanding protocells. Designing experiments in which cells are primitive (but not as primitive as non-living lipid vesicles) and still retain a functional resemblance to a living cell does pose some practical challenges. Laboratory experiments with substitute (proxy) protocells almost always come with some limitations. Although not a perfect proxy, we believe protocells and protoplasts share certain characteristics. Having said that, we would like to reemphasize that protoplasts are not protocells. Our reasons for using protoplasts as model organisms and working with this bacterial species (Exiguobacterium Strain-Molly) are based on several scientific and practical criteria listed below.

(1) Irrespective of cell physiology and intracellular complexity, we believe that protoplasts and protocells share certain similarities in the biophysical properties of their cytoplasm. We explained our reasoning in the manuscript introduction and in our previous manuscripts (Kanaparthi et al., 2024 & Kanaparthi et al., 2023). In short, to be classified as a cell, even a protocell should possess minimal biosynthetic pathways, a physiological mechanism of harvesting free energy from the surrounding (energy-yielding pathways), and a means of replicating its genetic material and transferring it to the daughter cells. These minimal physiological processes could incorporate considerable cytoplasmic complexity. Hence, the biophysical properties of the protocell cytoplasm could have resembled those of the cytoplasm of protoplasts, irrespective of the genomic complexity. 

(2) Irrespective of their physiology, protoplasts exhibit several key similarities to protocells, such as their inherent inability to regulate their morphology or reproduction. This similarity was pointed out in previous studies (3). Despite possessing all the necessary genetic information, protoplasts undergo reproduction through simple physiochemical processes independent of canonical molecular biological processes. This method of reproduction is considered to have been erratic and rather primitive, akin to the theoretical propositions on protocells. Although protoplasts are fully evolved cells with considerable physiological complexity, the above-mentioned biophysical similarities suggest that the protoplast life cycle could morphologically resemble that of protocells (in no other aspect except for their morphology and reproduction).  

(3) Physiologically or genomically different species of Gram-positive protoplasts are shown to exhibit similar morphologies. This suggests that when Gram-positive bacteria lose their cell wall and turn into a protoplast,  they reproduce in a similar manner independent of physiological or genome-based differences. As morphology and only morphology is key to our study, at least from the scope of this study, intracellular complexity is not a key consideration. 

(4) This specific strain was isolated from submerged freshwater springs in the Dead Sea. This isolate and members of this bacterial genus are known to have been well acclimatized to growing in a wide range of salt concentrations and in different salt species. This is important for our study (this and previous manuscript), in which cells must be grown not only at high salt concentrations (1-15%) but in different salts like NaCl, MgCl₂, and KCl. 

(5) Our initial interest in this isolate was due to its ability to reduce iron at high salt concentrations. Given that most spherical microfossils are found in Archaean-banded iron formations covered in pyrite, this suggests that these microfossils could have been reducing oxidized iron species like Fe(III). Nevertheless, over the course of our study, we realized the complexities of live cell staining and imaging under anoxic conditions. Given that the scope of the manuscript is restricted only to comparing the morphologies, not the physiology, we abandoned the idea of growing cells under anoxic conditions.  

Based on these observations, cell physiology may not be a key consideration, at least within the scope of studying microfossil morphology. However, we want to emphasize again that “We do not claim present-day protoplasts are protocells.”  

Regarding the absence of quantitative data:

We are unsure what the reviewer meant by the absence of quantitative data. Is it from the cell size/reproductive pathways perspective or from a microfossil/ecological perspective? At the risk of being portrayed in a bad light, we admit that we did not present quantitative data from either of these perspectives. In our defense, this was not due to our lack of effort but due to the practical limitations imposed by our model organism. 

If the reviewer means the quantitative data regarding cell sizes and morphology: In our previous work, we studied the relationship between protoplast morphology, growth rate, and environmental conditions. In that study, we proposed that the growth rate is one factor that regulates protoplast morphology. Nevertheless, we did not observe uniformity in the sizes of the cells. This lack of uniformity was not just between the replicates but even among the cells grown within the same culture flask or the cells within the same microscopic field. Moreover, cells are often observed to be reproducing either by forming internal or external or by both these processes at the same time. The size and morphological differences among cells within a growth stage could be explained by the physiological and growth rate heterogenicity among cells. 

Bacterial growth curves and their partition into different stages (lag, log & stationary), in general, represent the growth dynamics of an entire bacterial population. Nevertheless, averaging the data obscures the behavior of individual cells (4,5). It is known that genetically identical cells within a single bacterial population could exhibit considerable cell-to-cell variation in gene expression (6,7) and growth rates (8). The reason for such stochastic behavior among monoclonal cells has not been well understood. In the case of normal cells, morphological manifestation of these variations is restricted by a rigid cell wall. Given the absence of a cell wall in protoplasts, we assume such cell-to-cell variations in growth rate is manifested in cell morphology. This makes it challenging to quantitatively determine variations in cell sizes or the size increase in a statically robust manner, even in monoclonal cells. 

Although this lack of uniformity in cell sizes should not be perceived as a limitation, this behavior is consistently observed among microfossils. Spherical microfossils of similar morphology but different sizes were reported from different microfossil sites (9,10). In this regard, both protoplasts and microfossils are very similar. 

If the reviewer means the quantitative data from an ecological perspective: 

Based on the elemental composition and the isotopic signatures of the organic carbon, we can deduce if these structures are of biological origin or not. However, any further interpretation of this data to annotate these microfossils to a particular physiology group is fraught with errors. Hence, we refrain from making any inferences about the physiology and ecological function of these microfossils. This lack of clarity on the physiology of microfossils reduces the chance of quantitative studies on their ecological functions. Moreover, we would like to re-emphasize that the scope of this work is restricted to morphological comparison and is not targeted at understanding the ecological function of these microfossils. This narrow objective also limits the nature of the quantitative data we could present.

Moreover, developing a quantitative understanding of some phenomena could be technically challenging. Many theories on the origin of life, like chemical evolution, started with the qualitative observation that lightning could mediate the synthesis of biologically relevant organic carbon. Our quantitative understanding of this process is still being explored and debated even to this day.     

Reviewer #2 (Public Review): 

Summary: 

In summary, the manuscript describes life-cycle-related morphologies of primitive vesiclelike states (Em-P) produced in the laboratory from the Gram-positive bacterium Exiguobacterium Strain-Molly) under assumed Archean environmental conditions. Em-P morphologies (life cycles) are controlled by the "native environment". In order to mimic Archean environmental conditions, soy broth supplemented with Dead Sea salt was used to cultivate Em-Ps. The manuscript compares Archean microfossils and biofilms from selected photos with those laboratory morphologies. The photos derive from publications on various stratigraphic sections of Paleo- to Neoarchean ages. Based on the similarity of morphologies of microfossils and Em-Ps, the manuscript concludes that all Archean microfossils are in fact not prokaryotes, but merely "sacks of cytoplasm". 

Strengths: 

The approach of the authors to recognize the possibility that "real" cells were not around in the Archean time is appealing. The manuscript reflects the very hard work by the authors composing the Em-Ps used for comparison and selecting the appropriate photo material of fossils. 

Weaknesses: 

While the basic idea is very interesting, the manuscript includes flaws and falls short in presenting supportive data. The manuscript makes too simplistic assumptions on the "Archean paleoenvironment". First, like in our modern world, the environmental conditions during the Archean time were not globally the same. Second, we do not know much about the Archean paleoenvironment due to the immense lack of rock records. More so, the Archean stratigraphic sections from where the fossil material derived record different paleoenvironments: shelf to tidal flat and lacustrine settings, so differences must have been significant. Finally, the Archean spanned 2.500 billion years and it is unlikely that environmental conditions remained the same. Diurnal or seasonal variations are not considered. Sediment types are not considered. Due to these reasons, the laboratory model of an Archean paleoenvironment and the life therein is too simplistic. Another aspect is that eucaryote cells are described from Archean rocks, so it seems unlikely that prokaryotes were not around at the same time. Considering other fossil evidence preserved in Archean rocks except for microfossils, the many early Archean microbialites that show baffling and trapping cannot be explained without the presence of "real cells". With respect to lithology: chert is a rock predominantly composed of silica, not salt. The formation of Em-Ps in the "salty" laboratory set-up seems therefore not a good fit to evaluate chert fossils. Formation of structures in sediment is one step. The second step is their preservation. However, the second aspect of taphonomy is largely excluded in the manuscript, and the role of fossilization (lithification) of Em-Ps is not discussed. This is important because Archean rock successions are known for their tectonic and hydrothermal overprint, as well as recrystallization over time. Some of the comparisons of laboratory morphologies with fossil microfossils and biofilms are incorrect because scales differ by magnitudes. In general, one has to recognize that prokaryote cell morphologies do not offer many variations. It is possible to arrive at the morphologies described in various ways including abiotic ones. 

Regarding the simplistic presumptions on the Archaean Eon environmental conditions, we provided a detailed explanation of this issue in our response to the eLife evaluation. In short, we agree with the reviewer that little is known about the Archaean Eon environmental conditions at a planetary scale. Hence, we restricted our study to one particular environment of which we had a comparatively good understanding. The Archaean Eon spanned 2.5 billion years. However, most of the microfossil sites we discussed in the manuscript are older than 3 billion years, with one exception (2.4 billion years old Turee Creek microfossils). We presume that conditions within this niche (coastal marine) environment could not have changed greatly until 2Ga, after which there have been major changes in the ocean salt composition and salinities.

In the manuscript, we discussed extensively the reasons for restricting our study to these particular environmental conditions. Further explanations of these choices are presented in our response to the eLife evaluation (also see our previous manuscript). In short, the fact that all known microfossils are restricted to coastal marine environments justifies the experimental conditions employed in our study. Nevertheless, we agree with the reviewer that all lab-based studies involve some extent of simplification. This gap/mismatch is even wider when it comes to studies involving origin or early life on Earth.

We are not arguing that prokaryotes are not around at this time. The key message of the manuscript is that they are present, but they have not developed intracellular mechanisms to regulate their morphology and remained primitive in this aspect.  

The sizes of the microfossils and cells from our study were similar in most cases. However, we agree with the reviewer that they deviated considerably in some cases, for example, S70, S73, and S83. These size variations are limited to sedimentary structures like laminations rather than cells. These differences should be expected as we try to replicate the real-life morphologies of biofilms that could have extended over large swats of natural environments in a 2ml volume chamber slide. More specifically, in Fig. S70, there is a considerable size mismatch. But, in Fig. S73, the sizes were comparable between A & C (of course, the size of our reproduction did not match B). In the case of Fig. S83, we do not see a huge size mismatch.      

Reviewer #1 (Recommendations For The Authors): 

We would like to provide several suggestions for changes in text and additions to data analysis. 

39-41: It has been stated that reconstructing the lifecycle is the only way of understanding the nature of these microfossils. First of all, I would rephrase this to 'the most promising way', as there are always multiple approaches to comparing phenomena. 

We agree with the reviewer's suggestion. The suggested changes have been made (line 41). 

125: Please rephrase "under the environmental condition of early Earth" to "under experimental conditions possibly resembling the conditions of the Paleoarchean Eon". Now it sounds like the exact environmental conditions have been produced, which has already been debated in the discussion. 

We agree with the reviewer's suggestion. The suggested changes have been made (line 127). 

125: Please mention the fold change in size, the original size in numbers, and whether this change is statistically significant. 

In the above sections of this document, we explained our reservations about presenting the exact number.

128: Have you found a difference in the relative percentages of modes of reproduction? In other words, is there a difference in percentage between forming internal daughter cells or a string of external daughter cells? 

We explained our reservations about presenting the exact number above. But this has been extensively discussed in our accompaining manuscript. We want to reemphasize that the scope of this manuscript is restricted to comparing morphologies rather than providing a mechanistic explanation of the reproduction process. 

151: A similar model for endocytosis has already been described in proliferating wall-less cells (Kapteijn et al., 2023). In the discussion, please compare your results with the observations made in that paper. 

This is an oversight on our part. The manuscript suggested by the reviewer has now been added (line 154 & 155).  

163: Please use another word for uncanny. We suggest using 'strong resemblance'. 

We changed this according to the reviewers' suggestion (line 168). 

433: Please elaborate on why the results are not shown. This sounds like a statement that should be substantiated further. 

To observe growth and simultaneously image the cells, we conducted these experiments in chamber slides (2ml volume). Over time, we observed cells growing and breaking out of the salt crust (Fig. S86, S87 & Movie 22) and a gradual increase in the turbidity of the media. Although not quantitative, this is a qualitative indication of growth. We did not take precise measurements for several reasons. This sample is precious; it took us almost two years to solidify the biofilm completely, as shown in Fig. S84A. Hence, it was in limited supply, which prevented us from inoculating these salt crusts into large volumes of fresh media. Given a long period of starvation, these cells often exhibited a long lag phase (several days), and there wasn't enough volume to do OD measurements over time. 

We also crushed the solidified biofilm with a sterile spatula before transferring it into the chamber slide with growth media. This resulted in debris in the form of small solid particles, which interfered with our OD measurements. These practical considerations made it challenging to determine the growth precisely. Despite these challenges, we measured an OD of 4 in some chamber slides after two weeks of incubation. Given that these measurements were done haphazardly, we chose not to present this data. 

456: Could you please double-check whether the description is correct for the figure? 8C and 8D are part of Figure 8B, but this is stated otherwise in the description. 

We thank the reviewer for pointing it out. It has now been rectified (line 461-472).

Reviewer #2 (Recommendations For The Authors): 

We thank Reviewer #2  for carefully reading the manuscript and such an elaborate list of questions. The revisions suggested have definitely improved the quality of the manuscript. Here, we would like to address some of the questions that came up repeatedly below. One frequently asked question is regarding the letters denoting the individual figures within the images. For comparison purposes, we often reproduced previously published images. To maintain a consistent figure style, we often have to block the previous denotations with an opaque square and give a new letter. 

The second question that appeared repeatedly below is the missing scale bars in some of the images within a figure. We often did not include a scale bar in the images when this image is an enlarged section of another image within the same figure.     

Title: Please consider being more precise in the title. Microfossils are only one fossil group of "oldest life". Perhaps better: "On the nature of some microfossils in Archean rocks". (see also Line 37).  

Authors’ response: The title conveys a broader message without quantitative insinuations. If our manuscript had been titled "On the nature of all known Archaean microfossils,” we should have agreed with the reviewer's suggestion and changed it to "On the nature of some microfossils in Archean rocks". As it is not, we respectfully decline to make this modification.     

Abstract:  

Line 41: "one way", not "the only way" 

We agree with the reviewer’s comment, and necessary changes have been made (line 41).  

Introduction: 

Line 58f: "oldest sedimentary rock successions", not "oldest known rock formations". There are rocks of much older ages, but those are not well preserved due to metamorphic overprint, or the rocks are igneous to begin with. Minor issue: please note that "formations" are used as stratigraphic units, not so much to describe a rock succession in the field. 

We agree with the reviewer’s comment and have made necessary changes (line 58).

Line 67: Microfossils are widely accepted as evidence of life. Please rephrase. 

We agree with the reviewer’s comment, and necessary changes have been made.

Line 71 - 74: perhaps add a sentence of information here.

We agree with the reviewer’s comment, and necessary changes have been made (line 71).

Line 76: which "chemical and mineralogical considerations"? 

This has been rephrased to “Apart from the chemical and δ¹³C-biomass composition” (line 76).

Line 84ff: This is a somewhat sweeping statement. Please remember that there are microbialites in such rocks that require already a high level of biofilm organization. The existence of cyanobacteria-type microbes in the Archean is also increasingly considered. 

We are aware of literature that labeled the clusters of Archaean microfossils as biofilms and layered structures as microbialites or stromatolite-like structures. However, the use of these terms is increasingly being discouraged. A more recent consensus among researchers suggests annotating these structures simply as sedimentary structures, as microbially induced sedimentary structures (MISS). 

We respectfully disagree with the reviewer’s comment that Archaean microfossils exhibit a high level of biofilm organization. We are not aware of any studies that have conducted such comprehensive research on the architecture of Archaean biofilms. We are not even certain if these clusters of Archaean cells could even be labeled as biofilms in the true sense of the term. We presently lack an exact definition of a biofilm. In our study, we do see sedimentation and bacteria and their encapsulation in cell debris. From a broader perspective, any such aggregation of cells enclosed in cell debris could be annotated as a biofilm. However, more in-depth studies show that biofilm is not a random but a highly organized structure. Different bacterial species have different biofilm architectures and chemical composition. The multispecies biofilms in natural environments are even more complex. We do agree with the reviewer that these structures could broadly be labeled as biofilms, but we presently lack a good, if any, understanding of the Archaean biofilm architecture. 

Regarding the annotation of microfossils as cyanobacteria, we respectfully disagree with the reviewer. This is not a new concept. Many of the Archaean microfossils were annotated as cyanobacteria at the time of their discovery. This annotation is not without controversy. With the advent of genome-based studies, researchers are increasingly moving away from this school of thought.  

Line 101ff: The conditions on early Earth are unknown - there are many varying opinions. Perhaps simply state that this laboratory model simulates an Archean Earth environment of these conditions outlined. 

This is a good idea. We thank the reviewer for this suggestion, and we made appropriate changes. 

Line 112: manuscript to be replaced by "paper"? 

This change has been made (line 114).

Line 116: "spanned years" - how many years? 

We now added the number of years in the brackets (line 118).

Results: 

Line 125: see comment for 101ff. 

we made appropriate changes. 

Figure 1: Caption: Please write out ICV the first time this abbreviation is used. Images: Note that some lettering appears to not fit their white labels underneath. (G, H, I, J0, and M). 

We apologize; this is an oversight on our part. We now spell complete expansion of ICV, the first time we used this abbreviation. 

We took these images from previously published work (references in the figure legend), so we must block out the previous figure captions. This is necessary to maintain a uniform style throughout the manuscript. 

Line 152ff.: here would be a great opportunity to show in a graph the size variations of modern ICVs and to compare the variations with those in the fossil material. 

In the above sections of this document, we explained our reservations about presenting the exact number.

Line 159f.: Fig.1K - what is to see here? Maybe a close-up or - better - a small sketch would help? 

Fig. 1K shows the surface depressions formed during the vesicle formation. The surface characteristics of EM-P and microfossils is very similar.   

Line 161f.: reference?  

The paragraph spanning lines 159 to 172 discusses the morphological similarities between EM-P and SPF microfossils. We rechecked the reference no 35 (Delarue 2019). This is the correct reference. We do not see a mistake if the reviewer meant the reference to the figures.    

Line 164ff.: A question may be asked, how many fossils of the Strelley Pool population would look similar to the "modeled" ones. Questions may rise in which way the environmental conditions control such morphology variations. Perhaps more details? 

This relationship between the environmental conditions and the morphology is discussed extensively in our previous work (11).  

Line 193: what is meant by "similar discontinuous distribution of organic carbon"?

This statement highlights similarities between EM-P and microfossils. The distribution of cytoplasm within the cells is not uniform. There are regions with and devoid of cytoplasm, which is quite unusual for bacteria. Some previous studies argued that this could indicate that these organic structures are of abiotic origin. Here, we show that EMP-like cells could exhibit such a patchy distribution of cytoplasm within the cell.    

Line 218 - 291: The observations are very nice, however, the figures of fossil material in Figures 3 A, B, and C appear not to conform. Perhaps use D, E and I to K. Also, S48 does not show features as described here (see below).  

We did not completely understand the reviewer’s question. As mentioned in the figure legend, both the microfossils and the cells exhibit string with spherical daughter cells within them. Moreover, there are also other similarities like the presence of hollow spherical structures devoid of organic carbon. We also saw several mistakes in the Fig. S48 legend. We have rectified them, and we thank the reviewer for pointing them out.   

Line 293f: Title with "." at end?

This change has been made.

Line 298: predominantly in chert. In clastic material preservation of cells and pores is unlikely due to the common lack of in situ entombment by silica. 

We rephrased this entire paragraph to better convey our message. Either way, we are not arguing that hollow pore spaces exist. As the reviewer mentioned, they will, of course, be filled up with silica. In this entire paragraph, we did not refer to hollow spaces. So, we are not entirely sure what the question was.     

Line 324, 328-349: Please see below comments on the supplementary figures 51-62. Some of the interpretations of morphologies may be incorrect. 

Please find our response to the reviewer’s comments on individual figures below.  

Figure 5 A to D look interesting, however E to J appear to be unconvincing. What is the grey frame in D (not the white insert). 

The grey color is just the background that was added during the 3D rendering process.  

Figure 6 does not appear to be convincing. - Erase? 

We did not understand the reviewer’s reservations regarding this figure. Images A-F within the figure show the gradual transformation of cells into honeycomb-like structures, and images G-J show such structures from the Archaean that are closely associated with microfossils. Moreover, we did not come up with this terminology (honeycomb-like). Previous manuscripts proposed it.  

Line 379ff: S66 and 69, please see my comments below. Microfossils "were often discovered" in layers of organic carbon. 

Please see our response below.   

Line 393-403: Laminae? There are many ways to arrive at C-rich laminae, especially, if the material was compressed during burial. Basically, any type of biofilm would appear as laminae, if compressed. The appearance of thin layers is a mere coincidence. Note that the scale difference in S70, S73, as well as S83, is way too high (cm versus μm!) to allow any such sweeping conclusions. What are α- and β- laminations, the one described by Tice et al.? The arguments are not convincing.

We propose that cells be compressed to form laminae. We answered this question above about the differences in the scale bars. Yes, we are referring to α- and β- laminations described by Tice et al.       

Figure 7: This is an interesting figure, but what are the arguments for B and C, the fossil material, being a membrane? Debris cannot be distinguished with certainty at this scale in the insert of C. B could also be a shriveled-up set of trichomes.  

We agree with the reviewer that debris cannot be definitely differentiated. Traditionally, annotations given to microfossil structures such as biofilm, intact cells, or laminations were all based on morphological similarities with existing structures observed in microorganisms. Given that the structures observed in our study are very similar to the microfossil structures, it is logical to make such inferences. Scales in A & B match perfectly well. The structure in C is much larger, but, as we mentioned in reply to one of the reviewer’s earlier questions, some of the structures from natural environments could not be reproduced at scale in lab experiments. Working in a 2 ml chamber slides does impose some restrictions.   

Figure 8: The figure does not show any honeycomb patterns. The "gaps" in the Moodies laminae are known as lenticular particles in biofilms. They form by desiccated and shriveledup biofilm that mineralizes in situ. Sometimes also entrapped gases induce precipitation. Note also that the modelled material shows a kind of skin around the blobs that are not present in the Moodies material.  

We agree that entrapped gas bubbles could have formed lenticular gaps. In the manuscript, we did not discount this possibility. However, if that is the case, one should explain why we often find clumps of organic carbon within these gaps. As we presented a step-by-step transformation of parallel layers of cells into laminations, which also had similar lenticular gaps, we believe this is a more plausible way such structures could have formed. In the end, there could have been more than one way such structures could have been formed. 

We do see the honeycomb pattern in the hollow gaps. Often, the 3D-rendering of the STED images obscures some details. Hence, in the figure legend, we referred to the supplementary figures also show the sequence of steps involved in the formation of such a pattern.      

Line 405-417: During deposition of clastic sediment any hollow space would be compressed during burial and settling. It is rare that additional pore space (except between the graingrain-contacts) remains visible, especially after consolidation. The exception would be if very early silicification took place filling in any pore space. What about EPS being replaced by mineralic substance? The arguments are not convincing. 

We are suggesting that EPS or cell debris is rapidly encrusted by cations from the surrounding environment and gets solidified into rigid structures. This makes it possible for the structures to be preserved in the fossil record. We believe that hollow structures like the lenticular gaps will be filled up with silica. 

We do not agree with the reviewer’s comment that all biological structures will be compressed. If this is true, there should be no intact microfossils in the Archaean sedimentary structures, which is definitely not the case.      

Line 419-430: Lithification takes place within the sediment and therefore is commonly controlled by the chemistry of pore water and chemical compounds that derive from the dissolution of minerals close by. Another aspect to consider is whether "desiccation cracks" on that small scale may be artefacts related to sample preparation (?).  

We agree that desiccation cracks could have formed during the sample preparation for SEM imaging, as this involves drying the biofilms. However, we observed that the sample we used for SEM is a completely solidified biofilm (Fig. S84), so we expect little change in its morphology during drying. Moreover, visible cracks and pointy edges were also observed in wet samples, as shown in Fig. S87.        

Line 432 - 439: Please see comments on the supplementary material below.

Please find our response to the reviewer’s comments on individual figures below.  

Discussion:  

Line 477f: "all known microfossil morphologies" - is this a correct statement? Also, would the Archean world provide only one kind of "EM-P type"? Morphologies of prokaryote cells (spherical, rod-shaped, filamentous) in general are very simple, and any researcher of Precambrian material will appreciate the difficulties in concluding on taxonomy. There are papers that investigate putative microfossils in chert as features related to life cycles. Microfossil-papers commonly appear not to be controversial give and take some specific cases.  

We made a mistake in using the term “all known microfossil morphologies.” We have now changed it to “all known spherical microfossils” from this statement (line 483). However, we do not agree with the statement that microfossil manuscripts tend not to be controversial. Assigning taxonomy to microfossils is anything but controversial. This has been intensely debated among the scientific community.     

Line 494-496: This statement should be in the Introduction.

We agree with the reviewer’s comment. In an earlier version of the manuscript this statement was in the introduction. To put this statement in its proper context, it needs to be associated with a discussion about the importance of morphology in the identification of microfossils. The present version of the manuscript do not permit moving an entire paragraph into the introduction. Hence, we think making this statement in the discussion section is appropriate. 

Line 484ff. The discussion on biogenicity of microfossils is long-standing (e.g., biogenicity criteria by Buick 1990 and other papers), and nothing new. In paleontology, modern prokaryotes may serve as models but everyone working on Archean microfossils will agree that these cannot correspond to modern groups. An example is fossil "cyanobacteria" that is thought to have been around already in the early Archean. While morphologically very similar to modern cyanobacteria, their genetic information certainly differed - how much will perhaps remain undisclosed by material of that high age.  

Yes, we agree with the reviewer that there has been a longstanding conflict on the topic of biogenicity of microfossils. However, we have never come across manuscripts suggesting that modern microorganisms should only be used as models. If at all, there have been numerous manuscripts suggesting that these microfossils represent cyanobacteria, streptomycetes, and methanotrophs. Regarding the annotation of microfossils as cyanobacteria, we addressed this issue in one of the previous questions raised by the reviewer.    

Line 498ff: Can the variation of morphology and sizes of the EM-Ps be demonstrated statistically? Line 505ff are very speculative statements. Relabeling of what could be vesicles as "microfossils" appears inappropriate. Contrary to what is stated in the manuscript, the morphologies of the Dresser Formation vesicles do not resemble the S3 to S14 spheroids from the Strelley Pool, the Waterfall, and Mt Goldsworthy sites listed in the manuscript. The spindle-shaped vesicles in Wacey et al are not addressed by this manuscript. What roles in mineral and element composition would have played diagenetic alteration and the extreme hydrothermal overprint and weathering typical for Dresser material? S59, S60 do not show what is stated, and the material derives from the Barberton Greenstone Belt, not the Pilbara.

Please see the comments below regarding the supplementary images. 

We did not observe huge variations in the cell morphology. Morphologies, in most cases, were restricted to spherical cells with intracellular vesicles or filamentous extensions. Regarding the sizes of the cells, we see some variations. However, we are reluctant to provide exact numbers. We have presented our reasons above.

We respectfully disagree with the reviewer’s comments. We see quite some similarities between Dresser formation microfossils and our cells. Not just the similarities, we have provided step-by-step transformation of cells that resulted in these morphologies. We fail to see what exactly is the speculation here. The argument that they should be classified as abiotic structures is based on the opinion that cells do form such structures. We clearly show here that they can, and these biological structures resemble Dresser formation microfossils more closely than the abiotic structures. 

Regarding the figures S3-S14. We think they are morphologically very similar. Often, it's not just comparing both images or making exact reproductions (which is not possible). We should focus on reproducing the distinctive morphological features of these microfossils.  

We agree with the reviewer that we did not reproduce all the structures reported by Wacey’s original manuscript, such as spherical structures. We are currently preparing another manuscript to address the filamentous microfossils. These spindle-like structures will be addressed in this subsequent work. 

We agree with the reviewer, we often have difficulties differentiating between cells and vesicles. This is not a problem in the early stages of growth. During the log phase, a significant volume of the cell consists of the cytoplasm, with hollow vesicles constituting only a minor volume (Fig. 1B or S1A). During the later growth stages (Fig. 1E7F or S11), cells were almost hollow, with numerous daughter cells within them. These cells often resemble hollow vesicles rather than cells. However, given these are biologically formed structures, and one could argue that these vesicles are still alive as there is still a minimal amount of cytoplasm (Fig. S27). Hence, we should consider them as cells until they break apart to release daughter cells. 

Regarding Figures S59 and S60, we did not claim either of these microfossils is from Pilbara Iron Formations. The legend of Figure S59 clearly states that these structures are from Buck Reef Chert, originally reported by Tice et al., 2006 (Figure 16 in the original manuscript). The legend of Figure S60 says these structures were originally reported by Barlow et al., 2018, from the Turee Creek Formation. 

Line 546f and 552: The sites including microfossils in the Archean represent different paleoenvironments ranging from marine to terrestrial to lacustrine. References 6 and 66 are well-developed studies focusing on specific stratigraphic successions, but cannot include information covering other Archean worlds of the over 2.5 Ga years Archean time.  

All the Archaean microfossils reported to date are from volcanic coastal marine environments. We are aware that there are rocky terrestrial environments, but no microfossils have been reported from these sites. We are unaware of any Archaean microfossils reported from freshwater environments. 

Line 570ff: The statements may represent a hypothesis, but the data presented are too preliminary to substantiate the assumptions.

We believe this is a correct inference from an evolutionary, genomic, and now from a morphological perspective. 

Figures:  

Please check all text and supplementary figures, whether scale bars are of different styles within the figure (minor quibble). 

S3 (no scale in C, D); S4, S5: Note that scale bars are of different styles. 

We believe we addressed this issue above. 

S6 D: depressions here are well visible - perhaps exchange with a photo in the main text? Note that scale bars are of different styles.  

We agree that depressions are well visible in E. The same image of EM-P cell in E is also present in Fig. 1D in the main text.   

S7: Scale bars should all be of the same style, if anyhow possible. Scale in D? 

We believe we addressed this issue above. 

S9: F appears to be distorted. Is the fossil like this? The figure would need additional indicators (arrows) pointing toward what the reader needs to see - not clear in this version. More explanation in the figure caption could be offered. 

We rechecked the figure from the original publication to check if by mistake the figure was distorted during the assembly of this image. We can assure you that this is not the case. We are not sure what further could be said in the figure legend.     

S13: What is shown in the inserts of D and E that is also visible in A and B? Here a sketch of the steps would help. 

We did not understand the question.  

S14: Scale in A, B? 

We believe we addressed this issue above. 

S15: Scales in A, E, C, D 

We believe we addressed this issue above. 

S16: scales in D, E, G, H, I, J?  

We believe we addressed this issue above. 

S17: "I" appears squeezed, is that so? If morphology is an important message, perhaps reduce the entire figure so it fits the layout. Note that labels A, B, C, and D are displaced. 

As shown in several subsequent figures, the hollow spherical vesicles are compressed first into honeycomb-like structures, and they often undergo further compression to form lamination-like structures. Such images often give the impression that the entire figure is squashed, but this is not the case. If one examines the figure closely, you could see perfectly spherical vesicles together with laterally sqeezed structures. Regarding the figure labels, we addressed this issue above. 

S18: The filamentous feature in C could also be the grain boundaries of the crystals. Can this be excluded as an interpretation? Are there microfossils with the cell membranes? That would be an excellent contribution to this figure. Note that scale bars are of different styles.

If this is a one-off observation, we could have arrived at the reviewer's opinion. But spherical cells in a “string of beads” configuration were frequently reported from several sites, to be discounted as mere interpretation.    

S19: The morphologies in A - insert appear to be similar to E - insert in the lower left corner. The chain of cells in A may look similar to the morphologies in E - insert upper right of the image. B - what is to see here? D - the inclusions do not appear spherical (?). Does C look similar to the cluster with the arrow in the lower part of image E? Note that scale bars are of different styles (minor quibble). A, B, C, and D appear compressed. Perhaps reduce the size of the overall image?  

The structures highlighted (yellow box) in C are similar to the highlighted regions in E—the agglomeration of hollow vesicles. It is hard to get understand this similarity in one figure. The similarities are apparent when one sees the Movie 4 and Fig. S12, clearly showing the spherical daughter cells within the hollow vesicle. We now added the movie reference to the figure legend.    

S20: A appears not to contribute much. The lineations in B appear to be diagenetic. However, C is suitable. Perhaps use only C, D, E? 

We believe too many unrecognizable structures are being labeled as diagenetic. Nevertheless, we do not subscribe to the notion that these are too lenient interpretations. These interpretations are justified as such structures have not been reported from live cells. This is the first study to report that cells could form such structures. As we now reproduced these structures, an alternate interpretation that these are organic structures derived from microfossils should be entertained. 

S 21: Note that scale bars are of different styles.  

We believe we addressed this issue above. 

S22: Perhaps add an arrow in F, where the cell opened, and add "see arrow" in the caption? Is this the same situation as shown in C (white arrow)? What is shown by the white arrow in A? Note that scale bars are of different styles.

We did the necessary changes.  

S23: In the caption and main text, please replace "&" with "and" (please check also the other figure captions, e.g. S24). Note that scale bars are of different styles. What is shown in F? A, D - what is shown here?

We replaced “&” with “and.”  

S24: Note that scale bars are of different styles. Note that Wacey et al. describe the vesicles as abiotic not as "microfossils"; please correct in figure caption [same also S26; 25; 28].

We are aware of Prof. Dr. Wacey’s interpretations. We discuss it at length in the discussion section our manuscript. Based on the similarities between the Dresser formation structures and structures formed by EM-P, we contest that these are abiotic structures.  

S25: Appears compressed; note different scale bars. 

We believe we addressed this issue above. 

S28: The label in B is still in the upper right corner; scale in D? What is to see in rectangles (blue and red) in A, B? In fossil material, this could be anything. 

These figures are taken from a previous manuscript cited in the figure legend. We could not erase or modify these figures.  

S33: "L"ewis; G appears a bit too diffuse - erase? Note that scale bars are of different styles.

We believe we addressed this issue above. 

S34: This figure appears unconvincing. Erase? 

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we can address his reservations.    

S35: It would be more convincing to show only the morphological similarities between the cell clusters. B and C are too blurry to distinguish much. Scales in D to F and in sketches? A appears compressed (?). 

We rechecked the original manuscript to see if image A was distorted while making this figure, but this is not the case. Regarding B & C, cells in this image are faint as they are hollow vesicles and, by nature, do not generate too much contrast when imaged with a phase-contrast microscope. There are some limitations on how much we can improve the contrast. We now added scale bars for D-I. Similarly, faint hollow vesicles can be seen in Fig. S21 C & D, and Fig. 3H.  

S36: Very nice; in B no purple arrow is visible. Note that scale bars are of different styles. S37 and S36 are very much the same - fuse, perhaps?  

We are sorry for the confusion. There are purple arrows in Fig. S37B-D. 

S38: this is a more unconvincing figure - erase? 

Unconvincing in wahy sense. There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we can address his reservations.

S39: white rectangle in A? Arrow in A? Note that scale bars are of different styles.

These are some of the unavoidable remnants from the image from the original publication. 

S40: in F: CM, V = ?; Note that scale bars are of different style. 

It’s an oversite on our part. We now added the definitions to the figure legaend. We thank the reviewer for pointing it out.  

S41: Rectangles in D, E, F, G can be deleted? Scales and labels missing in photos lower right. 

Those rectangles are added by the image processing software to the 3Drendered images. Regarding the missing scale bars in H & I they are the magnified regions of F. The scale bar is already present in F.   

S42: appears compressed. G could be trimmed. Labels too small; scale in G? 

This is a curled-up folded membrane. We needed to lower the resolution of some images to restrict the size of the supplement to journal size restrictions. It is not possible to present 85 figures in high resolution. But we assure you that the image is not laterally compressed in any manner.   

S43: This figure appears to be unconvincing. Reducing to pairing B, C, D with L, K? Spherical inclusions in B? Scales in E to G? Similar in S44: A, B, E only? Note that scale bars are of different styles. 

Figures I to K are important. They show not just the morphological similarities but also the sequence of steps through which such structures are formed. We addressed the issue of the scale bars above.  

S45: A, B, and C appear to show live or subrecent material. How was this isolated of a rock? Note that scale bars are of different styles.  

It is common to treat rocks with acids to dissolve them and then retrieve organic structures within them. This technique is becoming increasingly common. The procedure is quite extensively discussed in the original manuscript. We don’t see much differences in the scale bars of microfossils and EM-P cells, they are quite similar. 

S46: A: what is to see here? Note that scale bars are of different styles. 

There are considerable similarities between the folded fabric like organic structures with spherical inclusions and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we can address his reservations.    

S47: Perhaps enlarge B and erase A. Note that scale bars are of different styles. 

S48: Image B appears to show the fossil material - is the figure caption inconsistent? There are no aggregations visible in the boxes in A. H is described in the figure caption but missing in the figure. Overall, F and G do not appear to mirror anything in A to E (which may be fossil material?). 

S51; S52 B, C, E; S53: these figures appear unconvincing - erase? 

Unconvincing in what sense? The structures from our study are very similar to the microfossils.   

S54: North "Pole; scale bars in A to C =? 

These figures were borrowed from an earlier publication referenced in the figure legend. That is the reason for the differences in the styles of scale bars.  

S55: D and E appear not to contribute anything. Perhaps add arrow(s) and more explanation? Check the spelling in the caption, please. 

D & E show morphological similarities between cells from our study and microfossils (A).   

S56: Hexagonal morphologies may also be a consequence of diagenesis. Overall, perhaps erase this figure?  

I certainly agree that could be one of the reasons for the hexagonal morphologies. Such geometric polygonal morphologies have not been observed in living organisms. Nevertheless, as you can see from the figure, such morphologies could also be formed by living organisms. Hence, this alternate interpretation should not be discounted.   

S57: The figure caption needs improvement. Please add more description. What show arrows in A, what are the numbers in A? What is the relation between the image attached to the right side of A? Is this a close-up? Note that scale bars are of different styles. 

We expanded a bit on our original description of the figure. However, we request the reviewer to keep in mind that the parts of the figure are taken from previous publication. We are not at liberty to modifiy them, like removing the arrows. This imposes some constrains. 

S58: There are no honeycomb-shaped features visible. What is to see here? Erase this figure? 

Clearly, one can see spherical and polygonal shapes within the Archaean organic structures and mat-like structures formed by EM-P.  

S59 and S60: What is to see here? - Erase? 

Clearly, one can see spherical and polygonal shapes within the Archaean organic structures and mat-like structures formed by EM-P in Fig. S59. Further disintegration of these honeycomb shaped mats into filamentous struructures with spherical cells attached to them can be seen in both Archaean organic structures and structures formed by EM-P.   

S61: This figure appears to be unconvincing. B and F may be a good pairing. Note that scale bars are of different styles.  

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we might be able to address his reservations.     

S62: This figure appears to be unconvincing - erase?

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we might be able to address his reservations.     

S66: This figure is unconvincing - erase? 

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we might be able to address his reservations.    

S68: Scale in B, D, and E? 

Image B is just a magnified image of a small portion of image A. Hence, there is no need for an additional scale bar. The same is true for images D and E. 

S69: This figure appears to be unconvincing, at least the fossil part. Filamentous features are visible in fossil material as well, but nothing else. 

We are not sure what filamentous features the reviewer is referring to. Both the figures show morphologically similar spherical cells covered in membrane debris.    

S70 [as well as S82]: Good thinking here, but scales differ by magnitudes (cm to μm). Erase this figure? Very similar to Figure S73: Insert in C has which scale in comparison to B? Note that scale bars are of different styles.  

We realize the scale bars are of different sizes. In our defense, our experiments are conducted in 1ml volume chamber slides. We don’t have the luxury of doing these experiments on a scale similar to the natural environments. The size differences are to be expected. 

S71: Scale in E? 

Image E is just a magnified image of a small portion of image D. Hence, we believe a scale bar is unnecessary. 

S72: Scale in insert?  

The insert is just a magnified region of A & C

S75: This figure appears to be unconvincing. This is clastic sediment, not chert. Lenticular gaps would collapse during burial by subsequent sediment. - Erase? 

Regarding the similarities, we see similar lenticular gaps within the parallel layers of organic carbon in both microfossils, and structures formed by EM-P.

S76: A, C, D do not look similar to B - erase? Similar to S79, also with respect to the differences in scale. Erase? 

Regarding the similarities, we see similar lenticular gaps within the parallel layers of organic carbon in both microfossils, and structures formed by EM-P. We believe we addressed the issue of scale bars above. 

S80: A appears to be diagenetic, not primary. Erase? 

These two structures share too many resemblances to ignore or discount just as diagenic structures - Raised filamentous structures originate out of parallel layers of organic carbon (laminations), with spherical cells within this filamentous organic carbon.  

S85: What role would diagenesis play here? This figure appears unconvincing. Erase?

We do believe that diagenesis plays a major role in microfossil preservation. However, we also do not suscribe to the notion that we should by default assign diagenesis to all microfossil features. Our study shows that there could be an alternate explanation to some of the observations.  

S86 and S87: These appear unconvincing. What is to see here? Erase? 

The morphological similarities between these two structures. Stellarshaped organic structures with strings of spherical daughter cells growing out of them.  

S88: Does this image suggest the preservation of "salt" in organic material once preserved in chert?  

That is one inference we conclude from this observation. Crystaline NaCl was previously reported from within the microfossil cells.    

S89: What is to see here? Spherical phenomena in different materials? 

At present, the presence of honeycomb-like structures is often considered to have been an indication of volcanic pumice. We meant to show that biofilms of living organisms could result in honeycomb-shaped patterns similar to volcanic pumice.

References 

Please check the spelling in the references. 

We found a few references that required corrention. We now rectified them. 

References  

(1) Orange F, Westall F, Disnar JR, Prieur D, Bienvenu N, Le Romancer M, et al. Experimental silicification of the extremophilic archaea pyrococcus abyssi and methanocaldococcus jannaschii: Applications in the search for evidence of life in early earth and extraterrestrial rocks. Geobiology. 2009;7(4). 

(2) Orange F, Disnar JR, Westall F, Prieur D, Baillif P. Metal cation binding by the hyperthermophilic microorganism, Archaea Methanocaldococcus Jannaschii, and its effects on silicification. Palaeontology. 2011;54(5). 

(3) Errington J. L-form bacteria, cell walls and the origins of life. Open Biol. 2013;3(1):120143. 

(4) Cooper S. Distinguishing between linear and exponential cell growth during the division cycle: Single-cell studies, cell-culture studies, and the object of cell-cycle research. Theor Biol Med Model. 2006; 

(5) Mitchison JM. Single cell studies of the cell cycle and some models. Theor Biol Med Model. 2005; 

(6) Kærn M, Elston TC, Blake WJ, Collins JJ. Stochasticity in gene expression: From theories to phenotypes. Nat Rev Genet. 2005; 

(7) Elowitz MB, Levine AJ, Siggia ED, Swain PS. Stochastic gene expression in a single cell. Science. 2002; 

(8) Strovas TJ, Sauter LM, Guo X, Lidstrom ME. Cell-to-cell heterogeneity in growth rate and gene expression in Methylobacterium extorquens AM1. J Bacteriol. 2007; 

(9) Knoll AH, Barghoorn ES. Archean microfossils showing cell division from the Swaziland System of South Africa. Science. 1977;198(4315):396–8. 

(10) Sugitani K, Grey K, Allwood A, Nagaoka T, Mimura K, Minami M, et al. Diverse microstructures from Archaean chert from the Mount Goldsworthy–Mount Grant area, Pilbara Craton, Western Australia: microfossils, dubiofossils, or pseudofossils? Precambrian Res. 2007;158(3–4):228–62. 

(11) Kanaparthi D, Lampe M, Krohn JH, Zhu B, Hildebrand F, Boesen T, et al. The reproduction process of Gram-positive protocells. Sci Rep. 2024 Mar 25;14(1):7075.

Author response:

We genuinely appreciate the reviewer critiques of our submitted paper, “Otoacoustic emissions but not behavioral measurements predict cochlear-nerve frequency tuning in an avian vocal-communication specialist.” We are planning a number of changes based on the reviewers’ helpful comments that we feel will substantially improve the manuscript and clarify its implications.

We will add more support for the claim that budgerigars show unusual patterns of behavioral frequency tuning compared to other species. The original manuscript relied on previously published studies of budgerigar critical bands and psychophysical tuning curve to make this point (e.g., Fig. 1). Critical bands and psychophysical tuning curves have unfortunately not been studied in many bird species. Consequently, it was somewhat unclear (based on the information originally presented) whether the “unusual” behavioral tuning results shown in Fig. 1 reflect a hearing specialization in budgerigars or perhaps simply a general avian pattern attributable to declining audibility above 3-4 kHz (a point raised by both reviewers). Fortunately, behavioral critical-ratio results are available from a broader range of species. Albeit a less direct correlate of tuning, the results clearly highlight the unique hearing abilities of budgerigars in relation to other bird species as elaborated upon below.

The critical ratio is the threshold signal-to-noise ratio for tone detection in wideband noise and partly depends on peripheral tuning bandwidth. Critical ratios have been studied in over a dozen bird species, the vast majority of which show similar thresholds to one another and monotonically increasing critical ratios for higher frequencies (by 2-3 dB/octave, similar to most mammals; reviewed by Dooling et al., 2000). By contrast, budgerigar critical ratios diverge markedly from other species at mid-to-high frequencies, with ~8 dB lower (more sensitive) thresholds from 3-4 kHz (Dooling & Saunders, 1975; Okanoya & Dooling, 1987; Farabaugh 1988; see Figs 5 & 6 in Okanoya & Dooling, 1987). The unusual critical-ratio function in budgerigars is not attributable to the audiogram and was hypothesized by Okanoya and Dooling (1987) to reflect specialized cochlear tuning or perhaps central processing mechanisms. A brief discussion of these studies will be added to the introduction, along with a new figure panel (for Fig. 1) illustrating these intriguing species differences in critical ratios.

Another question was raised as to whether the simultaneous-masking paradigms and classic methods used to estimate behavioral tuning in budgerigars should be considered as valid, given newer forward-masking and notched-noise alternatives. We will expand the discussion of this issue in the revised manuscript. First, many of the methods from the classic budgerigar studies remain widely used in animal behavioral research (e.g., critical bands and ratios: Yost & Shofner, 2009; King et al., 2015; simultaneous masking: Burton et al., 2018). We therefore believe that it remains highly relevant to test and report whether these methods can accurately predict cochlear tuning. While forward-masking behavioral results are hypothesized to more accurately predict cochlear tuning humans (Shera et al., 2002; Joris et al., 2011; Sumner et al., 2018), evidence from nonhumans is controversial, with one study showing a closer match of forward-masking results to auditory-nerve tuning (ferret: Sumner et al., 2018), but several others showing a close match for simultaneous masking results (e.g., guinea pig, chinchilla, macaque; reviewed by Ruggero & Temchin, 2005; see Joris et al., 2011 for macaque auditory-nerve tuning). Moreover, forward- and simultaneous-masking results can often be equated with a simple scaling factor (e.g., Sumner et al., 2018). Given no real consensus on an optimal behavioral method, and seemingly limited potential for the “wrong” method to fundamentally transform the shape of the behavioral tuning quality function, it seems reasonable to accept previously published behavioral tuning estimates as essentially valid while also discussing limitations and remaining open to alternative interpretations.

We will add clarification throughout the revision as to the specific behavioral measures used to quantify tuning in budgerigars (i.e., critical bands, psychophysical tuning curve, and critical ratios). This avoids potentially disparaging alternative behavioral methods that have not been tested. That the budgerigar behavioral data are “old” seems not particularly relevant considering that the methods are still used in animal behavioral research as noted previously. Rather, it seems important to clarify the specific behavioral techniques used to estimate budgerigar’s frequency tuning in the revised paper.

Finally, we plan to add discussion of the apical-basal transition from the mammalian otoacoustic-emission literature, as suggested by reviewer 1, including how this concept might apply in budgerigars and other birds.

References not already cited in the preprint:

Burton JA, Dylla ME, Ramachandran R. Frequency selectivity in macaque monkeys measured using a notched-noise method. Hear Res. 2018 Jan;357:73-80. doi: 10.1016/j.heares.2017.11.012.

King J, Insanally M, Jin M, Martins AR, D'amour JA, Froemke RC. Rodent auditory perception: Critical band limitations and plasticity. Neuroscience. 2015 Jun 18;296:55-65. doi: 10.1016/j.neuroscience.2015.03.053.

Yost WA, Shofner WP. Critical bands and critical ratios in animal psychoacoustics: an example using chinchilla data. J Acoust Soc Am. 2009 Jan;125(1):315-23. doi: 10.1121/1.3037232. PMID: 19173418; PMCID: PMC2719489.

Author response:

(1) We do not know that the mechanism mediating the behavioral changes observed involves acetylcholine at all. (Reviewer 1)

The reviewer rightly pointed out the co-release of acetylcholine (ACh) and GABA from cholinergic terminals. We believe that the detected behavioral changes are because of the augmentation of this innate mixed chemical signal. We agree that identifying the receptor specificity is an essential next step; however, addressing this point requires a currently unavailable research tool to block cholinergic receptors for a few hundred milliseconds. This temporal specificity is vital because acetylcholine is released in the medial prefrontal cortex (mPFC) on two distinct timescales, the slow release over tens of minutes from the task onset and the fast release time-locked to salient stimuli (TelesGrilo Ruivo et al., 2017). Moreover, the former slow signal is far more robust than the latter phasic signal. The pharmacological experiments suggested by the reviewer will suppress both the tonic and phasic signals, making it difficult to interpret the results. Given the rapid technological advancement in this field, we hope to investigate the underlying mechanisms in detail in the future. 

(2) It is unclear whether mPFC cells are signaling predictions versus prediction errors. (Reviewer 2)

As the reviewer pointed out, mPFC cells signal the prediction of imminent outcomes (Baeg et al., 2001; Mulder et al., 2003; Takehara-Nishiuchi and McNaughton, 2008; Kyriazi et al., 2020).

However, the key difference between prediction signals and prediction error signals is their time course. The prediction signals begin to arise before the actual outcome occurs, whereas the prediction error signals are emitted after subjects experience the presence or absence of the expected outcome. In all our analyses, cell activity was normalized by the activity during the 1-second window before the threat site entry (i.e., the reveal of actual outcome; Lines 655-659). Also, all the statistical comparisons were made on the normalized activity during the 500-msec window, starting from the threat site entry (Lines 669670). Because this approach isolated the change in cell activity after the actual outcome, we interpret the data in Figure 4C as prediction error signals. 

(3) The task does not fully dissociate place field coding. (Reviewer 2)

The present analysis included several strategies to dissociate outcome selectivity from location selectivity (Figure 4). First, we collapsed cell activity on two threat sites to suppress the difference in cell activity between the sites. Second, our analysis compared how cell activity at the same location differed depending on whether outcomes were expected or surprising (Figure 4C). Nevertheless, we can use the present data to investigate the spatial tuning of mPFC cells. Indeed, an earlier version of this manuscript included some characterizations of spatial tuning. However, these data were deemed irrelevant and distracting when this manuscript was reviewed for publication in a different journal. As such, these data were removed from the current version. We are in the process of publishing another paper focusing on the spatial tuning of mPFC cells and their learning-dependent changes. 

(4) The basic effects of cholinergic terminal stimulation on mPFC cell activity are unclear. (Reviewers 1, 3)

We acknowledge the lack of characterization of the optogenetic manipulation of cholinergic terminals on mPFC cell activity outside the task context. As outlined in the discussion section (Lines 309-321), cholinergic modulation of mPFC cell activity is highly complex and most likely varies depending on behavioral states. In addition, because we intended to augment naturally occurring threatevoked cholinergic terminal responses (Tu et al., 2022), our optogenetic stimulation parameters were 3-5 times weaker than those used to evoke behavioral changes solely by the optogenetic stimulation of cholinergic terminals (Gritton et al., 2016). Based on these points, we validated the optogenetic stimulation based on its effects on air-puff-evoked cell activity during the task (Figure 2C, 2D). 

(5) Some choices of statistical analyses are questionable (Reviewers 1, 3)

We used the Kolmogorov-Smirnov (KS) test to investigate whether the distribution of cell responses differed between the two groups (Figure 2D) or changed with learning (Figure 3Ac, 3Bc). As seen in Figure 3Aa, some mPFC cells increased calcium activity in response to air-puffs, while others decreased. We expected that the manipulation or learning would alter these responses. If they are strengthened, the increased responses will become more positive, while the decreased responses will become more negative. If they are weakened, both responses will become closer to 0. Under such conditions, the shape of the distribution of cell response will change but not the median. The KS test can detect this, but not other tests sensitive to the difference in medians, such as Wilcoxon rank-sum tests. In Figure 2D, KS tests were applied to the independently sampled data from the control and ChrimsonRexpressing mice. In Figure 3Ac and 3Bc, we used all cells imaged in the first and fifth sessions. Considering that ~50% of them were longitudinally registered on both days, we acknowledge the violation in the assumption of independent sampling. In Figure 1D, we detected significant interaction between the group and sessions. Several approaches are appropriate to demonstrate the source of this interaction. We chose to conduct one-way ANOVA separately in each group to demonstrate the significant change in % adaptive choice across the sessions in the control group but not the ChrimsonR group. The cutoff for significance was adjusted with the Bonferroni correction in follow-up paired t-tests used in Figure 1F.

Author response:

Reviewer #1 (Public review):

This manuscript presents an interesting exploration of the potential activation mechanisms of DLK following axonal injury. While the experiments are beautifully conducted and the data are solid, I feel that there is insufficient evidence to fully support the conclusions made by the authors.

In this manuscript, the authors exclusively use the puc-lacZ reporter to determine the activation of DLK. This reporter has been shown to be induced when DLK is activated. However, there is insufficient evidence to confirm that the absence of reporter activation necessarily indicates that DLK is inactive. As with many MAP kinase pathways, the DLK pathway can be locally or globally activated in neurons, and the level of DLK activation may depend on the strength of the stimulation. This reporter might only reflect strong DLK activation and may not be turned on if DLK is weakly activated. The results presented in this manuscript support this interpretation. Strong stimulation, such as axotomy of all synaptic branches, caused robust DLK activation, as indicated by puc-lacZ expression. In contrast, weak stimulation, such as axotomy of some synaptic branches, resulted in weaker DLK activation, which did not induce the puc-lacZ reporter. This suggests that the strength of DLK activation depends on the severity of the injury rather than the presence of intact synapses. Given that this is a central conclusion of the study, it may be worthwhile to confirm this further. Alternatively, the authors may consider refining their conclusion to better align with the evidence presented.

We wish to further clarify a striking aspect of puc-lacZ induction following injury: it is bimodal. It is either induced (in various injuries that remove all synaptic boutons), or not induced, including in injuries that spared only 1-2 remaining boutons. This was particularly evident for injuries that spared the NMJ on muscle 29, which is comprised of only a few boutons. In some instances, only a single bouton was evident on muscle 29. While our injuries varied enormously in the number of branches and boutons that were lost, we did not see a comparable variability in puc-lacZ induction.  In the revision we will include additional images to better demonstrate this observation.

The reviewer (and others) fairly point out that our current study focuses on puc-lacZ as a reporter of Wnd signaling in the cell body. We consider this to be a downstream integration of events in axons that are more challenging to detect. It is striking that this integration appears strongly sensitized to the presence of spared synaptic boutons. Examination of Wnd’s activation in axons and synapses is a goal for our future work.

As noted by the authors, DLK has been implicated in both axon regeneration and degeneration. Following axotomy, DLK activation can lead to the degeneration of distal axons, where synapses are located. This raises an important question: how is DLK activated in distal axons? The authors might consider discussing the significance of this "synapse connection-dependent" DLK activation in the broader context of DLK function and activation mechanisms.

While it has been noted that inhibition of DLK can mildly delay Wallerian degeneration (Miller et al., 2009), this does not appear to be the case for retinal ganglion cell axons following optic nerve crush (Fernandes et al., 2014). It is also not the case for Drosophila motoneurons and NMJ terminals following peripheral nerve injury (Xiong et al., 2012; Xiong and Collins, 2012). Instead, overexpression of Wnd or activation of Wnd by a conditioning injury leads to an opposite phenotype - an increase in resiliency to Wallerian degeneration for axons that have been previously injured (Xiong et al., 2012; Xiong and Collins, 2012). The downstream outcome of Wnd activation is highly dependent on the context; it may be an integration of the outcomes of local Wnd/DLK activation in axons with downstream consequences of nuclear/cell body signaling.  The current study suggests some rules for the cell body signaling, however, how Wnd is regulated at synapses and why it promotes degeneration in some circumstances but not others are important future questions.

For the reviewer’s suggestion, it is interesting to consider DLK’s potential contributions to the loss of NMJ synapses in a mouse model of ALS (Le Pichon et al., 2017; Wlaschin et al., 2023). Our findings suggest that the synaptic terminal is an important locus of DLK regulation, while dysfunction of NMJ terminals is an important feature of the ‘dying back’ hypothesis of disease etiology (Dadon-Nachum et al., 2011; Verma et al., 2022). We propose that the regulation of DLK at synaptic terminals is an important area for future study, and may reveal how DLK might be modulated to curtail disease progression. Of note, DLK inhibitors are in clinical trials (Katz et al., 2022; Le et al., 2023; Siu et al., 2018), but at least some have been paused due to safety concerns (Katz et al., 2022). Further understanding of the mechanisms that regulate DLK are needed to understand whether and how DLK and its downstream signaling can be tuned for therapeutic benefit.

Reviewer #2 (Public review):

Summary:

The authors study a panel of sparsely labeled neuronal lines in Drosophila that each form multiple synapses. Critically, each axonal branch can be injured without affecting the others, allowing the authors to differentiate between injuries that affect all axonal branches versus those that do not, creating spared branches. Axonal injuries are known to cause Wnd (mammalian DLK)-dependent retrograde signals to the cell body, culminating in a transcriptional response. This work identifies a fascinating new phenomenon that this injury response is not all-or-none. If even a single branch remains uninjured, the injury signal is not activated in the cell body. The authors rule out that this could be due to changes in the abundance of Wnd (perhaps if incrementally activated at each injured branch) by Wnd, Hiw's known negative regulator. Thus there is both a yet-undiscovered mechanism to regulate Wnd signaling, and more broadly a mechanism by which the neuron can integrate the degree of injury it has sustained. It will now be important to tease apart the mechanism(s) of this fascinating phenomenon. But even absent a clear mechanism, this is a new biology that will inform the interpretation of injury signaling studies across species.

Strengths:

(1) A conceptually beautiful series of experiments that reveal a fascinating new phenomenon is described, with clear implications (as the authors discuss in their Discussion) for injury signaling in mammals.

(2) Suggests a new mode of Wnd regulation, independent of Hiw.

Weaknesses:

(1) The use of a somatic transcriptional reporter for Wnd activity is powerful, however, the reporter indicates whether the transcriptional response was activated, not whether the injury signal was received. It remains possible that Wnd is still activated in the case of a spared branch, but that this activation is either local within the axons (impossible to determine in the absence of a local reporter) or that the retrograde signal was indeed generated but it was somehow insufficient to activate transcription when it entered the cell body. This is more of a mechanistic detail and should not detract from the overall importance of the study

We agree. The puc-lacZ reporter tells us about signaling in the cell body, but whether and how Wnd is regulated in axons and synaptic branches, which we think occurs upstream of the cell body response, remains to be addressed in future studies.

(2) That the protective effect of a spared branch is independent of Hiw, the known negative regulator of Wnd, is fascinating. But this leaves open a key question: what is the signal?

This is indeed an important future question, and would still be a question even if Hiw were part of the protective mechanism by the spared synaptic branch. Our current hypothesis (outlined in Figure 4) is that regulation of Wnd is tied to the retrograde trafficking of a signaling organelle in axons. The Hiw-independent regulation complements other observations in the literature that multiple pathways regulate Wnd/DLK (Collins et al., 2006; Feoktistov and Herman, 2016; Klinedinst et al., 2013; Li et al., 2017; Russo and DiAntonio, 2019; Valakh et al., 2013). It is logical for this critical stress response pathway to have multiple modes of regulation that may act in parallel to tune and restrain its activation.

Reviewer #3 (Public review):

Summary:

This manuscript seeks to understand how nerve injury-induced signaling to the nucleus is influenced, and it establishes a new location where these principles can be studied. By identifying and mapping specific bifurcated neuronal innervations in the Drosophila larvae, and using laser axotomy to localize the injury, the authors find that sparing a branch of a complex muscular innervation is enough to impair Wallenda-puc (analogous to DLK-JNK-cJun) signaling that is known to promote regeneration. It is only when all connections to the target are disconnected that cJun-transcriptional activation occurs.

Overall, this is a thorough and well-performed investigation of the mechanism of spared-branch influence on axon injury signaling. The findings on control of wnd are important because this is a very widely used injury signaling pathway across species and injury models. The authors present detailed and carefully executed experiments to support their conclusions. Their effort to identify the control mechanism is admirable and will be of aid to the field as they continue to try to understand how to promote better regeneration of axons.

Strengths:

The paper does a very comprehensive job of investigating this phenomenon at multiple locations and through both pinpoint laser injury as well as larger crush models. They identify a non-hiw based restraint mechanism of the wnd-puc signaling axis that presumably originates from the spared terminal. They also present a large list of tests they performed to identify the actual restraint mechanism from the spared branch, which has ruled out many of the most likely explanations. This is an extremely important set of information to report, to guide future investigators in this and other model organisms on mechanisms by which regeneration signaling is controlled (or not).

Weaknesses:

The weakest data presented by this manuscript is the study of the actual amounts of Wallenda protein in the axon. The authors argue that increased Wnd protein is being anterogradely delivered from the soma, but no support for this is given. Whether this change is due to transcription/translation, protein stability, transport, or other means is not investigated in this work. However, because this point is not central to the arguments in the paper, it is only a minor critique.

We agree and are glad that the reviewer considers this a minor critique; this is an area for future study. In Supplemental Figure 1 we present differences in the levels of an ectopically expressed GFP-Wnd-kinase-dead transgene, which is strikingly increased in axons that have received a full but not partial axotomy. We suspect this accumulation occurs downstream of the cell body response because of the timing. We observed the accumulations after 24 hours (Figure S1F) but not at early (1-4 hour) time points following axotomy (data not shown). Further study of the local regulation of Wnd protein and its kinase activity in axons is an important future direction.

As far as the scope of impact: because the conclusions of the paper are focused on a single (albeit well-validated) reporter in different types of motor neurons, it is hard to determine whether the mechanism of spared branch inhibition of regeneration requires wnd-puc (DLK/cJun) signaling in all contexts (for example, sensory axons or interneurons). Is the nerve-muscle connection the rule or the exception in terms of regeneration program activation?

DLK signaling is strongly activated in DRG sensory neurons following peripheral nerve injury (Shin et al., 2012), despite the fact that sensory neurons have bifurcated axons and their projections in the dorsal spinal cord are not directly damaged by injuries to the peripheral nerve. Therefore it is unlikely that protection by a spared synapse is a universal rule for all neuron types. However the molecular mechanisms that underlie this regulation may indeed be shared across different types of neurons but utilized in different ways. For instance, nerve growth factor withdrawal can lead to activation of DLK (Ghosh et al., 2011), however neurotrophins and their receptors are regulated and implemented differently in different cell types. We suspect that the restraint of Wnd signaling by the spared synaptic branch shares a common underlying mechanism with the restraint of DLK signaling by neurotrophin signaling. Further elucidation of the molecular mechanism is an important next step towards addressing this question.

Because changes in puc-lacZ intensity are the major readout, it would be helpful to better explain the significance of the amount of puc-lacZ in the nucleus with respect to the activation of regeneration. Is it known that scaling up the amount of puc-lacZ transcription scales functional responses (regeneration or others)? The alternative would be that only a small amount of puc-lacZ is sufficient to efficiently induce relevant pathways (threshold response).

While induction of puc-lacZ expression correlates with Wnd-mediated phenotypes, including sprouting of injured axons (Xiong et al., 2010), protection from Wallerian degeneration (Xiong et al., 2012; Xiong and Collins, 2012) and synaptic overgrowth (Collins et al., 2006), we have not observed any correlation between the degree of puc-lacZ induction (eg modest, medium or high) and the phenotypic outcomes (sprouting, overgrowth, etc). Rather, there appears to be a striking all-or-none difference in whether puc-lacZ is induced or not induced. There may indeed be a threshold that can be restrained through multiple mechanisms. We posit in figure 4 that restraint may take place in the cell body, where it can be influenced by the spared bifurcation.

References Cited:

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Dadon-Nachum M, Melamed E, Offen D. 2011. The “dying-back” phenomenon of motor neurons in ALS. J Mol Neurosci 43:470–477.

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Fernandes KA, Harder JM, John SW, Shrager P, Libby RT. 2014. DLK-dependent signaling is important for somal but not axonal degeneration of retinal ganglion cells following axonal injury. Neurobiol Dis 69:108–116.

Ghosh AS, Wang B, Pozniak CD, Chen M, Watts RJ, Lewcock JW. 2011. DLK induces developmental neuronal degeneration via selective regulation of proapoptotic JNK activity. J Cell Biol 194:751–764.

Hao Y, Frey E, Yoon C, Wong H, Nestorovski D, Holzman LB, Giger RJ, DiAntonio A, Collins C. 2016. An evolutionarily conserved mechanism for cAMP elicited axonal regeneration involves direct activation of the dual leucine zipper kinase DLK. Elife 5. doi:10.7554/eLife.14048

Huntwork-Rodriguez S, Wang B, Watkins T, Ghosh AS, Pozniak CD, Bustos D, Newton K, Kirkpatrick DS, Lewcock JW. 2013. JNK-mediated phosphorylation of DLK suppresses its ubiquitination to promote neuronal apoptosis. J Cell Biol 202:747–763.

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Klinedinst S, Wang X, Xiong X, Haenfler JM, Collins CA. 2013. Independent pathways downstream of the Wnd/DLK MAPKKK regulate synaptic structure, axonal transport, and injury signaling. J Neurosci 33:12764–12778.

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Li J, Zhang YV, Asghari Adib E, Stanchev DT, Xiong X, Klinedinst S, Soppina P, Jahn TR, Hume RI, Rasse TM, Collins CA. 2017. Restraint of presynaptic protein levels by Wnd/DLK signaling mediates synaptic defects associated with the kinesin-3 motor Unc-104. Elife 6. doi:10.7554/eLife.24271

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Author response:

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

Reviewer 1:

We thank the reviewer for their comments and suggestions. We have made several edits to the paper to address these comments, including the addition of several new control experiments, corrections to mislabeled figures in Fig 2, and other additions to improve the clarity of several figures.

This work is missing several controls that are necessary to substantiate their claims. My most important concern is that the optogenetic screen for neurons that alter pathogenic lawn occupancy does not have an accompanying control on non-pathogenic OP50 bacteria. Hence, it remains unclear whether these neuronal inhibition experiments lead to pathogen-specific or generalized lawn-leaving alterations. For strains that show statistical differences between - and + ATR conditions, the authors should perform follow-up validation experiments on non-pathogenic OP50 lawns to ensure that the observed effect is PA14-specific. Similarly, neuronal inhibition experiments in Figures 5E and H are only performed with naïve animals on PA14 - we need to see the latency to re-entry on OP50 as well, to make general conclusions about these neurons' role in pathogen-specific avoidance.

We have added data from new control experiments to Fig. S1 (subfigures B, C) for both exit and re-entry dynamics on OP50. We find that inhibition of neurons produces different effects on both lawn entry and exit on PA14 compared to OP50. We observed that inhibition of neurons failed to change the re-entry dynamics for any of the lines which showed delayed latency to re-entry on PA14. Our results suggest that the neural control of re-entry dynamics we see are PA14 specific.

My second major concern is regarding the calcium imaging experiments of candidate neurons involved in lawn re-entry behavior. Although the data shows that AIY, AVK, and SIA/SIB neurons all show reduced activity following pathogen exposure, the authors do not relate these activity changes to changes in behavior. Given the well-established links between these cells and forward locomotion, it is essential to not only report differences in activity but also in the relationship between this activity and locomotory behavior. If animals are paused outside of the pathogen lawn, these neurons may show low activity simply because the animals are not moving forward. Other forward-modulated neurons may also show this pattern of reduced activity if the animals remain paused. Given that the authors have recorded neural activity before and after contact with pathogenic bacteria in freely moving animals, they should also provide an analysis of the relationship between proximity to the lawn and the activity of these neurons.

In response, we added an additional supplementary figure S7 to illustrate the role of each neuron in navigational control and added text to the discussion to better explain the role of each neuron type in the regulation of re-entry, in light of our previously published work on SIA in speed control.

This work is missing methodological descriptions that are necessary for the correct interpretation of the results shown here. Figure 2 suggests that the determination of statistical significance across the optogenetic inhibition screen will be found in the Methods, but this information is not to be found there. At various points in the text, authors refer to "exit rate", "rate constant", and "entry rate". These metrics seem derived from an averaged measurement across many individual animals in one lawn evacuation assay plate. However "latency to re-entry" is only defined on a per-animal basis in the lawn re-exposure assay. These differences should be clearly stated in the methods section to avoid confusion and to ensure that statistics are computed correctly.

Additional details have been added to the methods section to provide more in depth information on the statistical analysis performed. In brief, the latency to re-entry is calculated in the same way across all assays – re-entry events across replicate experiments for a given experimental condition are aggregated together and used to calculate relevant statistics.

This work also contains mislabeled graphs and incorrect correspondence with the text, which make it difficult to follow the authors 'claims. The text suggests that Pdop-2::Arch3 and Pmpz-1::Arch3 show increased exit rates, whereas Figure 2 shows that Pflp-4::Arch3 but not Pmpz-1::Arch3 has increased exit rate. The authors should also make a greater effort to correctly and clearly label which type of behavioral experiment is used to generate each figure and describe the differences in experimental design in the main text, figure legends, and methods. Figure 2E depicts trajectories of animals leaving a lawn over a 2.5-minute interval but it is unclear when this time window occurs within the 18-hour lawn leaving assay. Likewise, Figure 2H depicts a 30-minute time window which has an unclear relationship to the overall time course of lawn leaving. This figure legend is also mislabeled as "Infected/Healthy", whereas it should be labeled "-/+ ATR".

In Figures 2C and F, the x-axis labels are in a different order, making it difficult to compare between the 2 plots. Promoter names should be italicized. What does the red ring mean in Figure 2A? Figure 2 legend incorrectly states that four lines showed statistically significant changes for the Exist rate constant - only 2 lines are significant according to the figure.

We thank the reviewer for identifying this embarrassing error. Figure 2C and F were flipped, and we have corrected this, we are sorry for the error. Promoter names have been italicized, and we have added additional text in the captions that the red ring is a ring light for background illumination of the worms. In addition, we have corrected the error in the figure legends from “Infected/Healthy” to “+/- ATR”.

Lines in figure 2C and 2F are ordered by significance rather than keeping the same order in both. Majority feedback from colleagues suggested that this ordering was preferred.

This work raises the interesting possibility that different sets of neurons control lawn exit and lawn re-entry behaviors following pathogen exposure. However, the authors never directly test this claim. To rigorously show this, the authors would need to show that lawn-exit-promoting neurons (CEPs, HSNs, RIAs, RIDs, SIAs) are dispensable for lawn re-entry behavior and that lawn re-entry promoting neurons (AVK, SIA, AIY, MI) are dispensable for lawn exit behavior in pathogen-exposed animals.

We agree with the reviewer’s comments that there is insufficient evidence to show a complete decoupling of lawn exit and lawn re-entry. However, we note that our screen results show that only 1 line (dop-2) shows changes in both exit and re-entry dynamics upon neural inhibition (Fig. 2). This seems to suggest that at least some degree of neural control of re-entry is decoupled from exit.

Please label graph axes with units in Figure 1 - instead of "Exit Rate" make it #exits per worm per hour, and make it more clear that Figures 1C and E have a different kind of assay than Figures 1A, B and D. There should be more consistency between the meaning of "pre/post" and "naive/infected/healthy" - and how many hours constitutes post.

We have edited Figure 1 and made additions to the captions of figure 1 to make both points clearer. We have also standardized our language for subsequent figures (such as figure 5) to provide less ambiguity in pre/post and naïve/infected/healthy.

Figure 5 - it should be made more clear when the stimulation/inhibition occurred in these experiments and how long they were recorded/analyzed.

We have added additional details to the figure captions to make it clearer when the data was collected.

Workspaces and code have been added under a data availability section in the manuscript.

Reviewer 2:

However, the paper's main weakness lies in its lack of a detailed mechanism explaining how the delayed reentry process directly influences the actual locomotor output that results in avoidance. The term 'delayed reentry' is used as a dynamic metric for quantifying the screening, yet the causal link between this metric and the mechanistic output remains unclear. Despite this, the study is well-structured, with comprehensive control experiments, and is very well constructed.

We thank the reviewer for their comments and suggestions. We have added additional data and details to our work to cover these weaknesses, as can be seen in our responses to the suggestions below.

(1) A key issue in the manuscript is the mechanistic link between the delayed process and locomotor output. AIY is identified as a crucial neuron in this process, but the specifics of how AIY influences this delay are not clear. For instance, does AIY decrease the reversal rate, causing animals to get into long-range search when they leave the bacterial lawn? Is there any relationship between pdf-2 expression and reversal rates? Given that AIY typically promotes long-range motion when activated, the suppression of this function and its implications on motion warrants further clarification.

We have included additional data to explain how AIY might be able to regulate lawn entry behaviors and have added more to the discussion to explain how neural suppression might lead to changes in the behavior (new figure S7). Both AIY and SIA dynamics have been linked to worm navigation. In previous work (Lee 2019), we have demonstrated that SIA can control locomotory speed. Inhibition of SIA decreases locomotory speed, and as a result may serve to drive the increased latency of re-entry.

AIY’s role in navigation has been previously established (Zhaoyu 2014), but we have added an additional supplementary figure and edited our discussion to further illustrate this point. As can be seen in the new figure S7, AIY neural activity undergoes a transition after removal from a bacterial lawn, going from low activity to high activity. This activity increase is correlated with a transition from a high reversal rate local search state to a long range search state characterized by longer runs. Inhibition of AIY during this long range search state increased the reversal rate resulting in a higher rate of re-orientations. This might serve as a part of the mechanistic explanation for AIY’s role in preventing lawn re-entry, as inhibition dramatically increased the rate of re-orientation, preventing worms from making directed runs into the bacterial lawn. However, there is an additional effect of the inhibition of AIY, not seen during food search. Inhibition of AIY in the context of a pathogenic bacterial lawn leads to stalling at the edge. Therefore, re-entry AIY could have an additional role in governing the animals movement, post exposure, upon contact with a pathogenic lawn.

(2) I recommend including supplementary videos to visually demonstrate the process. These videos might help others identify aspects of the mechanism that are currently missing or unclear in the text.

(4) The authors mention that the worms "left the lawn," but the images suggest that the worms do not stray far and remain around the perimeter. Providing videos could help clarify this observation and strengthen the argument by visually connecting these points

Additional supplementary videos (1-3) taken at several stages of lawn evacuation have been added to visually demonstrate the process.

(3) Regarding the control experiments (Figure 1E-G), the manuscript describes testing animals picked from a PA14-seeded plate and retesting them on different plates. It's crucial to clarify the differences between these plates. Specifically, the region just outside the lawn should be considered, as it is not empty and worms can spread bacteria around. Testing animals on a new plate with a pristine proximity region might introduce variables that affect their behavior.

We have reworded the paper to make it clearer that these new conditions on a fresh PA14 lawn represent a different type of assay from the lawn evacuation assay. Fresh PA14 plates will indeed have a pristine proximity region compared to plates where the worms have spread the bacteria.

These experiments were done to test if the evacuation effect is purely due to aversive signals left on the lawn or attractive signals left outside of the lawn. Given that worms are known to be able to leave compounds such as ascarosides to communicate with each other, we wanted to test that this lawn re-entry defect was not simply the result of deposited pheromones. Without any other method to remove such compounds, we relied on using fresh PA14 lawns instead to test this. We have updated the manuscript to clarify this point.

(5) The manuscript notes that the PA14 strain was grown without shaking. Typically, growing this strain without agitation leads to biofilm formation. Clarifying whether there is a link between biofilm formation and avoidance behavior would add depth to the understanding of the experimental conditions and their impact on the observed behaviors.

As the reviewer has noted, growth of PA14 without shaking might indeed lead to biofilm formation. This does represent a legitimate concern, as evidence from previous work has suggested that biofilm formation could be linked to pathogen avoidance as worms make use of mechanosensation to avoid pathogenic bacteria (Chang et al. 2011).  However, we do not observe substantial formation of biofilm in our cultured bacteria, likely since our growth time might be insufficient for sufficient biofilm formation to occur. We also note that our evacuation dynamics appear to be of similar timescale to results reported in previous work which used different growth conditions. As such, we believe that our growth conditions thus represent similar conditions as to those historically used in the lawn evacuation literature.

Reviewer 3:

Weaknesses:

My only concern is that the authors should be more careful about describing their "compressed sensing-based approach". Authors often cite their previous Nature Methods paper, but should explain more because this method is critical for this manuscript. Also, this analysis is based on the hypothesis that only a small number of neurons are responsible for a given behavior. Authors should explain more about how to determine scarcity parameters, for example.

We have added more details to our paper outlining some of the details involved in our compressed sensing approach. We go into more detail about how we chose sparsity parameters and note that our discovered neurons for re-entry appear to be robust over choice of sparsity parameters. These additional details can be found in both the paper body and the methods section.

Line 45: This paragraph tries to mention that there should be "small sets of neurons" that can play key roles in integrating previous information to influence subsequent behavior. Is it valid as an assumption in the nervous systems?

We want to clarify that what is important is not that there are ‘small sets of neurons’, but rather that these key neurons make up a small fraction of the total number of neurons in the nervous system. More correctly: the compressed sensing approach identifies information bottlenecks in the neural circuits, and the assumption is that the number of neurons in these bottlenecks are small. This is the underlying sparsity assumption being made here that allows us to utilize a compressed sensing based approach to identify these neurons. We have reworded this section to make it clear that what is important is not that the total number of neurons is small, but that they must be a small fraction of the total number of neurons in the nervous system.

Line 125: "These approaches…" Authors repeatedly mentioned this statement to emphasize that their compressed sensing-based approach is the best choice. Are you really sure?

We agree that there are several approaches that might allow for faster screening of the nervous system. For example, many studies approach the problem by looking at neurons with synapses onto a neuron already known to be implicated in the behavior or find neurons that express a key gene known to regulate the behavior of interest. These approaches utilize prior information to greatly reduce the pool of candidate neurons needed to be screened.

In the absence of such prior information, we believe that our compressed sensing based approach allows a rapid way to perform an unbiased interrogation of the entire nervous system to identify key neurons at bottlenecks of neural circuits. Once these key neurons are identified, neurons upstream and downstream of these key neurons can be investigated in the future.  This approach gives us the added advantage of being able to identify neurons that do not connect to neurons that are already implicated in the behavior, or that don’t have clear genetic signatures in the behavior of interest. Our approach further allows for screening of neurons with no clear single genetic marker without the next to utilize intersectional genetic strategies.  We should not use the phrase “best choice” which might not be justified. We have reworded these statements, and we believe that compressed sensing based methods provide a complementary approach to those in the literature.

Line 42: If authors refer to mushroom bodies and human hippocampus in relation to the significance of their work, authors should go back to these references in the Discussion and explain how their work is important.

We thank the reviewer for this feedback, and we have added to our discussion to expand upon these points.

Line 151: "the accelerated pathogen avoidance" Accelerated pathogen avoidance does not necessarily indicate the existence of the neural mechanism that inhibits the association of pathogenicity with microbe-specific cues (during early stages: first two hours).

We agree with the reviewer’s statements that these results alone do not indicate the presence of an early avoidance mechanism. Other evidence for early avoidance mechanisms exists as seen in two choice assay experiments (Zhang 2005), and our results do seem to support this. However, we agree that early neural inhibition is insufficient evidence towards such a mechanism. We have thus removed this statement for accuracy.

Author response:

Reviewer #1 (Public review):

Summary:

In this manuscript by Lopez-Blanch and colleagues, 21 microexons are selected for a deep analysis of their impacts on behavior, development, and gene expression. The authors begin with a systematic analysis of microexon inclusion and conservation in zebrafish and use these data to select 21 microexons for further study. The behavioral, transcriptomic, and morphological data presented are for the most part convincing. Furthermore, the discussion of the potential explanations for the subtle impacts of individual microexon deletions versus loss-of-function in srrm3 and/or srrm4 is quite comprehensive and thoughtful. One major weakness: data presentation, methods, and jargon at times affect readability / might lead to overstated conclusions. However, overall this manuscript is well-written, easy to follow, and the results are of broad interest.

We thank the Reviewer for their positive comments on our manuscript. In the revised version, we will try to improve readability, reduce jargon and avoid overstatements. 

Strengths:

(1) The study uses a wide variety of techniques to assess the impacts of microexon deletion, ranging from assays of protein function to regulation of behavior and development.

(2) The authors provide comprehensive analyses of the molecular impact of their microexon deletions, including examining how host-gene and paralog expression is affected.

Weaknesses / Major Points:

(1) According to the methods, it seems that srrm3 social behavior is tested by pairing a 3mpf srrm3 mutant with a 30dpf srrm3 het. Is this correct? The methods seem to indicate that this decision was made to account for a slower growth rate of homozygous srrm3 mutant fish. However, the difference in age is potentially a major confound that could impact the way that srrm3 mutants interact with hets and the way that srrm3 mutants interact with one another (lower spread for the ratio of neighbour in front value, higher distance to neighbour value). This reviewer suggests testing het-het behavior at 3 months to provide age-matched comparisons for del-del, testing age-matched rather than size-matched het-del behavior, and also suggests mentioning this in the main text / within the figure itself so that readers are aware of the potential confound.

Thank you for bringing up this point. For the tests shown in Figure 5, we indeed decided to match the srrm3 pairs by fish size since we thought this would be more comparable to the other lines both biologically and methodologically (in terms of video tracking, etc.). However, we are confident the results would be very similar if matched by age, since the differences in social interactions between the srrm3 homozygous mutants and their control siblings are very dramatic at any age. For example, this can be appreciated, in line with the Reviewer's suggestion, in Videos S2 and S3, which show groups of five 5 mpf fish that are either srrm3 mutants or controls. It can be observed that the behavior of 5 mpf control fish is very similar to those of 1 mpf fish pairs, with very small interindividual distances. We will nonetheless agree that this decision on the experimental design should be clearly stated in the text and figure legend and we will do so in the revised version.

(2) Referring to srrm3+/+; srrm4-/- controls for double mutant behavior as "WT for simplicity" is somewhat misleading. Why do the authors not refer to these as srrm4 single mutants?

We thought it made the interpretation of plots easier, but we will change this in the revised version.

(3) It's not completely clear how "neurally regulated" microexons are defined / how they are different from "neural microexons"? Are these terms interchangeable?

Yes, they are interchangeable. We will double check the wording to avoid confusion.

(4) Overexpression experiments driving srrm3 / srrm4 in HEK293 cells are not described in the methods.

Apologies for this omission. We will briefly described the methods; however, please note that the data was obtained from a previous publication (Torres-Mendez et al, 2019), where the detailed methodology is reported.

(5) Suggest including more information on how neurite length was calculated. In representative images, it appears difficult to determine which neurites arise from which soma, as they cross extensively. How was this addressed in the quantification?

We will add further details to the revised version. With regards to the specific question, we would like to mention that this has not been a very common problem for the time points used in the manuscript (10 hap and 24 hap). At those stages, it was nearly always evident how to track each individual neurite. Dubious cases were simply discarded. Of course, such cases become much more common at later time points (48 and 72 hap), not sure in this study.

Reviewer #2 (Public review):

Summary:

This manuscript explores in zebrafish the impact of genetic manipulation of individual microexons and two regulators of microexon inclusion (Srrm3 and Srrm4). The authors compare molecular, anatomical, and behavioral phenotypes in larvae and juvenile fish. The authors test the hypothesis that phenotypes resulting from Srrm3 and 4 mutations might in part be attributable to individual microexon deletions in target genes.

The authors uncover substantial alterations in in vitro neurite growth, locomotion, and social behavior in Srrm mutants but not any of the individual microexon deletion mutants. The individual mutations are accompanied by broader transcript level changes which may resemble compensatory changes. Ultimately, the authors conclude that the severe Srrm3/4 phenotypes result from additive and/or synergistic effects due to the de-regulation of multiple microexons.

Strengths:

The work is carefully planned, well-described, and beautifully displayed in clear, intuitive figures. The overall scope is extensive with a large number of individual mutant strains examined. The analysis bridges from molecular to anatomical and behavioral read-outs. Analysis appears rigorous and most conclusions are well-supported by the data.

Overall, addressing the function of microexons in an in vivo system is an important and timely question.

Weaknesses:

The main weakness of the work is the interpretation of the social behavior phenotypes in the Srrm mutants. It is difficult to conclude that the mutations indeed impact social behavior rather than sensory processing and/or vision which precipitates apparent social alterations as a secondary consequence. Interpreting the phenotypes as "autism-like" is not supported by the data presented.

The Reviewer is absolutely right and we apologize for this omission, since it was not our intention to imply that these social defects should be interpreted simply as autistic-like. It is indeed very likely that the main reason for the social alterations displayed by the srrm3's mutants are due to their impaired vision. We will add this discussion explicitly in the revised version. 

Reviewer #3 (Public review):

Summary:

Microexons are highly conserved alternative splice variants, the individual functions of which have thus far remained mostly elusive. The inclusion of microexons in mature mRNAs increases during development, specifically in neural tissues, and is regulated by SRRM proteins. Investigation of individual microexon function is a vital avenue of research since microexon inclusion is disrupted in diseases like autism. This study provides one of the first rigorous screens (using zebrafish larvae) of the functions of individual microexons in neurodevelopment and behavioural control. The authors precisely excise 21 microexons from the genome of zebrafish using CRISPR-Cas9 and assay the downstream impacts on neurite outgrowth, larvae motility, and sociality. A small number of mild phenotypes were observed, which contrasts with the more dramatic phenotypes observed when microexon master regulators SRRM3/4 are disrupted. Importantly, this study attempts to address the reasons why mild/few phenotypes are observed and identify transcriptomic changes in microexon mutants that suggest potential compensatory gene regulatory mechanisms.

Strengths:

(1) The manuscript is well written with excellent presentation of the data in the figures.

(2) The experimental design is rigorous and explained in sufficient detail.

(3) The identification of a potential microexon compensatory mechanism by transcriptional alterations represents a valued attempt to begin to explain complex genetic interactions.

(4) Overall this is a study with a robust experimental design that addresses a gap in knowledge of the role of microexons in neurodevelopment.

Thank you very much for your positive comments to our manuscript.