Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This manuscript by Bai et al concerns the expression of Scleraxis (Scx) by muscle satellite cells (SCs) and the role of that gene in regenerative myogenesis. The authors report the expression of this gene associated with tendon development in satellite cells. Genetic deletion of Scx in SCs impairs muscle regeneration, and the authors provide evidence that SCs deficient in Scx are impaired in terms of population growth and cellular differentiation. Overall, this report provides evidence of the role of this gene, unexpectedly, in SC function and adult regenerative myogenesis.

We appreciate the comments and thank her/him for the support.

There are a few minor points of concern.

(1) From the data in Figure 1, it appears that all of the SCs, assessed both in vitro and in vivo, express Scx. The authors refer to a scRNA-seq dataset from their lab and one report from mdx mouse muscle that also reveals this unexpected gene expression pattern. Has this been observed in many other scRNA-seq datasets? If not, it would be important to discuss potential explanations as to why this has not been reported previously.

Thanks for this question regarding data in Fig.1. We did initially use immunofluorescence staining of Pax7 and GFP on muscle sections and primary myoblast cultures prepared from Tg-ScxGFP mice to conclude that Scx was expressed in satellite cells (SCs). In addition to the cited mdx RNA-seq data, we have included a re-analysis of a published scRNA-seq data set in Fig.2E (Dell'Orso et al., Development, 2019), and our own scRNA-seq data (Fig.S5D, F). We have now re-examined an additional scRNA-seq data set of TA muscles at various regeneration time points (De Micheli et al., Cell Rep. 2020), in which Scx expression was detected in MuSC progenitors and mature muscle cells. We have added the De Micheli et al. reference and the re-analysis of that scRNA-seq data set for Scx expression as an additional panel in Fig. 2E, with accompanying text (p. 7, ln. 4-6). Thus, our immunostaining results are consistent with scRNA-seq data from our and two other independent scRNA-seq data sets.

We think that Scx expression in the adult myogenic lineage was not previously reported mainly because its expression level was low, and might be dismissed as spurious detection. Additionally, detecting such low expression levels requires sophisticated detection methods with high capture efficiency. Previous studies have noted limitations in transcript capture or transcription factor dropout in 10x Genomics-based datasets (Lambert et al., Cell, 2018; Pokhilko et al., Genome Res., 2021). The most likely and straightforward reason is that Scx was simply not a focus in prior studies amid so many other genes of interest. We have now added this last explanation in the text (p.7, ln. 8-9), following the re-analyses of Scx expression in published scRNA-seq data sets.

(2) A major point of the paper, as illustrated in Fig. 3, is that Scx-neg SCs fail to produce normal myofibers and renewed SCs following injury/regeneration. They mention in the text that there was no increased PCD by Caspase staining at 5 DPI. A failure of cell survival during the process of SC activation, proliferation, and cell fate determination (differentiation versus self-renewal) would explain most of the in vivo data. As such, this conclusion would seem to warrant a more detailed analysis in terms of at least one or two other time points and an independent method for detecting dead/dying cells (the in vitro data in Fig. 4F is also based on an assessment of activated Caspase to assess cell death). The in vitro data presented later in Fig. S4G, H do suggest an increase in cell loss during proliferative expansion of Scx-neg SCs. To what extent does cell loss (by whatever mechanism of cell death) explain both the in vivo findings of impaired regeneration and even the in vitro studies showing slower population expansion in the absence of Scx?

We appreciate these constructive suggestions. Based on the number of available control and cKO animals, we were limited to one additional time point at 3 dpi to assess PCD by TUNEL in vivo. We were disappointed again to find no appreciable levels of PCD at 3 dpi by TUNEL (new Fig.S4I), thus no quantifications were included. We also re-did the in vitro experiment using purified SCs and monitored PCD by staining for cleaved Caspase-3 using a validated tube of antibodies (positive staining after 6 h of treatment by 1 mM staurosporine of control and ScxcKO cells; included as new Fig. S4J and legend). We were pleased to find an increase of cleaved Caspase3 stained cells, i.e. PCD, of Scx-cKO SCs at day 4 in culture, compared to that of the control. We have now replaced the old Fig. 4F with new Fig.4F and 4G to document PCD. We also provided new text/legend for these new data (p.10. ln. 2-10; new legend for Fig. 4F and 4G).

(3) I'm not sure I understand the description of the data or the conclusions in the section titled "Basement membrane-myofiber interaction in control and Scx cKO mice". Is there something specific to the regeneration from Scx-neg myogenic progenitors, or would these findings be expected in any experimental condition in which myogenesis was significantly delayed, with much smaller fibers in the experimental group at 5 DPI?

We very much appreciate this comment. We agree that there is unlikely anything specific about the regeneration from Scx-negative myogenic progenitors. Unfilled or empty ghost fibers (basement membrane remnant) are expected due to small fiber and poor regeneration in the ScxcKO mice at 5 dpi. We have removed the subtitle and changed the content to an expected consequence rather than something special (p. 8, ln. 19-22).

(4) The data presented in Fig. 4B showing differences in the purity of SC populations isolated by FACS depending on the reporter used are interesting and important for the field. The authors offer the explanation of exosomal transfer of Tdt from SCs to non-SCs. The data are consistent with this explanation, but no data are presented to support this. Are there any other explanations that the authors have considered and that could be readily tested?

Thanks for highlighting this phenomenon. We struggled with the SC purity issue for a long time. The project started with using the R26RtdT reporter for tdT’s paraformaldehyde  resistant strong fluorescence (fixation) to aid visualization in vivo. Later, when we used the tdT signal to purify SCs by FACS, we found that only 80% sorted tdT+ cells are Pax7+. We then switched to the R26RYFP reporter, from which we achieved much higher purity (95%) of SCs (Pax7+) by FACS. As such, we also repeated and confirmed many in vivo experimental results using the R26RYFP reporter (included in the manuscript). Due to the low purity of tdT+SCs by FACS, we discontinued that mouse colony after we confirmed the superior utility of the R26RYFP reporter for SC isolation.

We sincerely apologize for not being able to conduct further testable experiments on this intriguing phenomenon. However, this issue has since been addressed and published by Murach et al., iScience, (2021). Like our experience, they found non-satellite mononuclear cells with tdT fluorescence after TMX treatment when SCs were isolated via FACS. To determine this was not due to off-target recombination or a technical artifact from tissue processing, they conducted extensive analyses. They found that the tdT+ mononuclear cells included fibrogenic cells (fibroblasts and FAPs), immune cells/macrophages, and endothelial cells. Additionally, they confirmed the significant potential of extracellular vesicle (EV)-mediated cargo transfer, which facilitates the transfer of full-length tdT transcript from lineage-marked Pax7+ cells to those mononuclear cells. We have modified the text to emphasize and acknowledge their contribution to this important point, and explained the difference between YFP and tdT reporter alleles in more detail (p.9, ln. 11-17).

(5) The Cut&Run data of Fig. 6 certainly provide evidence of direct Scx targets, especially since the authors used a novel knock-in strain for analyses. The enrichment of E-box motifs provides support for the 207 intersecting genes (scRNA-seq and Cut&Run) being direct targets. However, the rationale elaborated in the final paragraph of the Results section proposing how 4 of these genes account for the phenotypes on the Scx-neg cells and tissues is just speculation, however reasonable. These are not data, and these considerations would be more appropriate in the Discussion in the absence of any validation studies.

We agree with this comment and have moved speculations into the Discussion (p. 15, ln. 4-15, and from p. 18, ln. 4 to p. 19, ln. 4).

Reviewer #2 (Public Review):

Summary:

Scx is a well-established marker for tenocytes, but the expression in myogenic-lineage cells was unexplored. In this study, the authors performed lineage-trace and scRNA-seq analyses and demonstrated that Scx is expressed in activated SCs. Further, the authors showed that Scx is essential for muscle regeneration using conditional KO mice and identified the target genes of Scx in myogenic cells, which differ from those of tendons.

Strengths:

Sometimes, lineage-trace experiments cause mis-expression and do not reflect the endogenous expression of the target gene. In this study, the authors carefully analyzed the unexpected expression of Scx in myogenic cells using some mouse lines and scRNA-seq data.

We appreciate the comments and thank her/him for noting the strengths of our manuscript.

Weaknesses:

Scx protein expression has not been verified.

We are aware of this weakness. We had previously used Western blotting (WB) using cultured SCs from control and ScxcKO mice, but did not detect endogenous Scx protein even in the control. In response to this comment, we have re-done several WB experiments using new lysates from control and ScxcKO SCs and two commercial antibodies: anti-Scx antibody 1 from Abcam (ab58655) and anti-Scx antibody 2 from Invitrogen (PA5-23943). These antibodies have been reported to detect endogenous Scx protein in tendon cells in Spang et al., BMC Musculoskelet Disord (2016) and  Bochon et al., Int J Stem Cells (2021). Despite our best efforts, we were not able to detect a reliable Scx band. We have also conducted immunofluorescence using these two antibodies. Still, we failed to detect a difference of staining signals between control and cKO SCs using these antibodies. Lastly, we conducted immunofluorescence using the ScxTy1 myoblasts and we did not find the staining signal coinciding with the Ty1 signal (by double staining). We have been very frustrated by not knowing what caused this technical difficulty in our hands. Given that these were negative data, we did not include them. However, we do hope that the combined data from scRNA-seq, ScxCreERT2 lineage-tracing, Tg-ScxGFP expression, and ScxTy1 knock-in together are deemed sufficient to make up for the deficiency of data for endogenous Scx protein in regenerative myogenic cells.

Response to Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

p. 8: The text refers to Fig. 3I, but this should be Fig. 3H.

We apologize for the confusion. Please note that by keeping all 14 dpi data in the same row, we placed Fig.3I at an unconventional/unexpected position, i.e., next to 3D &3E, and above 3F-H. We were aware that this unconventional placement could cause confusion, and it did. With that said, we have now re-arranged the subfigures (same data content) so that the updated Fig.3 contains subfigures in the expected and proper spatial order. We double-checked the figure referral in the text (p. 8, ln. 16-17) and the text is correct – just that the original Fig.3I should have been at the original Fig.3H position and that is now corrected.

Reviewer #2 (Recommendations For The Authors):

(1) Given that Scx binds to the E-box and regulates gene expression, it is of interest to know the relevance between MyoD and Scx. If possible, the reviewer recommends to include some discussions.

Thanks for the comment. MyoD1 is a well-known transcript factor regulating myogenesis, whereas Scx is primarily studied in tenocytes and other connective tissues. We agree that our new findings deserve a discussion regarding the relevance between MyoD1 and Scx.  We have added a description of their differences in the discussion and two new references (p.19, ln. 7-17).

(2) Considering that Scx is a transcriptional factor, it is interesting that Scx-GFP was not detected in the nuclei of regenerated myofibers. Could the subcellular localization of Scx-GFP provide some insights into the function of Scx as a transcription factor during muscle regeneration?

Tg-ScxGFP is a transgenic line generated by random insertion into the genome (Pryce et al., 2007; cited). The plasmid used for transgenesis was constructed by replacing most of Scx’s first exon with GFP, and including ~ 9Kb flanking regulatory sequences. As such, the ScxGFP is not a fusion gene, but rather that the GFP expression is regulated by Scx promoter and enhancer(s). This GFP reporter lacks a nuclear localization signal (NLS), hence it is mainly detected in the cytoplasm; some nuclear signal is detected, presumably due to GFP’s small size permitting passive diffusion into the nucleus. Thus, the GFP signal is used as a reporter for Scx expression, but GFP subcellular localization does not provide insight into Scx function per se. Conversely, ScxTy1/Ty1 is a knock-in allele created by fusing a triple-Ty1 tag (3XTy1) to the C-terminus of Scx, and we observed that Ty1 is located in the nucleus by the immunofluorescent staining. We used the Ty1 epitope to carry out CUT&RUN experiments to gain insight to the function of Scx as a transcription factor.

(3) Fig1D The number of arrows in the Merge image is not matched with others. In addition, the star mark in the Pax7 image is likely an error.

Apologies. We have now corrected these errors in the revised Fig.1D.

(4) FigS1A Is there only one myofiber shown in the dashed line in this image? It is unclear why only this myofiber is surrounded by the dashed line.

The dashed line encircles a single fiber because it was not visible in the provided image. However, there are 3 fibers in this image. Because we did not immuno-stain for myofibers here, we circled one fiber for illustration. For clarity, we brightened the background (of the entire original images) so the background signals from myofiber boundaries are discernable without outlines.

(5) FigS1B There was no overlapped DAPI staining in the Myogenin+ cell. DAPI-staining should be present in Myogenin+ cells because myogenin is located in the nucleus.

Fig.S1B is immuno-staining for MyoD , and we marked one MyoD+DAPI+GFP+ cell/nucleus. Fig.S1C is immune-staining for Myogenin, and we also marked one (cell/nucleus) that is triple positive.

(6) The position of the asterisk for the ScxGFP in FigS1D is misaligned. In addition, the position is not matched with Fig1C. Because all myofibers are Scx-positive, it is strange that only one myofiber has an asterisk. The reviewer suggests removing the mark.

Thank you for pointing out these errors. We have now corrected the misalignment and removed the unnecessary asterisk.

Author response:

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

eLife Assessment 

This study presents valuable experimental and numerical results on the motility of a magnetotactic bacterium living in sedimentary environments, particularly in environments of varying magnetic field strengths. The evidence supporting the claims of the authors is solid, although the statistical significance comparing experiments with the numerical work is weak. The study will be of interest to biophysicists interested in bacterial motility. 

We thank the reviewers and editors for their careful reading and the constructive comments. With respect to the statement about weak statistical significance, we think that this statement mixes two separate issues, the significance of the difference between experiments at 0 and 50µT and the comparison of experiments with simulations. We have amended our manuscript to address both points as described below. The difference between the experiments at 0 and 50µT is indeed significant, and the discrepancy between experiments and simulations can be explained by unavoidable differences in the way we quantify bacterial throughput.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors present experimental and numerical results on the motility Magnetospirillum gryphiswaldense MSR-1, a magnetotactic bacterium living in sedimentary environments. The authors manufactured microfluidic chips containing three-dimensional obstacles of irregular shape, that match the statistical features of the grains observed in the sediment via microcomputer tomography. The bacteria are furthermore subject to an external magnetic field, whose intensity can be varied. The key quantity measured in the experiments is the throughput ratio, defined as the ratio between the number of bacteria that reach the end of the microfluidic channel and the number of bacteria entering it. The main result is that the throughput ratio is non-monotonic and exhibits a maximum at magnetic field strength comparable with Earth's magnetic field. The authors rationalize the throughput suppression at large magnetic fields by quantifying the number of bacteria trapped in corners between grains. 

Strengths: 

While magnetotactic bacteria's general motility in bulk has been characterized, we know much less about their dynamics in a realistic setting, such as a disordered porous material. The micro-computer tomography of sediments and their artificial reconstruction in a microfluidic channel is a powerful method that establishes the rigorous methodology of this work. This technique can give access to further characterization of microbial motility. The coupling of experiments and computer simulations lends considerable strength to the claims of the authors, because the model parameters (with one exception) are directly measured in the experiments. 

Weaknesses: 

The main weakness of the manuscript pertains to the discussion of the statistical significance of the experimental throughput ratio. Especially when comparing results at zero and 50 micro Tesla. The simulations seem to predict a stronger effect than seen in the experiments. The authors do not address this discrepancy. 

We thank the reviewer for their positive assessment and the detailed constructive remarks. 

The increase in bacterial throughput between 0 and 50 µT is indeed more pronounced in the simulations than in the experiments, partly due to the fact that there is considerably more variability in the experimental data. We did two things to address this issue: (1) We performed additional statistical test addressing the difference between the experimental results at 0 and 50 µT. Indeed, the difference is only weakly significant (in contrast to the difference of either to 500µT). The increase is however consistent with the observation in the absence of obstacles in the channel, where we see a monotonous increase from 0 to 500 µT (Supp. Figure S5). We have added the test results in the caption of Fig. 3. (2) To address the difference between simulations and experiments, we added a section in Methods on how we determine the throughput and a short discussion in the Results section. The key points are that the initial condition is different in simulations and experiments and that the throughput is therefore quantified differently. This difference is due to experimental limitations: we cannot track bacteria through the whole channel and we wanted to avoid pushing them into the channel with fluid flow to avoid effects of flow on the results. As a consequence, bacteria continue to enter the IN region of the channel from the inlet during the experiment, while in the simulation, they all start at the beginning of the channel simultaneously. We expect this to mostly affect the case with diffusive transport (B=0).

Reviewer #2 (Public Review): 

Summary: 

simulation study of magnetotactic bacteria in microfluidic channels containing sediment-mimicking obstacles. The obstacles were produced based on micro-computer tomography reconstructions of bacteria-rich sediment samples. The swimming of bacteria through these channels is found experimentally to display the highest throughput for physiological magnetic fields. Computer simulations of active Brownian particles, parameterized based on experimental trajectories are used to quantify the swimming throughput in detail. Similar behavior as in experiments is obtained, but also considerable variability between different channel geometries. Swimming at strong field is impeded by the trapping of bacteria in corners, while at weak fields the direction of motion is almost random. The trapping effect is confirmed in the experiments, as well as the escape of bacteria with reducing field strength. 

Strengths: 

This is a very careful and detailed study, which draws its main strength from the fruitful combination of the construction of novel microfluidic devices, their use in motility experiments, and simulations of active Brownian particles adapted to the experiment. Based on their results, the authors hypothesize that magnetotactic bacteria may have evolved to produce magnetic properties that are adapted to the geomagnetic field in order to balance movement and orientation in such crowded environments. They provide strong arguments in favor of such a hypothesis. 

Weaknesses: 

Some of the issues touched upon here have been studied also in other articles. It would be good to extend the list of references accordingly and discuss the relation briefly in the text. 

We thank the reviewer for the constructive comments. We answer to the point concerning previous literature in the response to the recommendations below.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Here follows a list of points the authors should address. 

(1) Are additional experiments feasible to decrease the statistical noise present in Fig. 3c? At the very least, the authors should discuss the statistical significance of the results at 50 muT vis-a-vis 0 T. 

See our response to Strengths/Weaknesses above

(2) The experimental setup is not immediately clear. I think that adding a panel from Fig. S1 (or a sketch thereof) would help clarify, especially in relation to the entry zone and end zone. 

We are not sure what you mean. Fig. 3A already contains exactly such a panel. We have however added another supplementary figure that shows an additional detailed view of the setup (Fig. S3). In addition, we revised several figures: We have replaced Fig. S1 with a better version and exchanged the schematic view of the obstacle channel in Fig 1, removing the additional inlets that were not used in this study (also in Fig 3A), Instead we added a comment in Methods explaining their presence. Hopefully this makes the setup clear.

(3) It should be also stated that there is no external flow imposed on the channel. 

We have added such a statement in the description of the experiment (in section 2.2 Swimming of magnetotactic bacteria through sediment-mimicking obstacle channels.  

(4) Fig. 3c and Fig. 6c are seemingly showing the same quantity (or closely related ones). The authors should use the same symbol and give an explicit mathematical definition. 

The two quantities are not exactly the same, as we cannot directly quantify the flux of bacteria through the channel in our experiments. On the one hand, we cannot track bacteria through the whole channel, on the other hand, the initial conditions are not exactly the same as in the simulations. In the simulations all bacteria start at the same time at the entrance to the channel. In the experiments, they enter from the inlet and do so at different times (pushing them in with fluid flow would be possible, but carries the risk of perturbing the results due to induced flow through the channel). We have added a new section in the Methods section that explains this difference and describes the procedure used to obtain the throughput from the experiments in detail. We have also added a corresponding comment in the Result section, where the simulations are compared with the experiments. 

Minor issues: 

- Figures have different styles that should be unified. For example, the panel labels sometimes have round brackets and sometimes they don't.

See above

- Page 6, (muCT) should have the Greek letter mu 

Thanks, corrected.

- Fig. 3a is not very clear; see my point 2 above. 

See above

Reviewer #2 (Recommendations For The Authors): 

I have only a few comments and questions, which the authors should address: 

(1) The observed exponential dependence of decay time on the "well" depth could be related to the exponential density distribution of active particles in a gravitational field, which has been derived previously. Might be interesting to discuss such a possible connection. 

Thank you for the suggestion, the two cases are indeed somewhat analogous with behaviors reminiscent of thermal processes with an effective temperature. Such a description is however not generally possible (even for sedimentation, only some features are described). We plan to address in future work whether it can be made more quantitative in our case of escape from the corner traps. We have included a short discussion of the analogy in the section on trapping and escape. 

(2) The authors should consider the following relevant references, and discuss them briefly in their manuscript:

- Sedimentation, trapping, and rectification of dilute bacteria J Tailleur, ME Cates EPL 86, 60002 (2009) 

- Human spermatozoa migration in microchannels reveals boundary-following navigation P Denissenko, V Kantsler, DJ Smith, J Kirkman-Brown Proc. Natl. Acad. Sci. USA 109, 8007-8010 (2012) 

- Wall accumulation of self-propelled spheres J Elgeti, G Gompper Europhysics Letters 101, 48003 (2013) 

- Wall entrapment of peritrichous bacteria: a mesoscale hydrodynamics simulation study SM Mousavi, G Gompper, RG Winkler Son Maber 16 (20), 4866-4875 (2020) 

- A Geometric Criterion for the Optimal Spreading of Active Polymers in Porous Media C Kurzthaler, S Mandal, T Bhabacharjee, H Löwen, SS Daba, HA Stone Nat. Commun. 12, 7088 (2021) 

- Run-to-Tumble Variability Controls the Surface Residence Times of E. coli Bacteria G Junot, T Darnige, A Lindner, VA Martinez, J Arlt, A Dawson, WCK Poon, H Auradou, E Clement Phys. Rev. Leb. 128, 248101 (2022) 

- Dynamics and phase separation of active Brownian particles on curved surfaces and in porous media P Iyer, RG Winkler, DA Fedosov, G Gompper Phys. Rev. Research 5, 033054 (2023) 

We agree that there is a lot of literature on these aspects, specifically interaction of self-propelled objects with walls and motion of swimmers through porous media. We have slightly extended our overview of previous literature in the introduction and included most of these references.

Author response:

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

Reviewer #1: 

(1) Their results with human macrophages suggest that there are differences between murine and human macrophages in inflammasome-mediated restriction of STm growth. For example, Thurston et al. showed that in murine macrophages that inflammasome activation controls the replication of mutant STm that aberrantly invades the cytosol, but only slightly limits replication of WT STm. In contrast, here the authors found that primed human macrophages rely on caspase-1, gasdermin D and ninjurin-1 to restrict WT STm. I wonder if the priming of the human macrophages in this study could account for the differences in these studies. Along those lines, do the authors see the same results presented in this study in the absence of priming the macrophages with Pam3CSK4. I think that determining whether the control of intracellular STm replication is dependent on priming is very important.

We thank the Reviewer for their careful attention to our manuscript and for their thoughtful comments. We have addressed this question about the impact of priming by repeating the bacterial intracellular burden assays in unprimed WT and CASP1-/- THP-1 cells. We have added additional figures to the manuscript to address this: Figure 1 – Figure Supplement 3. Under unprimed conditions, CASP1-/- cells still harbored significantly higher bacterial burdens at 6 hpi and a significant fold-increase in bacterial CFUs compared to WT cells. These results suggest that the caspase-1-mediated restriction of intracellular Salmonella replication in human macrophages is independent of priming. 

(2) Another difference with the Thurston et al. paper is the way that the STm inoculum was prepared - stationary phase bacteria that were opsonized. Could this also account for differences between the two studies rather than differences between murine and human macrophages in inflammasome-dependent control of STm?

We thank the Reviewer for this excellent suggestion. To address this possibility, we repeated the bacterial intracellular burden assays in WT and CASP1-/- THP-1 cells using stationary phase bacteria. We infected WT and CASP1-/- THP-1 cells with stationary phase Salmonella, and we subsequently assayed for intracellular bacterial burdens. These data have now been added to the manuscript in Figure 1 – Figure Supplement 4. Interestingly, we did not observe any fold-change in the bacterial colony forming units in both the WT and CASP1-/- THP-1 cells for the stationary phase Salmonella. These data indicate that by 6 hours postinfection, Salmonella do not replicate efficiently in human macrophages unless grown under SPI-1-inducing conditions. Furthermore, these results suggest that differences in how the Salmonella inoculum is prepared may contribute to the discrepancies between our study and previous studies, as noted by the Reviewer. 

(3) The authors show that the pore-forming proteins GSDMD and Ninj1 contribute to control of STm replication in human macrophages. Is it possible that leakage of gentamicin from the media contributes to this control?

Response: We thank the Reviewer for their insightful comment. We have addressed this question on the impact of gentamicin by repeating the bacterial intracellular burden assays using a lower concentration of gentamicin in combination with extensively washing the cells with RPMI media to remove the gentamicin. WT and CASP1-/- THP-1 cells were infected with WT Salmonella. Then, at 30 minutes post-infection, cells were treated with 25 μg/ml of gentamicin to kill any extracellular bacteria. At 1 hour post-infection (hpi), the cells were washed for a total of five times with fresh RPMI to remove the gentamicin, and then the media was replaced with fresh media containing no gentamicin. In parallel, we also treated cells with 100 μg/ml of gentamicin at 30 minutes post-infection, washed the cells five times with fresh RPMI at 1 hpi to remove the gentamicin, and then replaced the media with fresh media containing 10 μg/ml of gentamicin. This data has now been included in the manuscript as Figure 1 – Figure Supplement 5. We observed similar levels in the intracellular bacterial burdens at 1 hpi and 6 hpi and a fold-increase in bacterial colony forming units in CASP1-/- cells compared to WT cells across both gentamicin conditions, suggesting that gentamicin appears to not contribute to the intracellular control of Salmonella replication in human macrophages. Of note, we also tried repeating the bacterial intracellular burden assays without gentamicin, using only washes to remove extracellular at 1 hpi; however, under these experimental conditions, we observed high levels of extracellular Salmonella. Therefore, we relied on using a lower concentration of gentamicin to kill extracellular Salmonella in conjunction with extensive washing to remove the gentamicin for the remainder of the infection. 

(4) One major question that remains to be answered is whether casp-1 plays a direct role in the intracellular localization of STm. If the authors quantify the percentage of vacuolar vs. cytosolic bacteria at early time points in WT and casp-1 KO macrophages, would that be the same in the presence and absence of casp-1? If so, then this would suggest that there is a basal level of bacterial-dependent lysis of the SCV and in WT macrophages the presence of cytosolic PAMPS trigger cell death and bacteria can't replicate in the cytosol. However, in the inflammasome KO macrophages, the host cell remains alive and bacteria can replicate in the cytosol.

We thank this Reviewer for raising this important point. We have addressed this experimentally by quantifying the percentage of vacuolar vs. cytosolic Salmonella at 2 hpi in WT, NAIP-/-, and CASP1-/- THP-1 cells using a chloroquine (CHQ) resistance assay. This data has now been included in the manuscript in the new Figure 5A. The original subfigures of Figure 5 have consequently been rearranged. We did not observe any significant differences in vacuolar and cytosolic bacterial burdens at this early time point in WT, NAIP-/-, and CASP1-/- THP-1 cells. As noted by the Reviewer, these results suggest that the basal level of bacterialdependent lysis of the SCV in human macrophages is not dependent on caspase-1 or NAIP. 

Reviewer #3: 

(1) The main weaknesses of the study are the inherent limitations of tissue culture models. For example, to study interaction of Salmonella with host cells in vitro, it is necessary to kill extracellular bacteria using gentamicin. However, since Salmonella-induced macrophage cell death damages the cytosolic membrane, gentamicin can reach intracellular bacteria and contribute to changes in CFU observed in tissue culture models (major point 1). This can result in tissue culture "artefacts" (i.e., observations/conclusions that cannot be recapitulated in vivo). For example, intracellular replication of Salmonella in murine macrophages requires T3SS-2 in vitro, but T3SS-2 is dispensable for replication in macrophages of the spleen in vivo (Grant et al., 2012).  

We thank the Reviewer for their helpful comments and insightful suggestions. We have addressed some of the concerns about gentamicin in our response to Reviewer #1 above. To address the Reviewer’s concerns further, we have included language to acknowledge the limitations of our study based on the artefacts of tissue culture models in our Discussion section: “In this study, we utilized tissue culture models to examine intracellular Salmonella replication in human macrophages. These in vitro systems allow for precise control of experimental conditions and, therefore, serve as powerful tools to interrogate the molecular mechanisms underlying inflammasome responses and Salmonella replication in both immortalized and primary human cells. Still, there are limitations of tissue culture models, as they lack the inherent complexity of tissues and organs in vivo. To assess whether our findings reflect Salmonella dynamics in the mammalian host, it will be important to complement our studies and extend the implications of our work using approaches that model more complex systems, such as organoids or organ explant models co-cultured with immune cells, and in vivo techniques, such as humanized mouse models.”

(2) In Figure 1: are increased CFU in WT vs CASP1-deficient THP-1 cells due to Caspase 1 restricting intracellular replication or due to Caspase-1 causing pore formation to allow gentamicin to enter the cytosol thereby restricting bacterial replication? The same question arises about Caspase-4 in Figure 2, where differences in CFU are observed only at 24h when differences in cell death also become apparent. The idea that gentamicin entering the cytosol through pores is responsible for controlling intracellular Salmonella replication is also consistent with the finding that GSDMD-mediated pore formation is required for restricting intracellular Salmonella replication (Figure 3). Similarly, the finding that inflammasome responses primarily control Salmonella replication in the cytosol could be explained by an intact SCV membrane protecting Salmonella from gentamicin (Figure 5). 

We thank the Reviewer for highlighting this important point regarding gentamicin.

We have addressed this question in our response above to Review #1 and in Figure 1 – Figure Supplement 5. We observed caspase-1-mediated restriction of Salmonella in human macrophages even when cells were treated with a lower concentration of gentamicin (25 μg/ml) for 30 minutes and then extensively washed with RPMI media to remove any gentamicin for the remainder of the infection. These data suggest that gentamicin is likely not responsible for controlling intracellular Salmonella in human macrophages.

Author response:

We thank all three reviewers and the editors for their detailed comments on our manuscript.  The two main themes of this feedback concern the paper’s generality and its presentation.  Reviewers #2 and #3 raise questions about how the discrepancies in fitness statistics we report will be realized across organisms, environments, and in models with interactions beyond resource competition (e.g., toxicity or cross-feeding).  All reviewers and the editors have also expressed the need for the presentation to be improved, including a broader introduction to the concept of fitness (Reviewer #1), a clearer explanation of our model (Reviewer #1), better explanations of how quantifying fitness answers key biological questions (Reviewer #3), and improvements to the most technical sections to ensure accessibility to experimentalists (Reviewer #3).

In light of these comments, we wish to clarify that the goal of this paper is to provide a proof-of-principle for how different choices in quantifying fitness can lead to different analysis outcomes.  Since the focus of this paper is on the theoretical concepts, we focus on a few example data sets and a simple model to demonstrate the existence of these discrepancies.  While other organisms and environments, especially with more complex growth dynamics and interactions, could certainly have additional or different discrepancies in fitness statistics, we believe the simplicity of our approach is valuable because it demonstrates that even basic features of microbial growth (common across systems) with realistic parameter values are sufficient to cause significant differences in fitness depending on these quantification choices.  We agree with the reviewers that a systematic documentation of how these fitness discrepancies are empirically realized is important, but we believe that question is best explored in separate future works that can focus fully on this empirical rather than theoretical question.

We plan to revise the manuscript in several ways, following the suggestions of the three reviewers and the editor.  First, we will better articulate the main goal and conclusions of this manuscript, especially its generality and limitations.  Second, we will work to streamline and clarify several points in the main text identified by the reviewers to make it more accessible and useful to a broader audience, especially experimentalists who routinely measure fitness in their work.  We are grateful to the reviewers and the editor for their time and effort in assessing the manuscript, and we look forward to providing an updated version that addresses these concerns.

Author response:

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

Public Reviews:

Reviewer #1:

Summary:

Casas-Tinto et al. present convincing data that injury of the adult Drosophila CNS triggers transdifferentiation of glial cells and even the generation of neurons from glial cells. This observation opens up the possibility of getting a handle on the molecular basis of neuronal and glial generation in the vertebrate CNS after traumatic injury caused by Stroke or Crush injury. The authors use an array of sophisticated tools to follow the development of glial cells at the injury site in very young and mature adults. The results in mature adults revealing a remarkable plasticity in the fly CNS and dispels the notion that repair after injury may be only possible in nerve cords which are still developing. The observation of so-called VC cells which do not express the glial marker repo could point to the generation of neurons by former glial cells.

Conclusion:

The authors present an interesting story that is technically sound and could form the basis for an in-depth analysis of the molecular mechanism driving repair after brain injury in Drosophila and vertebrates.

Strengths:

The evidence for transdifferentiation of glial cells is convincing. In addition, the injury to the adult CNS shows an inherent plasticity of the mature ventral nerve cord which is unexpected.

Weaknesses:

Traumatic brain injury in Drosophila has been previously reported to trigger mitosis of glial cells and generation of neural stem cells in the larval CNS and the adult brain hemispheres. Therefore this report adds to but does not significantly change our current understanding. The origin and identity of VC cells is unclear.

The Reviewer correctly points out that it has been reported that traumatic brain injury trigger generation of neural stem cells. However, according to previous reports, those cells where quiescent Dpn+ neuroblast. We now report that already differentiated adult neuropil glia transdifferentiate into neurons. Which is a new mechanism not previously reported. 

We agree with the reviewer regarding the identity of VC neurons although according to the results of G-TRACE experiments the origin is clear, they originate from neuropil glia (i.e. Astrocyte-like glia and ensheathing glia). We have used a battery of antibodies previously reported to identify specific subtypes of neurons to identify these newly generated neurons (Figure S1). We did not find any other neuronal marker rather than Elav that co-localize with VC cells

Reviewer #2:

Summary:

Casas-Tinto et al., provide new insight into glial plasticity using a crush injury paradigm in the ventral nerve cord (VNC) of adult Drosophila. The authors find that both astrocyte-like glia (ALG) and ensheating glia (EG) divide under homeostatic conditions in the adult VNC and identify ALG as the glial population that specifically ramps up proliferation in response to injury, whereas the number of EGs decreases following the insult. Using lineagetracing tools, the authors interestingly observe the interconversion of glial subtypes, especially of EGs into ALGs, which occurs independent of injury and is dependent on the availability of the transcription factor Prospero in EGs, adding to the plasticity observed in the system. Finally, when tracing the progeny of differentiated glia, Casas-Tinto and colleagues detect cells of neuronal identity and provide evidence that such glia-derived neurogenesis is specifically favored following ventral nerve cord injury, which puts forward a remarkable way in which glia can respond to neuronal damage.

Numerous experiments have been carried out in 7-day-old flies, showing that the observed plasticity is not due to residual developmental remodeling or a still immature VNC.

By elegantly combining different genetic tools, the authors show glial divisions with mitotic-dependent tracing and find that the number of generated glia is refined by apoptosis later on.

The work identifies Prospero in glia as an important coordinator of glial cell fate, from development to the adult context, which draws further attention to the upstream regulatory mechanisms.

We express our gratitude to the reviewer for their keen appreciation of our efforts and their enthusiasm for the outcomes of this research.

Weaknesses:

Although the authors do use a variety of methods to show glial proliferation, the EdU data (Figure 1B) could be more informative (Figure 1B) by displaying images of non-injured animals and providing quantifications or the mention of these numbers based on results previously acquired in the system.

We appreciate the Reviewer’s comment. We believed that adding images of non-injured animals did not add new information as we already quantified the increase of glial proliferation upon injury in Losada-Perez let al. 2021. Besides, the purpose of this experiment was to figure out if dividing cells where Astrocyte-like glia rather than the number of dividing cells. Comparing independent experiments could be tricky but if we compare the quantifications of G2-M glia (repo>fly-Fucci) done in Losada-Perez et al 2021 (fig 1C) with the quantifications of G2-M neuropil glia done in this work (fig 1C) we can see that the numbers are comparable.

The experiments relying on the FUCCI cell cycle reporter suggested considerable baseline proliferation for EGs and ALGs, but when using an independent method (Twin Spot MARCM), mitotic marking was only detected for ALGs. This discrepancy could be addressed by assessing the co-localization of the different glia subsets using the identified driver lines with mitotic markers such as PH3.

In our understanding this discrepancy could be explained by the magnitude of proliferation. The lower proliferation rate of EG (as indicate the fly-fucci experiments) combining with the incomplete efficiency of MARCM clones induction reduces considerably the chances of finding EG MARCM clones. PH3 is a mitotic marker but it is also found in apoptotic cells (Kim and Park 2012. DOI: 10.1371/journal.pone.0044307) however, we stained injured VNCs with anti-Ph3 and found ALG cells positive for PH3 (Author response image 1).

Author response image 1.

The data in Figure 1C would be more convincing in combination with images of the FUCCI Reporter as it can provide further information on the location and proportion of glia that enter the cell cycle versus the fraction that remains quiescent.

We added a Figure 1 V2 (version 2) with the suggested images (1-C’).

The analyses of inter-glia conversion in Figure 3 are complicated by the fact that Prospero RNAi is both used to suppress EG - to ALG conversion and as a marker to establish ALG nature. Clarifications if the GFP+ cells still expressed Pros or were classified as NP-like GFP cells are required here.

As described in the text, Pros is a marker for ALG and the results suggest that Prospero expression is required for the EG to ALG transition. We clarified these concepts in the text accordingly. In figure 3 we showed images of NP-like cells originated from EG that are prospero+, and therefore supporting the transdifferentiation from EG to ALG.  

The conclusion that ALG and EG glial cells can give rise to cells of neuronal lineage is based on glial lineage information (GFP+ cells from glial G-trace) and staining for the neuronal marker Elav. The use of other neuronal markers apart from Elav or morphological features would provide a more compelling case that GFP+ cells are mature neurons.

We completely agree with the reviewer's observation regarding the identity of VC neurons. We have used a battery of antibodies previously reported to identify specific subtypes of neurons to identify these newly generated neurons (Figure S1). We did not find any other neuronal marker rather than Elav that colocalize with VC cells

Although the text discusses in which contexts, glial plasticity is observed or increased upon injury, the figures are less clear regarding this aspect. A more systematic comparison of injured VNCs versus homeostatic conditions, combined with clear labelling of the injury area would facilitate the understanding of the panels.

We appreciate the Reviewer’s observation. We have carefully checked all figures and labelled then as “Injured” or “Not Injured”. We added a Figure 2-V2 and a figure 4-V2.

Context/Discussion

The study finds that glia in the ventral cord of flies have latent neurogenic potential. Such observations have not been made regarding glia in the fly brain, where injury is reported to drive glial divisions or the proliferation of undifferentiated progenitor cells with neurogenic potential.

Discussing this different strategy for cell replacement adopted by glia in the VNC and pointing out differences to other modes seems fascinating. Highlighting differences in the reactiveness of glia in the VNC compared to the brain also seems highly relevant as they may point to different properties to repair damage.

Based on the assays employed, the study points to a significant amount of

glial "identity" changes or interconversions, which is surprising under homeostatic conditions. The significance of this "baseline" plasticity remains undiscussed, although glia unarguably show extensive adaptations during nervous system development.

It would be interesting to know if the "interconversion" of glia is determined by the needs in the tissue or would shift in the context of selective ablation/suppression of a glial type.

We deeply appreciate the Reviewer’s enthusiasm on this subject, it is indeed fascinating. We made a reduced discussion in order to fit in the eLife Short report requirements but the specific condition that trigger glial interconversion are of great interest for us. To compromise EG or ALG viability and evaluate the behaviour of glial cells is of great interest for developmental biology and regeneration, but the precise scenario to develop these experiments is not well defined. In this report, we aim to reproduce an injury in Drosophila brain and this model should serve to analyze cellular behaviours. The scenario where we deplete on specific subpopulation of glial cells is conceptually attractive, but far away from the scope of this report.

Reviewer #3:

In this manuscript, Casas-Tintó et al. explore the role of glial cells in the response to a neurodegenerative injury in the adult brain. They used Drosophila melanogaster as a model organism and found that glial cells are able to generate new neurons through the mechanism of transdifferentiation in response to injury.

This paper provides a new mechanism in regeneration and gives an understanding of the role of glial cells in the process.

Author response:

Reviewer #1 (Public review):

Li et al. investigate Ca2+ signaling in T. gondii and argue that Ca2+ tunnels through the ER to other organelles to fuel multiple aspects of T. gondii biology. They focus in particular on TgSERCA as the presumed primary mechanism for ER Ca2+ filling. Although, when TgSERCA was knocked out there was still a Ca2+ release in response to TG present.

Note that we did not knockout SERCA as it is an essential gene so it would not be possible to isolate parasites that do not express SERCA. We created conditional mutants that downregulate the expression of SERCA and some activity is present in the mutant after 24 h of ATc treatment.

Overall the Ca2+ signaling data do not support the conclusion of Ca2+ tunneling through the ER to other organelles in fact they argue for direct Ca2+ uptake from the cytosol.

The authors show EM membrane contact sites between the ER and other organelles, so Ca2+ released by the ER could presumably be taken up by other organelles but that is not ER Ca2+ tunneling.

They clearly show that SERCA is required for T. gondii function.

Overall, the data presented to not fully support the conclusions reached

We agree that the data does not support Ca2+ tunneling as defined and characterized in mammalian cells. In response to this comment, we modified the title and the text accordingly.

However, we think that the study shows far more than just the role of SERCA in T. gondii functions. We argue that the study shows that the ER (through the activity of the SERCA pump) sequesters and re-distributes calcium to other organelles following influx through the PM. The experiments show that the ER is able to take calcium from the cytosol as it enters the parasite through SERCA activity, and this activity is important for the transition of the parasite between various extracellular calcium exposures. We believe that the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium is demonstrated in the experiments shown in Figs 1H-I, 4G-H and 5G,H, I, J, K . There are no previous T. gondii studies that address the question of how intracellular stores are filled with calcium, which are essential for the continuation of the lytic cycle, meaning they are essential for the parasitism of T. gondii.

Data argue for direct Ca2+ uptake from the cytosol

The ER most likely takes up calcium from the cytosol following its entry through the PM and redistributes it to the other organelles. We will delete the word “tunneling” and replace it with transfer and re-distribution as they represent our results.

What we think is re-distribution is shown in Figure 1H and I in which the calcium released after GPN and nigericin are enhanced after TG addition. Of note is that there is no experimental evidence that supports the regulation of calcium entry by store depletion (PMID: 24867952), and we do not think that the enhanced response is due to calcium entry.

Figure 4G and H show that knocking down SERCA reduces significantly the response to GPN. Fig 5I shows that the mitochondrial calcium uptake is reduced after the addition of GPN in the knockdown mutant. Fig 2B shows that SERCA can take up calcium at 55 nM calcium while mitochondrial uptake needs higher concentrations (Fig 5B-C). However, higher calcium concentrations could be reached at the microdomains formed around MCS between the ER and mitochondrion. Figure 5E shows that the mitochondrion is not responsive to an increase of cytosolic calcium. This is also shown for the apicoplast in Fig. 7 E and F of the Li et al, Nat Commun 2021 paper.

Reviewer #2 (Public review):

The role of the endoplasmic reticulum (ER) calcium pump TgSERCA in sequestering and redistributing calcium to other intracellular organelles following influx at the plasma membrane.

T. gondii transitions through life cycle stages within and exterior to the host cells, with very different exposures to calcium, adds significance to the current investigation of the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium.

They also use a conditional knockout of TgSERCA to investigate its role in ER calcium store-filling and the ability of other subcellular organelles to sequester and release calcium. These knockout experiments provide important evidence that ER calcium uptake plays a significant role in maintaining the filling state of other intracellular compartments.

We thank the reviewer.

While it is clearly demonstrated, and not surprising, that the addition of 1.8 mM extracellular CaCl2 to intact T. gondii parasites preincubated with EGTA leads to an increase in cytosolic calcium and subsequent enhanced loading of the ER and other intracellular compartments, there is a caveat to the quantitation of these increases in calcium loading. The authors rely on the amplitude of cytosolic free calcium increases in response to thapsigargin, GPN, nigericin, and CCCP, all measured with fura2. This likely overestimates the changes in calcium pool sizes because the buffering of free calcium in the cytosol is nonlinear, and fura2 (with a Kd of 100-200 nM) is a substantial, if not predominant, cytosolic calcium buffer. Indeed, the increases in signal noise at higher cytosolic calcium levels (e.g. peak calcium in Figure 1C) are indicative of fura2 ratio calculations approaching saturation of the indicator dye.

We agree about the limitations of using Fura2 but according to the literature (PMID:3838314, fig. 3) Fura2 is suitable for measurements between 100 nM and 1 mM calcium.  The responses in our experiments were within its linear range and the experiments with the SERCA mutant and mitochondrial GCaMPs supports the conclusions of our work.

We agree that the experiment shown in Fig 1C shows a response close to the limit of the linear range of Fura2 and we can provide a more representative trace in the final article. We can include new quantifications and comparisons.

Another caveat, not addressed, is that loading of fura2/AM can result in compartmentalized fura2, which might modify free calcium levels and calcium storage capacity in intracellular organelles.

We are aware of this issue and because of that we have modified our protocol to minimize compartmentalization. We load cells for 26 min at room temperature and keep cells in ice and do not use them for longer that 2-3 hours because we do see evidence of compartmentalization. One evidence of compartmentalization is the increase in the resting calcium concentration.

The finding that the SERCA inhibitor cyclopiazonic acid (CPA) only mobilizes a fraction of the thapsigargin-sensitive calcium stores in T. gondii coincides with previously published work in another apicomplexan parasite, P. falciparum, showing that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools (Borges-Pereira et al., 2020, DOI: 10.1074/jbc.RA120.014906). It would be valuable to determine whether this reflects the off-target effects of thapsigargin or the differential sensitivity of TgSERCA to the two inhibitors.

This is an interesting observation, and we will discuss the result considering the Plasmodium study and include the citation. We will add inhibition curves using the MagFluo protocol and compare CPA and TG.

Figure S1 suggests differential sensitivity, and it shows that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools in T. gondii. Also important is that we used 1 µM TG as we are aware that TG has shown off-target effects at higher concentrations. 

The authors interpret the residual calcium mobilization response to Zaprinast observed after ATc knockdown of TgSERCA (Figures 4E, 4F) as indicative of a target calcium pool in addition to the ER. While this may well be correct, it appears from the description of this experiment that it was carried out using the same conditions as Figure 4A where TgSERCA activity was only reduced by about 50%.

We partially agree as pointed by the reviewer knock down of TgSERCA by only 50% means that the ER still could be targeted by zaprinast and no evidence of another target calcium pool. From the MagFLuo4 experiment (although we are aware that the fluorescence of mag Fluo4 is not linear to calcium), there is SERCA activity after 24 hr of ATc treatment.  However, when adding Zaprinast after TG we see a significant release of calcium which is true for both wild type and conditional knockdowns. Because of this result we proposed that there could be another large neutral calcium pool than the one mobilized by TG. We will address these possibilities in the discussion and interpretation of the result.

The data in Figures 4A vs 4G and Figures 4B vs 4H indicate that the size of the response to GPN is similar to that with thapsigargin in both the presence and absence of extracellular calcium. This raises the question of whether GPN is only releasing calcium from acidic compartments or whether it acts on the ER calcium stores, as previously suggested by Atakpa et al. 2019 DOI: 10.1242/jcs.223883. Nonetheless, Figure 1H shows that there is a robust calcium response to GPN after the addition of thapsigargin.

The results of the experiments did not exclude the possibility that GPN can also mobilize some calcium from the ER besides acidic organelles. We don’t have any evidence to support that GPN can mobilize calcium from the ER either. Based on our unpublished work, we think GPN mainly release calcium from the PLVAC. We will include the mentioned citation and discuss the result considering the possibility that GPN may be acting on the ER.

An important advance in the current work is the use of state-of-the-art approaches with targeted genetically encoded calcium indicators (GECIs) to monitor calcium in important subcellular compartments. The authors have previously done this with the apicoplast, but now add the mitochondria to their repertoire. Despite the absence of a canonical mitochondrial calcium uniporter (MCU) in the Toxoplasma genome, the authors demonstrate the ability of T. gondii mitochondrial to accumulate calcium, albeit at high calcium concentrations. Although the calcium concentrations here are higher than needed for mammalian mitochondrial calcium uptake, there too calcium uptake requires calcium levels higher than those typically attained in the bulk cytosolic compartment. And just like in mammalian mitochondria, the current work shows that ER calcium release can elicit mitochondrial calcium loading even when other sources of elevated cytosolic calcium are ineffective, suggesting a role for ER-mitochondrial membrane contact sites. With these new tools in hand, it will be of great value to elucidate the bioenergetics and transport pathways associated with mitochondrial calcium accumulation in T. gondii.

We thank this reviewer for his/her positive comment. Studies of bioenergetics and transport pathways associated with mitochondrial calcium accumulation is part of our future plans.

The current studies of calcium pools and their interactions with the ER and dependence on SERCA activity in T. gondi are complemented by super-resolution microscopy and electron microscopy that do indeed demonstrate the presence of close appositions between the ER and other organelles (see also videos). Thus, the work presented provides good evidence for the ER acting as the orchestrating organelle delivering calcium to other subcellular compartments through contact sites in T. gondi, as has become increasingly clear from work in other organisms.

Thank you

Reviewer #3 (Public review):

This manuscript describes an investigation of how intracellular calcium stores are regulated and provides evidence that is in line with the role of the SERCA-Ca2+-ATPase in this important homeostasis pathway. Calcium uptake by mitochondria is further investigated and the authors suggest that ER-mitochondria membrane contact sites may be involved in mediating this, as demonstrated in other organisms.

The significance of the findings is in shedding light on key elements within the mechanism of calcium storage and regulation/homeostasis in the medically important parasite Toxoplasma gondii whose ability to infect and cause disease critically relies on calcium signalling. An important strength is that despite its importance, calcium homeostasis in Toxoplasma is understudied and not well understood.

We agree with the reviewer. Thank you

A difficulty in the field, and a weakness of the work, is that following calcium in the cell is technically challenging and thus requires reliance on artificial conditions. In this context, the main weakness of the manuscript is the extrapolation of data. The language used could be more careful, especially considering that the way to measure the ER calcium is highly artificial - for example utilising permeabilization and over-loading the experiment with calcium. Measures are also indirect - for example, when the response to ionomycin treatment was not fully in line with the suggested model the authors hypothesise that the result is likely affected by other storage, but there is no direct support for that.

The MagFluo protocol has been amply used in mammalian cells, DT40 cells and other cells for the characterization of the IP3 receptor response to IP3. We will include and discuss more citations in the revised article. The scheme at the top of the figure shows the protocol used. There is no overloading with calcium because the cells are permeabilized and the concentrations of calcium used are physiological and all experiments were performed at 220 nm calcium which is within the cytosolic levels tolerated by cells. The experiment was done with permeabilized cells because permeabilization allows the indicator to become diluted, the substrate MgATP to reach the membrane of the ER and in addition allows for the exposure to precise concentrations of calcium. MagFluo4 loading is intended for its compartmentalization to all intracellular compartments and the uptake stimulated by MgATP exclusively occurs in the compartment occupied by SERCA. IO is an ionophore that causes calcium release from other stores in addition to the ER and it is expected that will result in a larger release. We must clarify that the experiment shown in Fig. 2 was done to characterize the activity of SERCA and was not aimed at the characterization of the role of SERCA in the parasite. We will explain this result better in the revised version of the article.

Below we provide some suggestions to improve controls, however, even with those included, we would still be in favour of revising the language and trying to avoid making strong and definitive conclusions. For example, in the discussion perhaps replace "showed" with "provide evidence that are consistent with..."; replace or remove words like "efficiently" and "impressive"; revise the definitive language used in the last few lines of the abstract (lines 13-17); etc. Importantly we recommend reconsidering whether the data is sufficiently direct and unambiguous to justify the model proposed in Figure 7 (we are in favour of removing this figure at this early point of our understanding of the calcium dynamic between organelles in Toxoplasma).

We thank the reviewer for the suggestions and will modify the language as suggested.

Fig 7 is only a model and as all models could be incorrect. However, considering this reviewer’s criticism we will replace the model for a simpler one that is less speculative.

Another important weakness is poor referencing of previous work in the field. Lines 248-250 read almost as if the authors originally hypothesised the idea that calcium is shuttled between ER and mitochondria via membrane contact sites (MCS) - but there is extensive literature on other eukaryotes which should be first cited and discussed in this context. Likewise, the discussion of MCS in Toxoplasma does not include the body of work already published on this parasite by several groups. It is informative to discuss observations in light of what is already known.

We added a citation following the sentence mentioned by the reviewer in lines 248-250 (corrected preprint) and will include more in the revised article. We cite several pertinent articles that describe MCS in Toxoplasma (lines 378-380, very few actually). We will make sure not to miss any new articles that could have been recently published. Note that our work is not about describing the presence of MCSs. We are showing transfer of calcium between the ER and mitochondria and we present evidence that supports that it happens through MCSs.

Author response:

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

Reviewer #1:

- Summary: 

Recordings were made from the dentate nucleus of two monkeys during a decision-making task. Correlates of stimulus position and stimulus information were found to varying degrees in the neuronal activities. 

We agree with this summary.

- Strengths: 

A difficult decision-making task was examined in two monkeys.

We agree with this statement.

- Weaknesses: 

One of the monkeys did not fully learn the task. The manuscript lacked a coherent hypothesis to be tested, and no attempt was made to consider the possibility that this part of the brain may have little to do with the task that was being studied. 

We understand the reviewers concern. It is correct that one of the monkeys (Mi) did not perform at a high level, but it should be noted that both monkeys learned significantly above chance level. Therefore, we would argue that both monkeys in fact did learn the task but Mi’s performance was suboptimal. This difference in the performance levels gave us a rare opportunity to dive deeper into the reasons why some animals perform better than the others and we show that Mi (the lower performing monkey) paid more attention to the outcome of the previous trial – this is evident from our behavioural and decoding models.

We tested the overall hypothesis that neurons of the nucleus dentate can dynamically modulate their activity during a visual attention task, comprising not only sensorimotor but also cognitive attentional components. Many neurons in the dentate are multimodal (Figure 3C-D) which was something that was theorized. One of the specific hypotheses that we tested is that the dentate cells can be direction-selective for both the sensorimotor and cognitive component. Given that many of the recorded cells showed direction-selectivity in their firing rate modulation for gap directions and/or stimulus directions, we provide strong evidence that this hypothesis is correct. We have now spelled out this hypothesis more explicitly in the introduction of the revised version. We now also explain better why we tested this specific hypothesis. Indeed, earlier studies in primates such as those by Herzfeld and colleagues (2018, Nat. Neuro.) and van Es and colleagues (2019, Current Biol) have indicated that direction-selectivity of cerebellar activity may occur in various sensorimotor domains.

We also appreciate the comment of this Reviewer that in our original submission we did not show our attempt to consider the possibility that this part of the brain may have little to do with the task that was being studied. We in fact did consider this possibility in that we successfully injected 3 ml of muscimol (5 μg/ml, Sigma Aldrich) into the dentate nucleus in vivo in one of the monkeys (Mo). This application resulted in a reduction of more than 10% in correct responses of the covert attention task after 45 minutes, whereas the performance remained the same following saline injections. Unfortunately, due to the timing of the experiments and Covid19-related laboratory restrictions we were unable to perform these experiments in the other monkey or repeat them in Mo. We aim to replicate this in future experiments and publish it when we have full datasets of at least two monkeys available. For this paper we have prioritized our tracing experiments, highlighting the connections of the dentate nucleus with attention related areas in brainstem and cortex in both monkeys, following perfusion.

- Perhaps the large differences in performance between the two subjects can be used as a way to interpret the neural data's relationship to behavior, as it provided a source of variance. This is what we would hypothesize if we believed that this area of the brain is playing a significant role in the task. If one animal learns much more poorly, and this region of the brain is important for that behavior, then shouldn't there be clear, interpretable differences in the neural data? 

We thank the Reviewer for this comment. We have added a new Supplementary Figure 2, in which we present the data for both monkeys separately in the revised manuscript. Comparing the two datasets however, we see more commonalities related to the significant learning in both monkeys than differences that might be related to their different levels of learning. We have therefore decided to show the different datasets transparently in the new Supplementary Figure 2, but to stay on the conservative side in our interpretations.

- How should we look for these differences? A number of recent papers in mice have uncovered a large body of data showing that during the deliberation period, when the animal is interpreting a sensory stimulus (often using the whisker system), there is ramping activity in a principal component space among neurons that contribute to the decision. This ramping activity is present (in the PCA space) in the motor areas of the cortex, as well as in the medial and lateral cerebellar nuclei. Perhaps a similar computational approach would benefit the current manuscript. 

We also appreciate this point. We have done the principal component analysis accordingly, and we indeed do find the ramping activity in several components of the dentate activity of both monkeys (Mi and Mo). We have now added a new Supplementary Figure 3 with the first three components of both correct and incorrect trials for Mi and Mo, highlighting their potential contribution.

- What is the hypothesis that is being tested? That is, what do you think might be the function of this region of the cerebellum in this task? It seems to me that we are not entirely in the dark, as previous literature on mice decision-making tasks has produced a reasonable framework: the deliberation period coincides with ramping activity in many regions of the frontal lobe and the cerebellum. Indeed, the ramp in the cerebellum appears to be a necessary condition for the ramp to be present in the frontal lobe. Thus, we should see such ramping activity in this task in the dentate. When the monkey makes the wrong choice, the ramp should predict it. If you don't see the ramping activity, then it is possible that the hypothesis is wrong, or that you are not recording from the right place. 

It is indeed one of our specific hypotheses that the dentate cells can be direction-selective for the preparing cognitive component and/or sensorimotor response. We provide evidence that this hypothesis may be correct when we analyze the regular time response curves (see Figure 2 and the new Supplementary Figure 2 where the data of both monkeys are now presented separately). Moreover, we have now verified this by analysing the ramping curves of PCA space (new Supplementary Figure 3) and firing frequency of DN neurons that modulated upon presentation of the C-stimulus (new Supplementary Figure 4). These figures and findings are now referred to in the main text.

- As this is a difficult task that depends on the ability of the animals to understand the meaning of the cues, it is quite concerning that one of the monkeys performed poorly, particularly in the early sessions. Notably, the disparity between the two subjects is rather large: one monkey at the start of the recordings achieved a performance that was much better than the second monkey did at the end of the recording sessions. You highlighted the differences in performance in Figure 1D and mentioned that you started recording once the animals reached 60% performance. However, this did not make sense to me as the performance of Mi even after the final day of recording did not reach the performance of Mo on the first day of recording. Thus, in contrast to Mo, Mi appeared to be not ready for the task when the recording began.

We understand this point. However, please note that the learning performance of the monkeys concerned retraining sessions after they had had several weeks of vacation. So, even though it is correct that one of the two monkeys had a very good consolidation and started already at a relatively high level on the first retraining session, the other one also started and ended at a level above chance level (the y-axis starts at 0.5). We now highlight this point better in the Results section.

- One objective of having two monkeys is to illustrate that what is true in one animal is also true in the other. In some figures, you show that the neural data are significantly different, while in others you combine them into one. Thus, are you confident that the neural data across the animals should be combined, as you have done in Figure 2? Perhaps you can use the large differences in performance as a source of variance to find meaning in the neural data. 

This is a valid question; as highlighted above, we have now addressed this point in the new Supplementary Figure 2, where the data for both monkeys are presented separately. Given the sample sizes and level of variances, it is in general difficult to draw conclusions about the potential differences and contributions, but the data are sufficiently transparent to observe common trends. With regard to linking differences in the neural data to the differences in performance level, please also consider Figure 4, the new Supplementary Figure 3 (with the ramping PCA component) and new Supplementary Figure 4 (with the additional analysis of the ramping activity of DN neurons that modulated upon presentation of the C-stimulus), which suggests that the ramping stage of Mo starts before that of Mi. This difference highlights the possibility that injecting accelerations of the simple spike modulations of Purkinje cells in the cerebellar hemispheres into the complex of cerebellar nuclei may be instrumental in improving the performance of responses to covert attention, akin to what has been shown for the impact of Purkinje cells of the vestibulocerebellum on eye movement responses to vestibular stimulation (De Zeeuw et al. 1995, J Neurophysiol). This possibility is now also raised in the Discussion.

- How do we know that these neurons, or even this region of the brain, contribute to this task? When a new task is introduced, the contributions of the region of the brain that is being studied are usually established via some form of manipulation. This question is particularly relevant here because the two subjects differed markedly in their performance, yet in Figure 3 you find that a similar percentage of neurons are responding to the various elements of the task.

We appreciate this question. As highlighted above, we are refraining from showing our muscimol manipulation (3 ml of 5 μg/ml muscimol, Sigma Aldrich), as it only concerns 1 successful dataset and 1 control experiment. We hope to replicate this reversible lesion experiment in the future and publish it when we have full new datasets of at least two monkeys available. As explained above, for this paper we have sacrificed both monkeys following a timed perfusion, so as to have similar survival times for the transport of the neuro-anatomical tracer involved.  

- Behavior in both animals was better when the gap direction was up/down vs. left/right. Is this difference in behavior encoded during the time that the animal is making a decision? Are the dentate neurons better at differentiating the direction of the cue when the gap direction is up/right vs. left/right? 

These data have now been included in the new Supplementary Figure 2; we did not observe any significant differences in this respect.

Reviewer #2:

- The authors trained monkeys to discriminate peripheral visual cues and associate them with planning future saccades of an indicated direction. At the same time, the authors recorded single-unit neural activity in the cerebellar dentate nucleus. They demonstrated that substantial fractions of DN cells exhibited sustained modulation of spike rates spanning task epochs and carrying information about stimulus, response, and trial outcome. Finally, tracer injections demonstrated this region of the DN projects to a large number of targets including several known to interconnect the visual attention network. The data compellingly demonstrate the authors' central claims, and the analyses are well-suited to support the conclusions. Importantly, the study demonstrates that DN cells convey many motor and nonmotor variables related to task execution, event sequencing, visual attention, and arguably decision-making/working memory. 

We thank the Reviewer for this positive and constructive feedback.

- The study is solid and I do not have major concerns, but only points for possible improvement. 

We thank the Reviewer for this positive feedback.

- A key feature of this data is the extended changes/ramps in DN output across epochs (Figure 2). Crudely, this presents a challenge for the view that DN output mainly drives motor effectors, as the saccade itself lasts only a tiny fraction of the overall task. Some discussion of this dichotomy in thinking about the function(s) of the cerebellum, vis a vis the multifarious DN targets the authors demonstrate here, etc., would be helpful. 

We agree with the Reviewer and we have expanded our Discussion on this point, also now highlighting the outcome of the new PCA analysis recommended by Reviewer 1 (see the new Supplementary figure Figure 3).

- A high-level suggestion on the data: the presentation of the data focuses (sensibly) on the representation of the stimulus and response epochs (Figures 2-3). Yet, the authors then show that from decoding, it is, in fact, a trial outcome that is best represented in the population (Figure 4). While there is nothing 'wrong' with this, it reads slightly incongruously, and the reader does a bit of a "double take" back to the previous figures to see if they missed examples of the trial-outcome signals, but the previous presentations only show correct trials. Consider adding somewhere in the first 3 main figures some neural data showing comparisons with incorrect trials. This way, the reader develops prior expectations for the outcome decoding result and frame of reference for interpreting it. On a related note, the text contains an earlier introduction of this issue (p24 last sentence) and p25 paragraph 1 cites Figure 3D and 3E for signals "related to the absence of reward" - but the caption says this includes only correct trials? 

We thank the Reviewer for bringing up these points. We have addressed the textual suggestions. Moreover, we have done the PCA analysis suggested by Reviewer 1 for both the correct and incorrect trials (see Supplementary material).

- P29: The discrepancy in retrograde labeling between monkeys (2 orders of magnitude): I realize the authors can't really do anything about this, but the difference is large enough to warrant concerns in the interpretation (how did the tracer spread over the drastically larger area? Isotropically? Could it cross more "hard boundaries" and incorporate qualitatively different inputs/outputs?). A small discussion of possible caveats in interpreting the outcomes would be helpful. 

We fully agree with this comment. As highlighted in the text, in both monkeys we first identified the optimal points for injection in the dentate nucleus electrophysiologically and we used the same pump with the same settings to carry out the injections, but even so the differences are substantial. We suspect that the larger injection might have been caused by an air bubble trapped in the syringe or a deviation in the stock solution, but we can never be sure of that. We have added a potential explanation for the caveat that might have played a role.

- And a list of quick points: 

We have addressed all points listed below; we want to thank the Reviewer for bringing them up.

P3 paragraph 2 needs comma "in daily life,". 

P4 paragraph 2 "C-gap" terminology not previously defined. 

P4 paragraph 2 "animals employed different behavioral strategies". Grammatically, you should probably say "each animal employed a different behavioral strategy," but also scientifically the paragraph doesn't connect this claim to anything about the DN (whereas, e.g., the abstract does make this connection clear). 

P5 paragraph 1 "theca" should be "the". 

P6 paragraph 1 problem with ignashenkova citation insert. 

P10 paragraph 1 I think the spike rate "difference between highest and lowest" is not exactly the same as "variance," you might want to change the terminology. 

P10 paragraph 1 should probably say "To determine if a cell preferentially modulated". 

P10 paragraph 1 last sentence the last clause could be clearer. 

P17 paragraph 2 should be something like "as well as those by Carpenter and..."? 

P20 caption: consider "...directionality in the task: only one C-stim...". 

P20 caption: consider "to the left and right in the [L/R] task...to the top/bottom in the [U/D] task". 

Fig1E and S1 - is there a physical meaning of the "weight" unit, and if none, can this be transformed into a more meaningful unit? 

P21 paragraph 1 consider "activity was recorded for 304 DN neurons...". 

P21 paragraph 1 "correlations with the temporal windows" it's not clear how activity can "correlate" with a time window, consider rephrasing (activity levels changed during these time epochs, depending on stimulus identity). 

P21 paragraph 1 should be "by comparing the number of spikes in a bin...". 

P22 paragraph 2 "when we aligned the neurons to the time of maximum change" needs clarification. The maximum change of what? And per neuron? Across the population? 

P22 paragraph 2 "than that of the facilitating" should be "than did the facilitating units". 

P24 paragraph 1 needs a comma and rewording "Within each direction, trials are sorted by the time of saccade onset". 

P24 paragraph 1 should probably say "Same as in G, but for suppressed cells". 

P24 paragraph 2 should say "more than one task event" not "events". 

P24 paragraph 2 needs a comma "To fully characterize the neural responses, we fitted". 

P25 paragraph 1 should probably say "we sampled from similar populations of DN". 

P34 paragraph 3 consider rephrasing the sentence that contains both "dissociation" and "dissociate". 

P37 last line: consider "coordination of cerebellum and cerebral cortex *in* higher order mental..."? 

P38 paragraph 1 citation needed for "kinematics of goal-directed hand actions of others"? 

P38 paragraph 1 commas probably not needed "map visual input, from high-level visual regions, onto..." 

References

- Herzfeld D.J., Kojima Y, Soetedjo R, Shadmehr R (2018) Encoding of error and learning to correct that error by the Purkinje cells of the cerebellum. Nat Neurosci 21:736–743.

- van Es, D.M., van der Zwaag W., and Knapen T. (2019) Topographic Maps of Visual Space in the Human Cerebellum. Current Biol Volume 29, Issue 10p1689-1694.e3May 20.

- De Zeeuw CI, Wylie DR, Stahl JS, Simpson JI. (1995) Phase relations of Purkinje cells in the rabbit flocculus during compensatory eye movements. J Neurophysiol. Nov;74(5):2051-64. doi: 10.1152/jn.1995.74.5.2051.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors bring together implanted radiofrequency coils, high-field MRI imaging, awake animal imaging, and sensory stimulation methods in a technological demonstration. The results are very detailed descriptions of the sensory systems under investigation.

Strengths:

- The maps are qualitatively excellent for rodent whole-brain imaging. - The design of the holder and the coil is pretty clever.

Weaknesses:

- Some unexpected regions appear on the whole brain maps, and the discussion of these regions is succinct.

- The authors do not make the work and e ort to train the animals and average the data from several hundred trials apparent enough. This is important for any reader who would like to consider implementing this technology.

- The data is not available. This does not let the readers make their own assessment of the results.

Thank you for the comments on this manuscript. We have provided more detailed discussion of the unexpected regions(page 18 – line 491-494) and training procedures(page7-9 – line 172-236). We also uploaded the datasets to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts:  (https://zenodo.org/doi/10.5281/zenodo.13821455). 

Reviewer #2 (Public Review):

Summary:

The manuscript by Hike et al. entitled 'High-resolution awake mouse fMRI at 14 Tesla' describes the implementation of awake mouse BOLD-fMRI at high field. This work is timely as the field of mouse fMRI is working toward collecting high-quality data from awake animals. Imaging awake subjects o ers opportunities to study brain function that are otherwise not possible under the more common anesthetized conditions. Not to mention the confounding e  ects that anesthesia has on neurovascular coupling. What has made progress in this area slow (relative to other imaging approaches like optical imaging) is the environment within the MRI scanner (high acoustic noise) - as well as the intolerance of head and body motion. This work adds to a relatively small, but quickly growing literature on awake mouse fMRI. The findings in the study include testing of an implanted head-coil (for MRI data reception). Two designs are described and the SNR of these units at 9.4T and 14T are reported. Further, responses to visual as well as whisker stimulation recorded in acclimated awake mice are shown. The most interesting finding, and most novel, is the observation that mice seem to learn to anticipate the presentation of the stimulus - as demonstrated by activations evident ~6 seconds prior to the presentation of the stimulus when stimuli are delivered at regular intervals (but not when stimuli are presented at random intervals). These kinds of studies are very challenging to do. The surgical preparation and length of time invested into training animals are grueling. I also see this work as a step in the right direction and evidence of the foundations for lots of interesting future work. However, I also found a few shortcomings listed below.

Weaknesses:

(1) The surface coil, although o ering a great SNR boost at the surface, ultimately comes at a cost of lower SNR in deeper more removed brain regions in comparison to commercially available Bruker coils (at room temperature). This should be quantified. A rough comparison in SNR is drawn between the implanted coils and the Bruker Cryoprobe - this should be a quantitative comparison (if possible) - including any di erences in SNR in deeper brain structures. There are drawbacks to the Cryoprobe, which can be discussed, but a more thorough comparison between the implanted coils, and other existing options should be provided (the Cryoprobe has been used previously in awake mouse experiments(Sensory evoked fMRI paradigms in awake mice - Chen, Physiological e ects of a habituation procedure for functional MRI in awake mice using a cryogenic radiofrequency probe – Yoshida, PREVIOUS REFERENCE). Further, the details of how to build the implanted coils should be provided (shared) - this should include a parts list as well as detailed instructions on how to build the units. Also, how expensive are they? And can they be reused?

Thank you for the comment. We did not use a Bruker Cryoprobe for this work but rather a Bruker 4array surface coil. We are unable to compare to a cryoprobe since we do not have access to one for our system. A comparison to previously published data using different scanners could be possible but would require the sequence contain identical parameters to avoid introducing an uncontrollable variable, we are planning to recruit different laboratories to test the implanted RF coils with their existing cryoprobes in the future study. 

We have included an updated figure comparing SNR at different depths across the Bruker 4-array coil and the implanted RF coils. As shown in Supplementary Figure 7B, there is significant SNR enhancement up to 4 mm cortical depth for both single loop and Figure 8 implanted RF coils in comparison to the Bruker 4-array coil.

Author response image 1.

Comparison between implanted and commercial coils. A shows representative coils in the single loop (left) and figure 8 styles (right). Supplementary Table 1 provides a parts list and cost for making these coils and Supplementary Figure 1 provides a circuit diagram to assemble. B presents the SNR line profile values as a function of distance from Pia Matter for each coil tested at 9.4T: commercial phased array surface coil (4 Array), implanted single loop, and implanted figure 8. SNR values were calculated by dividing the signal by the standard deviation of the noise. C-E shows a representative FLASH image with line profile of SNR measurements from each of the coils used to create the graph seen in B. Clear visual improvement in SNR can be seen in figures C-E. C – Commercial phased array. D – Single loop at 9.4T. E – Figure 8 at 9.4T. (N4 array = 6, Nsingle loop = 5, Nfigure 8 = 5)

Additionally, we have added a supplementary figure (supp fig 1) of a circuit diagram, in an effort to disseminate the prototype design of the coils to other laboratories. We have included a detailed parts list with the cost for construction of the coils configured for our scanner(supp table 1). These specifics though would need to be adjusted to the precise field strength/bore size/animal the coil was being built for. As for reusability, the copper wire is cemented to the animal skull and this implantable coil should be considered as consumables for the awake mouse experiments, though the PCB parts can be retrieved.  

(2) In the introduction, the authors state that "Awake mouse fMRI has been well investigated". I disagree with this statement and others in the manuscript that gives the reader the impression that awake experiments are not a challenging and unresolved approach to fMRI experiments in mice (or rodents). Although there are multiple labs (maybe 15 worldwide) that have conducted awake mouse experiments (with varying degrees of success/thoroughness), we are far from a standardized approach. This is a strength of the current work and should be highlighted as such. I encourage the authors to read the recent systematic review that was published on this topic in Cerebral Cortex by Mandino et al. There are several elements in there that should influence the tone of this piece including awake mouse implementations with the Bruker Cryoprobe, prevalence of surgical preparations, and evaluations of stress.

Thank you for the comment. We agree with the reviewer that the current stage of awake mouse fMRI studies remains to be improved.  And, we have revised the Introduction to highlight the state-of-theart of awake mouse fMRI (Page 4 – line 81-88). 

(3) The authors also comment on implanted coils reducing animal stress - I don't know where this comment is coming from, as this has not been reported in the literature (to my knowledge) and the authors don't appear to have evaluated stress in their mice. 

Since question 3 and 4 are highly related to the acclimation procedures, we will answer the two questions together.   

(4) Following on the above point, measures of motion, stress, and more details on the acclimation procedure that was implemented in this study should be included.

We thank the reviewer to raise the animal training issues.  

During the animal training, we have measured both pupil dynamic and eye motion features from training sessions, of which the detailed procedure is described in Methods (page 7-9 – line 172236). 

The training procedure is carried out over a total of 5 weeks with four phases of training: i. Holding animal in hands, ii. Head-fixation and pupillometry, iii. Head-fixation and pupillometry with mockMRI acoustic exposure, iv. Head-fixation and pupillometry with Echo-Planar-Imaging (EPI) in the MR scanner.

Author response table 1.

As shown in Supp Fig 2B, the spectral power of pupil dynamics (<0.02Hz) and eye movements gradually increased as a function of the training time for head-fixed mice exposed to the mock MRI acoustic environment during phase 3.  In phase 4, when head-fixed mice were put into the scanner for the first time, both eye movements and pupil dynamics were initially reduced during scanning but recovered to an acclimated state on Day 2, similar to the level on Day 8 of phase 3.  These behavioral outputs would provide an alternative way to monitor the stress levels of the mice. 

Author response image 2.

The eye movements (A) and power spectra of pupil dynamics (<0.02Hz) (B) change during different training phases.

It should be noted that stress may be related to increased frequency of eye blinking or twitching movements in human subjects(1–3). Whereas, the eyeblink of head-fixed mice has been used for behavioral conditioning to investigate motor learning in normal behaving mice(4–6). Importantly, head-fixed mouse studies have shown that eye movements are significantly reduced compared to the free-moving mice(7). The increased eye movement during acclimation process would indicate an alleviated stress level of the head-fixed mice in our cases. Meanwhile, stress-related pupillary dilation could dominate the pupil dynamics at the early phase of training(8). We have observed a gradually increased pupil dynamic power spectrum at the ultra-slow frequency during phase 3, presenting the alleviated stress-related pupil dilation but recovered pupil dynamics to other factors, including arousal, locomotion, startles, etc. in normal behaving mice.  Despite the extensive training procedure of the present work in comparison to the existing awake mouse fMRI studies (training strategies for awake mice fMRI have been reviewed by Mandino et al. to show the overall training duration of existing studies(9)), the stress remains a confounding factor for the brain functional mapping in head-fixed mice. In particular, a recent study(10) shows that the corticosterone concentration in the blood samples of head-fixed mice is significantly reduced on Day 25 following the training but remains higher than in the control mice. In the discussion section, we have discussed the potential issues of stress-related confounding factors for awake mouse fMRI studies (Page 16 – lines 436-458). 

(1) A. Marcos-Ramiro, D. Pizarro-Perez, M. Marron-Romera, D. Gatica-Perez, Automatic blinking detection towards stress discovery. ICMI 2014 - Proceedings of the 2014 International Conference on Multimodal Interaction 307–310 (2014). https://doi.org/10.1145/2663204.2663239/SUPPL_FILE/ICMI1520.MP4.

(2) M. Haak, S. Bos, S. Panic, L. Rothkrantz, DETECTING STRESS USING EYE BLINKS AND BRAIN ACTIVITY FROM EEG SIGNALS. Lance 21, 76 (2009).

(3) E. Del Carretto Di Ponti E Sessam, Exploring the impact of Stress and Cognitive Workload on Eye Movements: A Preliminary Study. (2023).

(4) S. A. Heiney, M. P. Wohl, S. N. Chettih, L. I. Ru olo, J. F. Medina, Cerebellar-dependent expression of motor learning during eyeblink conditioning in head-fixed mice. J Neurosci 34, 14845–14853 (2014).

(5) S. N. Chettih, S. D. Mcdougle, L. I. Ruffolo, J. F. Medina, Adaptive timing of motor output in the mouse: The role of movement oscillations in eyelid conditioning. Front Integr Neurosci 5, 12996 (2011).

(6) J. J. Siegel, et al., Trace Eyeblink Conditioning in Mice Is Dependent upon the Dorsal Medial Prefrontal Cortex, Cerebellum, and Amygdala: Behavioral Characterization and Functional Circuitry. eNeuro 2, 51–65 (2015).

(7) A. F. Meyer, J. O’Keefe, J. Poort, Two Distinct Types of Eye-Head Coupling in Freely Moving Mice. Current Biology 30, 2116-2130.e6 (2020).

(8) H. Zeng, Y. Jiang, S. Beer-Hammer, X. Yu, Awake Mouse fMRI and Pupillary Recordings in the UltraHigh Magnetic Field. Front Neurosci 16, 886709 (2022).

(9) F. Mandino, S. Vujic, J. Grandjean, E. M. R. Lake, Where do we stand on fMRI in awake mice? Cereb Cortex 34 (2024).

(10) K. Juczewski, J. A. Koussa, A. J. Kesner, J. O. Lee, D. M. Lovinger, Stress and behavioral correlates in the head-fixed method: stress measurements, habituation dynamics, locomotion, and motor-skill learning in mice. Scientific Reports 2020 10:1 10, 1–19 (2020).

(5) It wasn't clear to me at what times the loop versus "Figure 8" coil was being used, nor how many mice (or how much data) were included in each experiment/plot. There is also no mention of biological sex.

Thank you for the comment. We have clarified sex and number. The figure 8 coil was only used as part of development to show the improvement of the coil design for cortical measurements. The detailed information is described in Method (Page 6 – line 127-129 & Page 10 – line 269-270). Additionally animal numbers have been included in the figure captions.

(6) Building on the points above, the manuscript overall lacks experimental detail (especially since the format has the results prior to the methods).

Thank you for the comment. We have modified the manuscript to increase the experimental detail and moved the methods section before the results.

(7) An observation is made in the manuscript that there is an appreciable amount of negative BOLD signal. The authors speculate that this may come from astrocyte-mediated BOLD during brain state changes (and cite anesthetized rat and non-human primate experiments). This is very strange to me. First, the negative BOLD signal is not plotted (please do this), further, there are studies in awake mice that measure astrocyte activation eliciting positive BOLD responses (see Takata et al. in Glia, 2017).

We thank the reviewer to raise the negative BOLD fMRI observation issue.  We added a subplot of the negative BOLD signal changes in the revised Figure 4. This negative BOLD signals across cortical areas could be coupled with brain state changes upon air-pu -induced startle responses. Our future studies are focusing on elucidating the brain-wide activity changes of awake mice with fMRI.  We also provide a detailed discussion of the potential mechanism underlying the negative BOLD fMRI signals. First, as reported in the paper (suggested  by the reviewer),  astrocytic Ca2+ transients coincide with positive BOLD responses in the activated cortical areas, which is aligning with the neurovascular coupling (NVC) mechanism. However, there is emerging evidence to show that astrocytic Ca2+ transients are coupled with both positive and negative BOLD responses in anesthetized rats(11) and awake mice(12). An intriguing observation is that cortex-wide negative BOLD signals coupled with the spontaneous astrocytic Ca2+ transients could co-exist with the positive BOLD signal detected at the activated cortex.  Studies have shown that astrocytes are involved in regulating brain state changes(13), in particular, during locomotion(14) and startle responses(15). These brain state-dependent global negative BOLD responses are also related to the arousal changes of both non-human primates(16) and human subjects(17).  The established awake mouse fMRI platform with ultra-high spatial resolution will enable the brain-wide activity mapping of the functional nuclei contributing to the brain state changes of head-fixed awake mice in future studies. (Page 17-18 – Line 478-490)

(11) M. Wang, Y. He, T. J. Sejnowski, X. Yu, Brain-state dependent astrocytic Ca2+ signals are coupled to both positive and negative BOLD-fMRI signals. Proc Natl Acad Sci U S A 115, E1647–E1656 (2018).

(12) C. Tong, Y. Zou, Y. Xia, W. Li, Z. Liang, Astrocytic calcium signal bidirectionally regulated BOLD-fMRI signals in awake mice in Proc. Intl. Soc. Mag. Reson. Med. 32, (2024).

(13) K. E. Poskanzer, R. Yuste, Astrocytes regulate cortical state switching in vivo. Proc Natl Acad Sci U S A 113, E2675–E2684 (2016).

(14) M. Paukert, et al., Norepinephrine controls astroglial responsiveness to local circuit activity. Neuron 82, 1263–1270 (2014).

(15) R. Srinivasan, et al., Ca2+ signaling in astrocytes from IP3R2−/− mice in brain slices and during startle responses in vivo. Nat Neurosci 18, 708 (2015).

(16) C. Chang, et al., Tracking brain arousal fluctuations with fMRI. Proc Natl Acad Sci U S A 113, 4518– 4523 (2016).

(17) B. Setzer, et al., A temporal sequence of thalamic activity unfolds at transitions in behavioral arousal state. Nat Commun 13 (2022).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I really enjoyed this work. The maps shown are among the best-quality maps out there. Here are suggestions to the authors.

(1) Both the ACA and VRA are rather unexpected. The authors explain these briefly as being part of the associative cortical areas. Both the ACA and VRA are not canonical associative areas (or at least not to us). This warrants a stronger discussion.

To verify both ACA and VRA as associate areas, we provide the  connectivity map projections from the Allen Brain Atlas (seen below). These projections are derived from a Cre-dependent AAV tracing of axonal projections. We have included an explanation of this in the introduction. 

Author response image 3.

Representative images are shown indicating connections between the barrel cortex and retrosplenial area from an injection in the barrel cortex (Left panel) as well as the visual cortex and cingulate connection from an injection in the visual cortex (Right panel). Images are of connectivity map projections from the Allen Brain Atlas derived from a Cre-dependent AAV tracing of axonal projections

(2) This is a lot of work. But looking at the figures, this is not obvious. We read in the caption that several hundred trials were used. It would be good to also specify how many mice. It would be clearer to represent this info in the figure as well to support the fact that this is not a trivial acquisition.

Thank the reviewer to raise the e ort issue. We have edited the figure to include this information and included the numbers in the text as well

(3) The training protocol is seemingly extensive, but this is only visible by following another reference. Including a description in this work would help the reader make sense of the effort that went into this work.

We thank the reviewer to raise the training protocol issue. We have more thoroughly discussed the training method used for this study (page 7-9 – line 172-236)

(4) I really would love to see that dataset made freely available - this should be the norm.

The datasets have been uploaded to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts: 

(https://zenodo.org/doi/10.5281/zenodo.13821455). 

(page 21 – line 573-579)

Reviewer #2 (Recommendations For The Authors):

(1) I'm a little confused about the stimulation paradigm and the effect of it causing an effective 2second TR (which is on the long side) - please elaborate (a figure might be helpful). The paradigm for visual stimulation also seems elaborate, can you please explain the logic and how it was developed?

Thank you for raising the detailed stimulation paradigm issues. The stimulation paradigm is independent and does not interfere with the setup of the effective 2-second TR. The 2-second TR is based on the usage of 2-segment EPI, each with a TR of 1-second. The application of 2-segment paradigm enables the echo spacing with 0.52 ms with effective image bandwidth with 3858Hz, assuring less image distortion.  The stimulation paradigm was defined by an “8s on, 32s o ” epoch such to elicit a strong BOLD response and could be used for any reasonable TR duration. 

We have included a figure outlining the stimulation paradigm (Supp Fig. 3)

(2) I had difficulties viewing the movies (on my MAC).

Thank you for this note. We have re-upload the videos in .mov format

Author response:

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

Reviewer #1 (Public Review):

Summary:

The pituitary gonadotropins, FSH and LH, are critical regulators of reproduction. In mammals, synthesis and secretion of FSH and LH by gonadotrope cells are controlled by the hypothalamic peptide, GnRH. As FSH and LH are made in the same cells in mammals, variation in the nature of GnRH secretion is thought to contribute to the differential regulation of the two hormones. In contrast, in fish, FSH and LH are produced in distinct gonadotrope populations and may be less (or differently) dependent on GnRH than in mammals. In the present manuscript, the authors endeavored to determine whether FSH may be independently controlled by a distinct peptide, cholecystokinin (CCK), in zebrafish.

Strengths:

The authors demonstrated that the CCK receptor is enriched in FSH-producing relative to LH-producing gonadotropes, and that genetic deletion of the receptor leads to dramatic decreases in gonadotropin production and gonadal development in zebrafish. Also, using innovative in vivo and ex vivo calcium imaging approaches, they show that LH- and FSH-producing gonadotropes preferentially respond to GnRH and CCK, respectively. Exogenous CCK also preferentially stimulated FSH secretion ex vivo and in vivo.

Weaknesses:

The concept that there may be a distinct FSH-releasing hormone (FSHRH) has been debated for decades. As the authors suggest that CCK is the long-sought FSHRH (at least in fish), they must provide data that convincingly leads to such a conclusion. In my estimation, they have not yet met this burden. In particular, they show that CCK is sufficient to activate FSH-producing cells, but have not yet demonstrated its necessity. Their one attempt to do so was using fish in which they inactivated the CCK receptor using CRISPR-Cas9. While this manipulation led to a reduction in FSH, LH was affected to a similar extent. As a result, they have not shown that CCK is a selective regulator of FSH.

Our conclusion regarding the necessity of CCK signaling for FSH secretion is based on the following evidence:

(1) CCK-like receptors are expressed in the pituitary gland predominantly on FSH cells.

(2) Application of CCK to pituitaries elicits FSH cell activation and to a much lesser degree activation of LH cells.  (calcium imaging assays)

(3) Application of CCK to pituitaries and by injections in-vivo significantly increased only FSH release.

(4) Mutating the FSH-specific CCK receptor in a different species of fish (medaka) also causes a complete shutdown of FSH production and phenocopies a fsh-mutant phenotype (Uehara, Nishiike et al. 2023).

Taken together, we believe that this data strongly supports the conclusion that CCK is necessary for FSH production and release from the fish pituitary. Admittedly, the overlapping effects of CCK on both FSH and LH cells in zebrafish (evident in both our calcium imaging experiments and especially in the KO phenotype) complicates the interpretation of the phenotype. We speculate that the effect of CCK on LH cells in zebrafish can be caused either by paracrine signaling within the gland or by the effects of CCK on GnRH neurons that were shown to express CCK receptors .

In the current version, we emphasize that CCK also induces LH secretion. Although it does not affect LH to the same extent as FSH, an overlap does exist. This is mentioned in the abstract and discussion.

Moreover, they do not yet demonstrate that the effects observed reflect the loss of the receptor's function in gonadotropes, as opposed to other cell types.

Although there is evidence for the expression of CCK receptor in other tissues, we do show a direct decrease of FSH and LH expression in the gonadotrophs of the pituitary of the mutant fish; taken together with its significant expression in FSH cells compared to the rest of the cells of the pituitary in the cell specific transcriptomic, it is the most reasonable explanation for the mutant phenotype.

Unfortunately, unlike in mice, technologies for conditional knockout of genes in specific cell types are not yet available for our model and cell types. Additional tissue distribution of the three receptors types of CCK was added in supplementary figure 1, from this tissue distribution it can be appreciated how in the pituitary only CCKBRA (our identified CCK receptor) is expressed, while in other tissues it is either not expressed or expressed with the additional CCK receptors that can compensate its activity.

It also is not clear whether the phenotypes of the fish reflect perturbations in pituitary development vs. a loss of CCK receptor function in the pituitary later in life. Ideally, the authors would attempt to block CCK signaling in adult fish that develop normally. For example, if CCK receptor antagonists are available, they could be used to treat fish and see whether and how this affects FSH vs. LH secretion.

While the observed gonadal phenotype of the KO (sex inversed fish) should have a developmental origin since it requires a long time to manifest, the effect of the KO on FSH and LH cells is probably more acute. Unfortunately a specific antagonist that affect only CCKRBA and not the other CCK receptors wasn’t identified yet.

In the Discussion, the authors suggest that CCK, as a satiety factor, may provide a link between metabolism and reproduction. This is an interesting idea, but it is not supported by the data presented. That is, none of the results shown link metabolic state to CCK regulation of FSH and fertility. Absent such data, the lengthy Discussion of the link is speculative and not fully merited.

In the revised manuscript, we provided data to link cck with metabolic status in supplementary figure 1 and modified the discussion to tone down the link between metabolic status to and reproductive state.

Also in the Discussion, the authors argue that "CCK directly controls FSH cells by innervating the pituitary gland and binding to specific receptors that are particularly abundant in FSH gonadotrophs." However, their imaging does not demonstrate innervation of FSH cells by CCK terminals (e.g., at the EM level).

Innervation of the fish pituitary does not imply a synaptic-like connection between axon terminals and endocrine cells. In fact, such connections are extremely rare, and their functionality is unclear. Instead, the mode of regulation between hypothalamic terminals and endocrine cells in the fish pituitary is more similar to "volume transmission" in the CNS, i.e. peptides are released into the tissue and carried to their endocrine cell targets by the circulation or via diffusion. A short explanation was added in lines 395-398 in the discussion

Moreover, they have not demonstrated the binding of CCK to these cells. Indeed, no CCK receptor protein data are shown.

Our revised manuscript  includes detailed experiments showing the activation of the receptor by its homologous ligand, supplementary Figure 1 includes a transactivation  assay of CCK to its receptor and the effect of the different mutants on the activation of the receptor. Unfortunately, no antibody is available against this fish specific receptor (one of the caveats of working with fish models); therefore, we cannot present receptor protein data.

The calcium responses of FSH cells to exogenous CCK certainly suggest the presence of functional CCK receptors therein; but, the nature of the preparations (with all pituitary cell types present) does not demonstrate that CCK is acting directly in these cells.

We agree with the reviewer that there are some disadvantages in choosing to work with a whole-tissue preparation. However, we believe that the advantages of working in a more physiological context far outweigh the drawbacks as it reflects the natural dynamics more precisely. Since our transcriptome data, as well as our ISH staining, show that the CCK receptor is exclusively expressed in FSH cells, it is improbable that the observed calcium response is mediated via a different pituitary cell type.

Indeed, the asynchrony in responses of individual FSH cells to CCK (Figure 4) suggests that not all cells may be activated in the same way. Contrast the response of LH cells to GnRH, where the onset of calcium signaling is similar across cells (Figure 3).

The difference between the synchronization levels of LH and FSH cells activity stems from the gap-junction mediated coupling between LH cells that does not exist between FSH cells(Golan, Martin et al. 2016). Therefore, the onset of calcium response in FSH cells is dependent on the irregular diffusion rate of the peptide within the preparation, whereas the tight homotypic coupling between LH cells generates a strong and synchronized calcium rise that propagates quickly throughout the entire population

The differences in connectivity between LH and FSH cells is mentioned in lines 194-195

Finally, as the authors note in the Discussion, the data presented do not enable them to conclude that the endogenous CCK regulating FSH (assuming it does) is from the brain as opposed to other sources (e.g., the gut).

We agree with the reviewer that, for now, we are unable to determine whether hypothalamic or peripheral CCK are the main drivers of FSH cells. While the strong innervation of the gland by CCK-secreting hypothalamic neurons strengthens the notion of a hypothalamic-releasing hormone and also fits with the dogma of the neural control of the pituitary gland in fish (Ball 1981), more experiments are required to resolve this question.

Reviewer #2 (Public Review):

Summary:

This manuscript builds on previous work suggesting that the CCK peptide is the releasing hormone for FSH in fishes, which is different than that observed in mammals where both LH and FSH release are under the control of GnRH. Based on data using calcium imaging as a readout for stimulation of the gonadotrophs, the researchers present data supporting the hypothesis that CCK stimulates FSH-containing cells in the pituitary. In contrast, LH-containing cells show a weak and variable response to CCK but are highly responsive to GnRH. Data are presented that support the role of CCK in the release of FSH. Researchers also state that functional overlap exists in the potency of GnRH to activate FSH cells, thus the two signalling pathways are not separate. The results are of interest to the field because for many years the assumption has been that fishes use the same signalling mechanism. These data present an intriguing variation where a hormone involved in satiation acts in the control of reproduction.

Strengths:

The strengths of the manuscript are that researchers have shed light on different pathways controlling reproduction in fishes.

Weaknesses:

Weaknesses are that it is not clear if multiple ligand/receptors are involved (more than one CCK and more than one receptor?). The imaging of the CCK terminals and CCK receptors needs to be reinforced.

Reviewer consultation summary: 

The data presented establish sufficiency, but not necessity of CCK in FSH regulation. The paper did not show that CCK endogenously regulates FSH in fish. This has not been established yet.

This is a very important comment, also raised by reviewer 1. To avoid repetition, please see our detailed response to the comment above.

The paper presents the pharmacological effects of CCK on ex vivo preparations but does not establish the in vivo physiological function of the peptide. The current evidence for a novel physiological regulatory mechanism is incomplete and would require further physiological experiments. These could include the use of a CCK receptor antagonist in adult fish to see the effects on FSH and LH release, the generation of a CCK knockout, or cell-specific genetic manipulations.

As detailed in the responses to the first reviewer, we cannot conduct conditional, cellspecific gene knockout in our model. However we did conducted KO and show the direct effect on FSH and LH secretion together with physiological characterisation of the mutant.

Zebrafish have two CCK ligands: ccka, cckb and also multiple receptors: cckar, cckbra and cckbrb. There is ambiguity about which CCK receptor and ligand are expressed and which gene was knocked out.

In the revised manuscript, we clarified which of the receptors are expressed (CCKRBA) and which receptor is targeted. We also provided data showing the specificity of the receptors (both WT and mutant) to the ligands. Supplementary 1 shows receptor cross-activation. The method also specifies the exact NCBI ID numbers of the targeted receptor and the antibody used for the immunostaining.

Blocking CCK action in fish (with receptor KO) affects FSH and LH. Therefore, the work did not demonstrate a selective role for CCK in FSH regulation in vivo and any claims to have discovered FSHRH need to be more conservative.

We agree with the reviewer that the overlap in the effect of CCK measured in the calcium activation of cells and in the KO model does not allow us to conclude selectivity. In this context, it is crucial to highlight that CCKRBA exhibits high expression on FSH cells but not on LH cells. Therefore, the effect of CCK on LH cells is likely paracrine or through GnRH neurons that were shown to express CCK receptors. In the current version, we emphasize that CCK also induces LH secretion. Although it does not affect LH to the same extent as FSH, an overlap does exist. This is mentioned in the abstract and discussion.

The labelling of the terminals with anti-CCK looks a lot like the background and the authors did not show a specificity control (e.g. anti-CCK antibody pre-absorbed with the peptide or anti-CCK in morphant/KO animals).

Figures colours had been updated to better visualise the specific staining of the antibody. Also, The same antibody had been previously used to mark CCK-positive cells in the gut of the red drum fish(Webb, Khan et al. 2010) , where a control (pre-absorbed with the peptide) experiment had been conducted.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Abstract:

The authors have not yet established that CCK is the primary regulator of FSH in vivo.

In the new version, we highlight the leading effect of CCK on the reproductive axis, which includes FSH and LH.

Introduction:

The authors need to make clear earlier in the Introduction that fish have two types of gonadotropes. This information comes too late (last paragraph) currently.

Added in line 42

They should discuss relevant data on the differential regulation of FSH and LH in fish, as a rationale for looking for different releasing factors.

This has been discussed in the first paragraph of the introduction

In the last sentence of the penultimate paragraph, the authors assume that it must be a hypothalamic factor that regulates FSH. Why is this necessarily the case? Are there data indicating that a hypothalamic factor is required for FSH production in fish?

This has been mentioned in the discussion, we do not deny that circulating CCK or CCK from other brain areas might affect FSH secretion in the pituitary (line 402-404). However, as the hypothalamus serves as the main gateway from the brain to the pituitary and contains hypophysiotropic CCK neurons it is the most reasonable assumption.

Results:

In the first paragraph, the authors reference three types of CCK receptors, only one of which is expressed in the pituitary. The specific receptor should be named here.

The receptor name and NCBI id had been added in this paragraph.

Figure 1: What specificity controls were used for the ISH in Figure 1?

HCR- The method used to identify RNA expression and developed by Molecular Instruments (https://www.molecularinstruments.com/hcr-rnafish-protocols), do not require specific control as had been previously done with older ISH methods. The use of multiple short probes assure the specificity to the RNA.More over the expression is specific to the targeted cells.

In Figure 1D, the red square is missing in the KO fish (at low magnification).

This was fixed in the updated version.

In Figure 1G, the number of dots does not correspond to the number of animals described in the figure legend. Does each point represent an animal?

Each dot represent a fish. The order of the numbers in the legend didn’t match the order in the graph, this had been fixed in the last version

Figure 2A: It is not clear that all FSH (GFP) cells are double-labeled. Should all double-labeled cells appear white? Many appear as green. Some quantification of the proportion of co-labeling is needed. Also, the scale bars are too small to read. Perhaps add the size of the scale bars to the legend.

They are all double-labeled, as can be seen by the single-color images, since GFP fluorescence is stronger than RCaMP fluorescence, the double-labelling might be seen a green cells; a scale bar was added.

Figure 2C: Is the synchronous activity of LH cells here dependent on endogenous GnRH? Can these events be blocked with a GnRH receptor antagonist?

We currently do not have enough data to support this hypothesis and the in vivo 2 photon system is not optimal to answer these questions since these are spontaneous events which are difficult to predict. This is the main reason we moved to an ex vivo system. The similar response we receive when applying GnRH in the ex vivo system support it is GnRH activation.

Figure 4C: As some LH cells respond to CCK, can the authors really claim that CCK is a selective regulator of FSH? What explains the heterogeneity in the response of LH cells to CCK?

In this version, we highlight that CCK directly activates FSH but it is also affecting LH to some extent. However it is clear that the effect on FSH cells is more significant.

Figures 5A and B: With larger Ns, some of the trends might be significant (e.g., GnRH stimulated FSH release and CCK stimulated LH release).

Though there is a trend, the values in the Y axis reveal that the trend of response of FSH to GnRH and LH to CCK is lower then the distribution of the basal response (the before) in all of the graphs. Hence we do not believe a larger N will affect those results. We added the range of the secreted hormones concentrations in the result description to emphasize the difference in values,

Figures 5C and D: What explains the lack of an increase in LH secretion following GnRH treatment?

We did not measure LH Secretion in the plasma as we didn’t have enough blood, we do see an increase in LH transcription (see supplementary figure 5 – figure supplement 1)

Also, as mRNA levels were measured (in C), reference should be made to expression rather than transcription. Not all changes in mRNA levels reflect changes in transcription.Also, remove transcription from the legend. Reference to supplementary Figure 4 in the legend should be supplementary Figure 6. Finally, in C and D, distinguish males from females (as in 5A and B).

Modifications had been done according to the reviewer suggestions.

Figure legends:

The figure legends are very long. One way to shorten them is to remove descriptions of the results. The legends should indicate what is in each figure, not the results of the experiments.

Modifications had been done according to the reviewer suggestions.

Sample sizes should be spelled out in the legends, as they are not in the M&M.

We made sure all sample sizes are mentioned in the legend

Materials and Methods:

Section 1.1 can be removed as it repeats content presented elsewhere.

This section was removed

Section 1.5: It is unclear what this means: "blinding was not applied to ensure tractability" Please clarify.

This section was removed

Reviewer #2 (Recommendations For The Authors):

It appears that zebrafish have two ligands: ccka, cckb. Also multiple receptors: cckar, cckbra and cckbrb. Authors need to discuss this and clearly state which ligand and which receptor they are referring to in the manuscript.

We discussed the receptor type in the first paragraph of the results, the exact synthetic peptide used is described in the methods. The 8 amino acids of the mature CCK peptide are the same between CCKa and CCKb. A sentence regarding the specificity of the antibody to the mature CCK peptide was added in line 101.

"to GnRH puff application (300 μl of 30 μg/μl)"; (250 μl of 30 μg/ml CCK)

Please give the final concentration to make it easy on the readers of the data.

The molarity of the final concentration was added.

(2.4) Differential calcium response underlies differential hormone. This section is a bit confusing to read, for example:

"For that, we collected the medium perfused through our ex vivo system (Fig. 2a) and measured LH and FSH levels using a specific ELISA validated for zebrafish [31] while monitoring the calcium activity of the cells."

So the authors did the ELISA while monitoring the activity (?). This sentence does not make sense: please rewrite it.

We modified this sentence  in line 308-311

To functionally validate the importance of CCK signalling we used CRISPR-cas9 to generate loss-of-function (LOF) mutations in the pituitary- CCK receptor gene.

The authors need to clearly state WHICH gene they inactivated: Zebrafish have three CCK-receptors, so "the pituitary receptor gene" needs to be defined.

Was added again in line 107, and is mentioned in the methods

Figure 3 is a crucial figure!

Figure 3B: The data are not very convincing. Please state how thick the sections are in the figure legend (assuming these are adult pituitaries),

Added in the legend (figure 1C in the new version), slice thickness and adult fish.

Please show at least the merged image a high magnification view of the co-localization of the receptor with the cells.

This is figure 1 in the new revision, a magnified figure was added

Please give the scale bar size for 3B.

Scales for all images were added

Figure 3C: the co-localization of the terminals of the CCK and FSH cells shows very few cells expressing close to terminals.

Important: Because the labelling of the terminals with anti-CCK looks a lot like the background, it is very important to show the control (anti-CCK antibody pre-absorbed with the peptide). The authors should have these data. The photo needs to have been taken at the same gain (contrast) and the photo showing the terminals.

This is  a commercial antibody that had been previously validated for CCK in fish. The co-localization pattern resembles GnRH innervation in the pituitary. In fish when hypothalamic neurons innervate the pituitary they do not innervate all the cells, as this is an endocrine system, the peptide can travel to neighbouring cells via diffusion or aided blood flow (Golan, Zelinger et al. 2015) ).  The images reveal the direct innervation of CCK in the pituitary and its proximity to FSH cells.

Figure 4c, on right. The text seems to be stretched as if the photo was adjusted without locking the aspect ratio. Please check the original images.

This has been fixed

Can the authors use different pseudo colours? Differentiating a double label of white versus yellow is very difficult, and thus the photo is not very convincing.

This had been changed to green and magenta

What is meant by "CCK-AB" antibody? Perhaps anti-CCK would be a better label

This has been fixed

Figure 5A: increase the magnification of the insets; the structure of the gonads is very difficult to see with clarity in these low mag images. The most obvious way to improve this figure is to reduce or eliminate the pie graph (not really necessary) and show a high magnification (and larger) image of the gonadal structure.

This is figure 1 in the new version, with magnification of the gonad next to each body section.

Discussion:

" Moreover, in the zebrafish, as well as in other species, the functional overlap in gonadotropin signalling pathways is not limited to the pituitary but is also present in the gonad, through the promiscuity of the two gonadotropin receptors"<br /> The reasoning of this sentence is not clear: zebrafish do not use GnRH to control reproduction: they lack GnRH1 through genomic rearrangement (see Whitlock, Postlethwait and Ewer 2019) and KO of GnRH2/GnRH3 does not affect reproduction.

While GnRH KO model indicate a redundancy of GnRH in this axis in zebrafish, there is also ample evidence for its importance in regulating reproduction such as its effect on gonadotropin (Golan, Martin et al. 2016) and its use in spawning inductions in fish (Mizrahi and Levavi-Sivan 2023). We believe it is currently too soon to conclude that GnRH signalling is completely non relevant to reproduction in cyprinids.  

Reviewing Editor (Recommendations For The Authors):

It would be interesting to see calcium imaging experiments in the CCKR receptor mutants to establish a more direct connection between peptide action and activity.

We added a receptor assay that reflect the non-activation of the mutated receptors by CCK (supplementary figure 1) , and compared it to the wild type that is activated. This show that: 1) CCK directly activate our identified receptor in FSH cells. 2) the mutated receptors are non-active.

"all homozygous fish (CCKR+12/+7/-1/ CCKR+12/+7/-1, n=12)"

It may be better to write the genotype of fish separately as CCKR+12/+12, CCKR+7/+7 and CCKR-1/-1, n=12) otherwise it seems as if all alleles occurred together in the same fish.

Modified according to the reviewer request

In Figure 1 scale bar legends are very small. 

Description of the scale bars were added to the all the legends

Figure 1 legend "On the top right of each panel is the gender distribution" - fish have no gender but sex.

Modified according to the reviewer request

The authors should endeavour to improve the presentation of the figures. They should use a sans-serif font and check that text is not cut at the edge of figure panels, that scale bars are uniform and clearly labelled and fonts are of similar size and clearly legible. E.g. labels of the fish brain of Fig3A are very small.

We modified all the figures to adapt the font and the scales, we increased the size of the image in Figure 3a to make the labels clearer.

Please use the elife format to name supplementary figures, as Figure X - Figure Supplement Y (each supplement associated with one of the main figures).

Fixed

Peptide concentrations in the ex vivo experiments should also be given as molar concentrations not only as '250 μl of 30 μg/ml CCK'.

Fixed

"In contrast, FSH cells responded with a very low calcium rise in hormonal secretion in response to GnRH" - a very low rise in hormonal secretion

Fixed

Please clarify why you used a GnRH synthetic agonist and not the native peptide.

It is commonly used for spawning induction in fish (line 245); it has also been shown to directly affect the secretion of LH and FSH (Biran, Golan et al. 2014, Biran, Golan et al. 2014, Mizrahi, Gilon et al. 2019) , added to line 245.

References

Ball, J. (1981). "Hypothalamic control of the pars distalis in fishes, amphibians, and reptiles." General and comparative endocrinology 44(2): 135-170.

Biran, J., M. Golan, N. Mizrahi, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2014). "Direct regulation of gonadotropin release by neurokinin B in tilapia (Oreochromis niloticus)." Endocrinology 155(12): 4831-4842.

Biran, J., M. Golan, N. Mizrahi, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2014). "LPXRFa, the Piscine Ortholog of GnIH, and LPXRF Receptor Positively Regulate Gonadotropin Secretion in Tilapia (Oreochromis niloticus)." Endocrinology 155(11): 4391-4401.

Golan, M., A. O. Martin, P. Mollard and B. Levavi-Sivan (2016). "Anatomical and functional gonadotrope networks in the teleost pituitary." Scientific Reports 6: 23777.

Golan, M., E. Zelinger, Y. Zohar and B. Levavi-Sivan (2015). "Architecture of GnRH-Gonadotrope-Vasculature Reveals a Dual Mode of Gonadotropin Regulation in Fish." Endocrinology 156(11): 4163-4173.

Mizrahi, N., C. Gilon, I. Atre, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2019). "Deciphering Direct and Indirect Effects of Neurokinin B and GnRH in the Brain-Pituitary Axis of Tilapia." Front Endocrinol (Lausanne) 10: 469.

Mizrahi, N. and B. Levavi-Sivan (2023). "A novel agent for induced spawning using a combination of GnRH analog and an FDA-approved dopamine receptor antagonist." Aquaculture 565: 739095.

Uehara, S. K., Y. Nishiike, K. Maeda, T. Karigo, S. Kuraku, K. Okubo and S. Kanda (2023). "Cholecystokinin is the follicle-stimulating hormone (FSH)-releasing hormone." bioRxiv: 2023.2005.2026.542428.

Webb, K. A., Jr., I. A. Khan, B. S. Nunez, I. Rønnestad and G. J. Holt (2010). "Cholecystokinin: molecular cloning and immunohistochemical localization in the gastrointestinal tract of larval red drum, Sciaenops ocellatus (L.)." Gen Comp Endocrinol 166(1): 152-159.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review):

The authors introduce a computational model that simulates the dendrites of developing neurons in a 2D plane, subject to constraints inspired by known biological mechanisms such as diffusing trophic factors, trafficked resources, and an activity-dependent pruning rule. The resulting arbors are analyzed in terms of their structure, dynamics, and responses to certain manipulations. The authors conclude that 1) their model recapitulates a stereotyped timecourse of neuronal development: outgrowth, overshoot, and pruning 2) Neurons achieve near-optimal wiring lengths, and Such models can be useful to test proposed biological mechanisms- for example, to ask whether a given set of growth rules can explain a given observed phenomenon - as developmental neuroscientists are working to understand the factors that give rise to the intricate structures and functions of the many cell types of our nervous system. 

Overall, my reaction to this work is that this is just one instantiation of many models that the author could have built, given their stated goals. Would other models behave similarly? This question is not well explored, and as a result, claims about interpreting these models and using them to make experimental predictions should be taken warily. I give more detailed and specific comments below.  

We thank the reviewer for the summary of the work. But the criticism “that this is one instantiation of many models [we] could have built” is unfair as it can apply to any model. We chose one of the most minimalistic models which implements known biological mechanisms including activity-independent and -dependent phases of dendritic growth, and constrained parameters based on experimental data. We compare the proposed model to other alternatives in the Discussion section. In the revised manuscript, we additionally investigate the sensitivity of model output to variations of specific parameters, as explained below.

Point 1.1. Line 109. After reading the rest of the manuscript, I worry about the conclusion voiced here, which implies that the model will extrapolate well to manipulations of all the model components. How were the values of model parameters selected? The text implies that these were selected to be biologically plausible, but many seem far off. The density of potential synapses, for example, seems very low in the simulations compared to the density of axons/boutons in the cortex; what constitutes a potential synapse? The perfect correlations between synapses in the activity groups is flawed, even for synapses belonging to the same presynaptic cell. The density of postsynaptic cells is also orders of magnitude of, etc. Ideally, every claim made about the model's output should be supported by a parameter sensitivity study. The authors performed few explorations of parameter sensitivity and many of the choices made seem ad hoc.  

We have performed detailed sensitivity analysis on the model parameters mentioned by the reviewer, including (I) the density of postsynaptic cells (somatas), (II) the density of potential synapses, and (III) the level of correlations between synapses. 

(I) While the density of postsynaptic cells in our baseline model seems a bit low, at least when compared to densities observed in adulthood (Keller et al., 2018), we explored how altering this value affects the model dynamics. We found that the postsynaptic cell density does not affect the timing of dendritic outgrowth, overshoot and synaptic pruning. It only changes the final size of the dendritic arbor and the resulting number of connected synapses. This analysis is now included in Supplementary Figure 3-2.

(II) The density of potential synapses and the density of connected synapses that we used in the manuscript are already in the range of densities that can be found in the literature (Leighton et al., 2024; Ultanir et al., 2007; Glynn et al., 2011; Yang et al., 2014), some of which we already cited in the original submission.

A potential concern might be that the rapid slowing down of growth in the model could be due to a depletion of potential synapses. To illustrate that this is not the case, we showed that the number of available potential synapses over the time course of the simulations remains high (Figure 3, new panel e). Therefore, the initial density of potential synapses is sufficient and does not affect the final density of connected synapses.

To further illustrate the robustness of our model dynamics to longer simulation times, we added a new supplementary figure (Supplementary Figure 3-1).

These new figure additions (Figure 3e, Supplementary Figure 3-1, and Supplementary Figure 3-2) and their implications for the model dynamics are discussed in the Results section of the revised paper:

p.9 line 198, “After the initial overshoot and pruning, dendritic branches in the model stay stable, with mainly small subbranches continuing to be refined (Figure 3-Figure Supplement 1). This stability in the model is achieved despite the number of potential synaptic partners remaining high (Figure 3e), indicating a balance between activity-independent and activitydependent mechanisms. The dendritic growth and synaptic refinement dynamics are independent of the postsynaptic somata densities used in our simulations (Figure 3-Figure Supplement 2). Only the final arbor size and the number of connected synapses decrease with an increase in the density of the somata, while the timing of synaptic growth, overshoot and pruning remains the same (Figure 3-Figure Supplement 2).”

We also added more details to the description of our model in the Methods section:

p.24 line 615, “For all simulations in this study, we distributed nine postsynaptic somata at regular distances in a grid formation on a 2-dimensional 185 × 185 pixel area, representing a cortical sheet (where 1 pixel = 1 micron, Figure 4). This yields a density of around 300 neurons per 𝑚𝑚2 (translating to around 5,000 per 𝑚𝑚3, where for 25 neurons in Figure 3Figure Supplement 2 this would be around 750 neurons per 𝑚𝑚2 or 20,000 per 𝑚𝑚3). The explored densities are a bit lower than compared to neuron densities observed in adulthood (Keller et al., 2018). In the same grid, we randomly distributed 1,500 potential synapses, yielding an initial density of 0.044 potential synapses per 𝜇𝑚2 (Figure 3e). At the end of the simulation time, around 1,000 potential synapses remain, showing that the density of potential synapses is sufficient and does not significantly affect the final density of connected synapses. Thus, the rapid slowing down of growth in our model is not due to a depletion of potential synaptic partners. The resulting density of stably connected synapses is approximately 0.015 synapses per 𝜇𝑚2 (around 60 synapses stabilized per dendritic tree, Figure 3b). This density compares well to experimental findings, where, especially during early development, synaptic densities are described to be within a range similar to the one observed in our model (Leighton et al., 2024; Ultanir et al., 2007; Glynn et al., 2011; Yang et al., 2014; Koshimizu et al., 2009; Tyler and Pozzo-Miller, 2001).”

(III) Lastly, we investigated how the correlation between synapses of the same activity group might affect our conclusions. As correlations in our model mainly arise from patterns of spontaneous activity which are abundant in early postnatal development (retinal waves (Ackman et al., 2012) or endogenous activity in the form of highly synchronized events involving a large fraction of the cells (Siegel et al., 2012), we explored varying the correlations within each activity group, across activity groups and combinations of both. While this analysis supported our previously described intuition on how competition between synaptic activities should drive activity-dependent refinement, recently a study found direct evidence for such subcellular refinement of synaptic inputs specifically dependent on spontaneous activity between retinal ganglion cell axons and retinal waves in the superior colliculus (Matsumoto et al., 2024). The new analysis confirmed our earlier results that the competition between activity groups leads to activity-dependent refinement and yielded further insight into how the studied activity correlations can affect the competition. Those results are presented in a completely new figure (new Figure 5, supported by the Supplementary Figure 5-1 and 5-2) and discussed in the Results section:

p.11 line 249, “Group activity correlations shape synaptic overshoot and selectivity competition across synaptic groups.

Since correlations between synapses emerge from correlated patterns of spontaneous activity abundant during postnatal development (Ackman et al., 2012; Siegel et al., 2012), we explored a wide range of within-group correlations in our model (Figure 5a). Although a change in correlations within the group has only a minor effect on the resulting dendritic lengths (Figure 5b) and overall dynamics, it can change the density of connected synapses and thus also affect the number of connected synapses to which each dendrite converges throughout the simulations (Figure 5c,e). This is due to the change in specific selectivity of each dendrite which is a result of the change in within-group correlations (Figure 5d). While it is easier for perfectly correlated activity groups to coexist within one dendrite (Figure 5-Figure Supplement 1a, 100%), decreasing within-group correlations increases the competition between groups, producing dendrites that are selective for one specific activity group (60%, Figure 5d, Figure 5-Figure Supplement 1a). This selectivity for a particular activity group is maximized at intermediate (approximately 60%) within-group correlations, while the contribution of the second most abundant group generally remains just above random chance levels (Figure 5-Figure Supplement 1a). Further reducing within-group correlations (20%, Figure 5a) causes dendrites to lose their selectivity for specific activity groups due to the increased noise in the activity patterns (20%, Figure 5a). Overall, reducing within-group correlations increases synapse pruning (Figure 5f, bottom), also found experimentally (Matsumoto et al., 2024) as dendrites require an extended period to fine-tune connections aligned with their selectivity biases. This phenomenon accounts for the observed reduction in both the density and number of synapses connected to each dendrite.

In addition to the within-group correlations, developmental spontaneous activity patterns can also change correlations between groups as for example retinal waves propagated in different domains (Feller et al., 1997) (Figure 5-Figure Supplement 2). An increase in between-group correlations in our model intuitively decreases competition between the groups since fully correlated global events synchronize the activity of all groups (Figure 5-Figure Supplement 2). The reduction in competition reduces pruning in the model, which can be recovered by combining cross-group correlations with decreased within-group correlations (Figure 5-Figure Supplement 2). Our simulations show that altering the correlations within activity groups increases competition (by lowering the within-group correlations) or decreases competition (by raising the across-group correlations). Hence, in our model, competition between activity groups due to non-trivially structured correlations is necessary to generate realistic dynamics between activity-independent growth and activity-dependent refinement or pruning.

In sum, our simulations demonstrate that our model can operate under various correlations in the spike trains. We find that the level of competition between synaptic groups is crucial for the activity-dependent mechanisms to either potentiate or depress synapses and is fully consistent with recent experimental evidence showing that the correlation between spontaneous activity in retinal ganglion cells axons and retinal waves in the superior colliculus governs branch addition vs. elimination (Matsumoto et al., 2024)."

Precise details on the implementation of the changed activity correlations were added to the Methods section:

p. 25 line 638, “Within-group and across-group activity correlations. For the decreased withingroup correlations, we generated parent spike trains for each individual group with the firing rate 𝑟𝑖𝑛 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ 𝑃𝑖𝑛 (e.g., 𝑃𝑖𝑛 = 100%; 60%; 20%, Figure 5). All the synapses of the same group share the same parent spike train and the remaining spikes for each synapse are uniquely generated with the firing rate 𝑟𝑟𝑒𝑠𝑡 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ (1 − 𝑃𝑖𝑛) (e.g., (1 − 𝑃𝑖𝑛) = 0%; 40%; 80%), resulting in the desired firing rate 𝑟𝑡𝑜𝑡𝑎𝑙 (see Table 1). For the increase in across-group correlations, we generated one master spike train with the firing rate 𝑟𝑐𝑟𝑜𝑠𝑠 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ 𝑃𝑐𝑟𝑜𝑠𝑠 for all the synapses of all groups (e.g., 𝑃𝑐𝑟𝑜𝑠𝑠 = 5%; 10%; 20%, Figure 5-Figure Supplement 2). This master spike train is shared across all groups and then filled up according to the within-group correlation (if not specified differently 𝑃𝑖𝑛 = 1 − 𝑃𝑐𝑟𝑜𝑠𝑠 to maintain the rate 𝑟𝑡𝑜𝑡𝑎𝑙). In all the cases, also in those where the change in across-group correlations is combined with the change in within-group correlations, the remaining spikes for each synapse are generated with a firing rate 𝑟𝑟𝑒𝑠𝑡 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ (1 − 𝑃𝑖𝑛 − 𝑃𝑐𝑟𝑜𝑠𝑠) to obtain an overall desired firing rate of 𝑟𝑡𝑜𝑡𝑎𝑙.”

Point 1.2. Many potentially important phenomena seem to be excluded. I realize that no model can be complete, but the choice of which phenomena to include or exclude from this model could bias studies that make use of it and is worth serious discussion. The development of axons is concurrent with dendrite outgrowth, is highly dynamic, and perhaps better understood mechanistically. In this model, the inputs are essentially static. Growing dendrites acquire and lose growth cones that are associated with rapid extension, but these do not seem to be modeled. Postsynaptic firing does not appear to be modeled, which may be critical to activity-dependent plasticity. For example, changes in firing are a potential explanation for the global changes in dendritic pruning that occur following the outgrowth phase.  

Thanks to the reviewer for bringing up these important considerations. We do indeed write in the Introduction (e.g. lines 36-76) which phenomena we include in the model and why. The Discussion also compares our model to others (lines 433-490), pointing out that most models either focus on activity-independent or activity-dependent phases. We include both, combining the influence of both molecular gradients and growth factors as well as activity-dependent connectivity refinements instructed by spontaneous activity. We consider our model a tractable, minimalist mechanistic model which includes both activity-independent and activity-dependent aspects. 

Regarding postsynaptic firing, this is indeed super relevant and an important point to consider. In one of our recent publications (Kirchner and Gjorgjieva, 2021), we studied only an activity-dependent model for the organization of synaptic inputs on non-growing dendrites which have a fixed length. There, we considered the effect of postsynaptic firing (via a back-propagating action potential) and demonstrated that it plays an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron. For example, we showed that it could lead to the emergence of retinotopic maps on the dendritic tree which have been found experimentally (Iacaruso et al., 2017). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree. This is now also discussed in the Discussion section of the revised manuscript:

p. 21 line 491, “Although we did not explicitly model postsynaptic firing, our previous work with static dendrites has shown that it can play an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron (Kirchner and Gjorgjieva, 2021). For example, we showed that it could lead to the emergence of retinotopic maps on the dendritic tree which have been found experimentally (Iacaruso et al., 2017). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree.”

Including the concurrent development of axons in the model is indeed very interesting. In fact, a recent tour-de-force techniques paper found similar to what we assume. Hebbian activity-dependent dynamics of axonal branches of retinal ganglion cells experiencing spontaneous activity in relation to retinal waves in the superior colliculus (Matsumoto et al., 2024). New branches tend to be added at the locations where spontaneous activity of individual branches is more correlated with retinal waves, whereas asynchronous activity is associated with branch elimination. We suspect the same Hebbian activity-dependent dynamics to apply also to dendritic growth. 

To address simultaneous dynamic axons to our growing dendrites, in the revised version of the manuscript, we included a simplified form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, which come from axons of presynaptic partners. We explored different median lifetimes of synapses in combination with several distances with which a synapse can move in the simulated space (new Supplementary Figure 3-3). Our results show that dynamically moving synapses only affect the dynamics and stability of our model when the rate of moving synapses combined with the distance of moving synapses is faster than the dendritic growth. In scenarios in which synapses can move across large distances, dendrites get further destabilized due to synapses transferring from one dendrite to another, perturbing the attractor fields of the potential synapses even in late phases of the simulations. Besides such non-biological scenarios, dynamically moving synapses do not affect the model dynamics too much. Thus, they mostly add additional noise and variability to the growth and pruning without changing the timing and amplitude of the dynamics. These results are discussed in the results section of the revised manuscript:

p.9 line 207, “The development of axons is concurrent with dendritic growth and highly dynamic Matsumoto et al. (2024). To address the impact of simultaneously growing axons, we implemented a simple form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, originating from the axons of presynaptic partners (Figure 3-Figure Supplement 3). When potential synapses can move rapidly (median lifetime of 1.8 hours), the model dynamics are perturbed quite substantially, making it difficult for the dendrites to stabilize completely (Figure 3–Figure Supplement 3c). However, slowly moving potential synapses (median lifetime of 18 hours) still yield comparable results (Figure 3-Figure Supplement 3). The distance of movement significantly influenced results only when potential synaptic lifetimes were short. For extended lifetimes, the moving distance had a minor impact on the dynamics, predominantly affecting the time required for dendrites to stabilize. This was the result of synapses being able to transfer from one dendrite to another, potentially forming new long-lasting connections even at advanced stages of synaptic refinement. In sum, our results show that potential axonal dynamics only affect the stability of our model when these dynamics are much faster than dendritic growth.”

Precise details on the implementation of the dynamically moving synapses and their synaptic lifetimes are now in the Methods section:

p. 25 line 650, “Dynamically moving synapses. For the moving synapses we introduced lifetimes for each synapse, randomly sampled from a log-normal distribution with median 1.8h (for when they move frequently), 4.5h or 18h (for when they move rarely) and variance equal to 1 (Figure 3-Figure Supplement 3b). The lifetime of a synapse decreases only when the synapse is not connected to any of the dendrites (i.e., is a potential synapse). When the lifetime of a synapse expires, the synapse moves to a new location with a new lifetime sampled from the same log-normal distribution. This enables synapses to move multiple times throughout a simulation. The exact locations and distances to which each synapse can move are determined by a binary matrix (dimensions: 𝑝𝑖𝑥𝑒𝑙𝑑𝑖𝑠𝑡𝑎𝑛𝑐𝑒 × 𝑝𝑖𝑥𝑒𝑙𝑑𝑖𝑠𝑡𝑎𝑛𝑐𝑒) representing a ring (annulus) with the inner radius 𝑑/4 and outer radius 𝑑/2 , where the synapse location is at the center of the matrix. All the locations of the matrix within the ring boundaries (between the inner radius and outer radius) are potential locations to which the synapse can move. The synapse then moves randomly to one of the possible locations where no other synapse or dendrite is located. For the movement distances, we chose the ring dimensions 3 × 3, 25 × 25 and 101 × 101, yielding the moving distances (radii) of 1 pixel per movement, 12 pixels per movement and 50 pixels per movement (𝑟 = (𝑑−1)/2). These pixel distances represent small movements, as much as a dendrite can grow in one step (1 micron), and larger movements which are far enough so that the synapse will not attract the same branches again (12 microns) or far enough so that it might attract a completely different dendrite (50 microns, Figure 3-Figure Supplement 3a).”

Point 1.3. Line 167. There are many ways to include activity -independent and -dependent components into a model and not every such model shows stability. A key feature seems to be that larger arbors result in reduced growth and/or increased retraction, but this could be achieved in many ways (whether activity dependent or not). It's not clear that this result is due to the combination of activity-dependent and independent components in the model, or conceptually why that should be the case.

We never argued for model uniqueness. There are always going to be many different models (at different spatial and temporal scales, at different levels of abstraction). We can never study all of them and like any modeling study in systems neuroscience we have chosen one model approach and investigated this approach. We do compare the current model to others in the Discussion. If the reviewers have a specific implementation that we should compare our model to as an alternative, we could try, but not if this means doing a completely separate project.

Point 1.4. Line 183. The explanation of overshoot in terms of the different timescales of synaptic additions versus activity-dependent retractions was not something I had previously encountered and is an interesting proposal. Have these timescales been measured experimentally? To what extent is this a result of fine-tuning of simulation parameters?  

We found that varying the amount of BDNF controls the timescale of the activity-dependent plasticity (see our Figure 6c). Hence, changing the balance between synaptic additions vs. retractions is already explored in Figure 6e and f. Here we show that the overshoot and retraction does not have to be fine-tuned but may be abolished if there is too much activity-dependent plasticity. 

Regarding the relative timescales of synaptic additions vs. retractions: since the first is mainly due to activity-independent factors, and the second due to activity-dependent plasticity, the questions is really about the timescales of the latter two. As we write in the Introduction (lines 61-63), manipulating activity-dependent synaptic transmission has been found to not affect morphology but rather the density and specificity of synaptic connections (Ultanir et al. 2007), supporting the sequential model we have (although we do not impose the sequence, as both activity-independent and activitydependent mechanisms are always “on”; but note that activity-dependent plasticity can only operate on synapses that have already formed).

The described results are robust to parameter variations (performed on the postsynaptic density, potential synapse density, and within- and across-group correlations) as described in the reply to reviewer #1 point 1.1.

Point 1.5. Line 203. This result seems at odds with results that show only a very weak bias in the tuning distribution of inputs to strongly tuned cortical neurons (e.g. work by Arthur Konnerth's group). This discrepancy should be discussed.  

First, we note that the correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter, but is rather a property of correlated spontaneous activity. 

Nonetheless, there is some variability in what the experimental data show. Many studies have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al., 2011; Takahashi et al., 2012; Winnubst et al., 2015; Gökçe et al., 2016; Wilson et al., 2016; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al., 2018; Kerlin et al., 2019; Ju et al., 2020, Hedrick et al., 2022, Hedrick et al., 2024). Interestingly, some in vivo studies have reported lack of fine-scale synaptic organization (Varga et al., 2011; X. Chen et al., 2011; T.-W. Chen et al., 2013; Jia et al., 2010; Jia et al., 2014), while others reported clustering for different stimulus features in different species. For example, dendritic branches in the ferret visual cortex exhibit local clustering of orientation selectivity but do not exhibit global organization of inputs according to spatial location and receptive field properties (Wilson et al. 2016; Scholl et al., 2017). In contrast, synaptic inputs in mouse visual cortex do not cluster locally by orientation, but only by receptive field overlap, and exhibit a global retinotopic organization along the proximal-distal axis (Iacaruso et al., 2017). We proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity similar to the BDNF-proBDNF model that we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021). This is now also discussed in the Discussion section of the revised manuscript:

p. 20 line 471, “The correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter, but is rather a property of spontaneous activity. Nonetheless, there is some variability in what the experimental data show. Many have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al., 2011; Winnubst et al., 2015; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al., 2018; Takahashi et al., 2012; Gökçe et al., 2016; Wilson et al., 2016; Kerlin et al., 2019; Ju et al., 2020; Hedrick et al., 2022, 2024). Other studies have reported lack of fine-scale synaptic organization (Chen et al., 2013; Varga et al., 2011; Chen et al., 2011; Jia et al., 2010, 2014). Interestingly, some of these discrepancies might be explained by different species showing clustering with respect to different stimulus features (orientation or receptive field overlap) (Scholl et al., 2017; Wilson et al., 2016; Iacaruso et al., 2017). Our prior work proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity as we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021).”

Point 1.6. Line 268. How does the large variability in the size of the simulated arbors relate to the relatively consistent size of arbors of cortical cells of a given cell type? This variability suggests to me that these simulations could be sensitive to small changes in parameters (e.g. to the density or layout of presynapses).  

We again thank the reviewer for the detailed explanation and feedback on parameters that should be tested in more detail. We have explored several of the suggested model parameters and believe that we have managed to explain and illustrate their effects on the model's dynamics clearly. The precise changes are explained in the reply to point 1.1 and are now available in the revised version of the manuscript.

Point 1.7. The modeling of dendrites as two-dimensional will likely limit the usefulness of this model. Many phenomena- such as diffusion, random walks, topological properties, etc - fundamentally differ between two and three dimensions.  

Indeed, there are many differences between two and three dimensions. We have ongoing work that extends the current model to 3D but is beyond the scope of the current paper. In systems neuroscience, people have found very interesting results making such simplified geometric assumptions about networks, for instance the one-dimensional ring model has been used to uncover fundamental insights about computations even though highly simplified and abstracted. We are convinced that our model, especially with the new sensitivity analysis, makes interesting and novel contributions and predictions.

Point 1.8. The description of wiring lengths as 'approximately optimal' in this text is problematic. The plotted data show that the wiring lengths are several deviations away from optimal, and the random model is not a valid instantiation of the 2D non-overlapping constraints the authors imposed. A more appropriate null should be considered.  

We appreciate the reviewer’s feedback regarding the use of the term “approximately optimal” in describing wiring lengths. We acknowledge that our initial terminology was imprecise and could be misleading. We had previously referred to the minimal wiring length as the optimal wiring length, which does not fully capture the nuances of neuronal wiring optimization. As noted in prior literature, such as the work by Hermann Cuntz (Cuntz et al., 2010 & 2012), neurons can optimize their wiring beyond simply minimizing dendritic length.

To address this issue, to better capture the balance between wiring minimization and functional constraints, such as conduction delays, we have developed a new modeling approach based on minimum spanning trees with a balancing factor (Cuntz et al., 2010 & 2012). This factor modulates the trade-off between minimizing wiring length and accounting for conduction delays from synapses to the soma. Specifically, the model assumes a balance between minimizing the total dendritic length and minimizing the tree distance between synapses and the site of input integration, typically the soma. This balance is illustrated in Figure 8 (Figure 7 in the original manuscript), where we demonstrate that the deviation from the theoretical minimum length arises because direct paths to synapses often require longer dendrites in our models.

Together with the new result, which we added as the new panels f, g and h to Figure 8 (originally Figure 7), we also adjusted panel a of Figure 8, to now illustrate the difference between random wiring, minimal wiring and minimal conductance delay. The updated Figure 8 and its new findings are discussed in the results section of the revised manuscript:

p.17 line 387, “This deviation is expected given that real dendrites need to balance their growth processes between minimizing wire while reducing conduction delays. The interplay between these two factors emerges from the need to reduce conduction delays, which requires a direct path length from a given synapse to the soma, consequently increasing the total length of the dendritic cable. (Cuntz et al., 2010, 2012; Ferreira Castro et al., 2020).

To investigate this further, we compared the scaling relations of the final morphologies of our models with other synthetic dendritic morphologies generated using a previously described minimum spanning tree (MST) based model. The MST model balances the minimization of total dendritic length and the minimization of conduction delays between synapses and the soma. This balance results in deviations from the theoretical minimum length because direct paths to synapses often require longer dendrites (Cuntz et al., 2008, 2010). The balance in the model is modulated by a balancing factor (𝑏𝑓 ). If 𝑏𝑓 is zero, dendritic trees minimize the cable only, and if 𝑏𝑓 is one, they will try to minimize the conduction delays as much as possible. It is important to note that the MST model does not simulate the developmental process of dendritic growth; it is a phenomenological model designed to generate static morphologies that resemble real cells.

To facilitate the comparison of total lengths between our simulated and MST morphologies, we generated MST models under the same initial conditions (synaptic spatial distribution) as our models and simulated them to match several morphometrics (total length, number of terminals, and surface area) of our grown morphologies. This allowed us to create a corresponding MST tree for each of our synthetic trees. Consequently, we could evaluate whether the branching structures of our models were accurately predicted by minimum spanning trees based on optimal wiring constraints. We found that the best match occurred with a trade-off parameter 𝑏𝑓 = 0.9250 (Figure 8f). Using the morphologies generated by the MST model with the specified trade-off parameter (𝑏𝑓 ), we showed that the square root of the synapse count and the total length (𝐿) in both our model generated trees and the MST trees exhibit a linear scaling relationship (Figure 8g; 𝑅2 = 0.65). The same linear relationship can be observed for the square root of the surface area and the total length 𝐿 of our model trees and the MST trees (Figure 8h; 𝑅2 = 0.73). Overall, these results indicate that our model generate trees are wellfitted by the MST model and follow wire optimization constraints.

We acknowledge that the value of the balancing factor 𝑏𝑓 in our model is higher than the range of balancing factors that is typically observed in the biological dendritic counterparts, which generally ranges between 0.2 and 0.4 (Cuntz et al., 2012; Ferreira Castro et al., 2020; Baltruschat et al., 2020). However, it is still remarkable that our model, which does not explicitly address these two conservation laws, achieves approximately optimal wiring. Why do we observe such a high 𝑏𝑓 value? We reason that two factors may contribute to this. First, in our models, local branches grow directly to the nearest potential synapse, potentially taking longer routes instead of optimally branching to minimize wiring length (Wen and Chklovskii, 2008). Second, the growth process in our models does not explicitly address the tortuosity of the branches, which can increase the total length of the branches used to connect synapses. In the future, it will be interesting to add constraints that take these factors into account. Taken together, combining activity-independent and -dependent dendrite growth produces morphologies that approximate optimal wiring.”

Further details on the fitted MST model and the corresponding analysis were added to the methods section:

p.26 line 669, “Comparison with wiring optimization MST models. To evaluate the wire minimization properties of our model morphologies (n=288), we examined whether the number of connected synapses (N), total length (L), and surface area of the spanning field (S) conformed to the scaling law 𝐿 ≈ 𝜋−1/2 ⋅ 𝑆1/2 ⋅ 𝑁1/2 (Cuntz et al., 2012). Furthermore, to validate that our model dendritic morphologies scale according to optimal wiring principles, we created simplified models of dendritic trees using the MST algorithm with a balancing factor (bf). This balancing factor adjusts between minimizing the total dendritic length and minimizing the tree distance between synapses and the soma (Cost = 𝐿 + 𝑏𝑓 ⋅ 𝑃 𝐿) (MST_tree; best bf = 0.925) (Cuntz et al., 2010); TREES Toolbox http://www.treestoolbox.org).

Initially, we generated MSTs to connect the same distributed synapses as our models. We performed MST simulations that vary the balancing factor between 𝑏𝑓 = 0 and 𝑏𝑓 = 1 in steps of 0.025 while calculating the morphometric agreement by computing the error (Euclidean distance) between the morphologies of our models and those generated by the MST models. The morphometrics used were total length, number of terminals, and surface area occupied by the synthetic morphologies.”

Point 1.9. It's not clear to me what the authors are trying to convey by repeatedly labeling this model as 'mechanistic'. The mechanisms implemented in the model are inspired by biological phenomena, but the implementations have little resemblance to the underlying biophysical mechanisms. Overall my impression is that this is a phenomenological model intended to show under what conditions particular patterns are possible. Line 363, describing another model as computational but not mechanistic, was especially unclear to me in this context.  

What we mean by mechanistic is that we implement equations that model specific mechanisms i.e. we have a set of equations that implement the activity-independent attraction to potential synapses (with parameters such as the density of synapses, their spatial influence, etc) and the activitydependent refinement of synapses (with parameters such as the ratio of BDNF and proBDNF to induce potentiation vs depression, the activity-dependent conversion of one factor to the other, etc). This is a bottom-up approach where we combine multiple elements together to get to neuronal growth and synaptic organization. This approach is in stark contrast to the so-called top-down or normative approaches where the method would involve defining an objective function (e.g. minimal dendritic length) which depends on a set of parameters and then applying a gradient descent or other mathematical optimization technique to get at the parameters that optimize the objective function. This latter approach we would not call mechanistic because it involves an abstract objective function (who could say what a neuron or a circuit should be trying to optimize?) and a mathematical technique for how to optimize the function (we don’t know if neurons can compute gradients of abstract objective functions). 

Hence our model is mechanistic, but it does operate at a particular level of abstraction/simplification. We don’t model individual ion channels, or biophysics of synaptic plasticity (opening and closing of NMDA channels, accumulation of proteins at synapses, protein synthesis). We do, however, provide a biophysical implementation of the plasticity mechanism through the BDNF/proBDNF model which is more than most models of plasticity achieve, because they typically model a phenomenological STDP or Hebbian rule that just uses activity patterns to potentiate or depress synaptic weights, disregarding how it could be implemented. To the best of our understanding, this is what is normally considered mechanistic in the field (in contrast to, for example, biophysical).

Reviewer #2 (Public Review): 

This work combines a model of two-dimensional dendritic growth with attraction and stabilisation by synaptic activity. The authors find that constraining growth models with competition for synaptic inputs produces artificial dendrites that match some key features of real neurons both over development and in terms of final structure. In particular, incorporating distance-dependent competition between synapses of the same dendrite naturally produces distinct phases of dendritic growth (overshoot, pruning, and stabilisation) that are observed biologically and leads to local synaptic organisation with functional relevance. The approach is elegant and well-explained, but makes some significant modelling assumptions that might impact the biological relevance of the results. 

Strengths: 

The main strength of the work is the general concept of combining morphological models of growth with synaptic plasticity and stabilisation. This is an interesting way to bridge two distinct areas of neuroscience in a manner that leads to findings that could be significant for both. The modelling of both dendritic growth and distance-dependent synaptic competition is carefully done, constrained by reasonable biological mechanisms, and well-described in the text. The paper also links its findings, for example in terms of phases of dendritic growth or final morphological structure, to known data well. 

Weaknesses: 

The major weaknesses of the paper are the simplifying modelling assumptions that are likely to have an impact on the results. These assumptions are not discussed in enough detail in the current version of the paper. 

(1) Axonal dynamics. 

A major, and lightly acknowledged, assumption of this paper is that potential synapses, which must come from axons, are fixed in space. This is not realistic for many neural systems, as multiple undifferentiated neurites typically grow from the soma before an axon is specified (Polleux & Snider, 2010). Further, axons are also dynamic structures in early development and, at least in some systems, undergo activity-dependent morphological changes too (O'Leary, 1987; Hall 2000). This paper does not consider the implications of joint pre- and post-synaptic growth and stabilisation.  

We thank the reviewer for the summary of the strengths and weaknesses of the work. While we feel that including a full model of axonal dynamics is beyond the scope of the current manuscript, some aspects of axonal dynamics can be included and are now implemented and tested in the revised manuscript. Since this feedback covers similar aspects of the model that were also pointed out by reviewer #1, we refer here to our detailed reply to their comments 1.1 and 1.2, where we list and discuss all the analyses performed to address the raised issues.

(2) Activity correlations 

On a related note, the synapses in the manuscript display correlated activity, but there is no relationship between the distance between synapses and their correlation. In reality, nearby synapses are far more likely to share the same axon and so display correlated activity. If the input activity is spatially correlated and synaptic plasticity displays distance-dependent competition in the dendrites, there is likely to be a non-trivial interaction between these two features with a major impact on the organisation of synaptic contacts onto each neuron.  

We have explored the amount of correlation (between and within correlated groups) in the revised manuscript (see also our reply to reviewer comment 1.1).

However, previous experimental work, (e.g. Kleindienst et al., 2011) has provided anatomical and functional analyses that it is unlikely that the functional synaptic clustering on dendritic branches is the result of individual axons making more than one synapse (see pg. 1019).

(3) BDNF dynamics 

The models are quite sensitive to the ratio of BDNF to proBDNF (eg Figure 5c). This ratio is also activity-dependent as synaptic activation converts proBDNF into BDNF. The models assume a fixed ratio that is not affected by synaptic activity. There should at least be more justification for this assumption, as there is likely to be a positive feedback relationship between levels of BDNF and synaptic activation.  

The reviewer is correct. We used the BDNF-proBDNF model for synaptic plasticity based on our previous work (Kirchner and Gjorgjieva, 2021).  

There, we explored only the emergence of functionally clustered synapses on static dendrites which do not grow. In the Methods section (Parameters and data fitting) we justify the choice of the ratio of BDNF to proBDNF from published experimental work. We also performed sensitivity analysis (Supplementary Fig. 1) and perturbation simulations (Supplementary Fig. 3), which showed that the ratio is crucial in regulating the overall amount of potentiation and depression of synaptic efficacy, and therefore has a strong impact on the emergence and maintenance of synaptic organization. Since we already performed all this analysis, we expect that the same results will also apply to the current model which includes dendritic growth, as it involves the same activity-dependent mechanism.

A further weakness is in the discussion of how the final morphologies conform to principles of optimal wiring, which is quite imprecise. 'Optimal wiring' in the sense of dendrites and axons (Cajal, 1895; Chklovskii, 2004; Cuntz et al, 2007, Budd et al, 2010) is not usually synonymous with 'shortest wiring' as implied here. Instead, there is assumed to be a balance between minimising total dendritic length and minimising the tree distance (ie Figure 4c here) between synapses and the site of input integration, typically the soma. The level of this balance gives the deviation from the theoretical minimum length as direct paths to synapses typically require longer dendrites. In the model this is generated by the guidance of dendritic growth directly towards the synaptic targets. The interpretation of the deviation in this results section discussing optimal wiring, with hampered diffusion of signalling molecules, does not seem to be correct. 

We agree with this comment. We had wrongly used the term “optimal wiring” as neurons can optimize their wiring not only by minimizing their dendritic length but other factors as noted by the reviewer. In the revised manuscript we replaced the term “optimal wiring” with “minimal wiring” wherever it was incorrectly used. On top of that, we performed further analysis and discussed these differences, as pointed out in the reply to reviewer #1 point 1.8.

To summarize, we want to again thank the reviewer for their in-depth review and all the suggestions that helped us improve the analysis and implementation of our model.

Reviewer #3 (Public Review): 

The authors propose a mechanistic model of how the interplay between activity-independent growth and an activity-dependent synaptic strengthening/weaken model influences the dendrite shape, complexity and distribution of synapses. The authors focus on a model for stellate cells, which have multiple dendrites emerging from a soma. The activity independent component is provided by a random pool of presynaptic sites that represent potential synapses and that release a diffusible signal that promotes dendritic growth. Then a spontaneous activity pattern with some correlation structure is imposed at those presynaptic sites. The strength of these synapses follow a learning rule previously proposed by the lab: synapses strengthen when there is correlated firing across multiple sites, and synapses weaken if there is uncorrelated firing with the relative strength of these processes controlled by available levels of BDNF/proBDNF. Once a synapse is weakened below a threshold, the dendrite branch at that site retracts and loses its sensitivity to the growth signal 

The authors run the simulation and map out how dendrites and synapses evolve and stabilize. They show that dendritic trees growing rapidly and then stabilize by balancing growth and retraction (Figure 2). They also that there is an initial bout of synaptogenesis followed by loss of synapses, reflecting the longer amount of time it takes to weaken a synapse (Figure 3). They analyze how this evolution of dendrites and synapses depends on the correlated firing of synapses (i.e. defined as being in the same "activity group"). They show that in the stabilized phase, synapses that remain connected to a given dendritic branch are likely to be from same activity group (Figure 4). The authors systemically alter the learning rule by changing the available concentration of BDNF, which alters the relative amount of synaptic strengthening, which in turn affects stabilization, density of synapses and interestingly how selective for an activity group one dendrite is (Figure 5). In addition the authors look at how altering the activity-independent factors influences outgrowth (Figure 6). Finally, one of the interesting outcomes is that the resulting dendritic trees represent "optimal wiring" solutions in the sense that dendrites use the shortest distance given the distribution of synapses. They compare this distribute to one published data to see how the model compared to what has been observed experimentally.  

There are many strengths to this study. The consequence of adding the activity-dependent contribution to models of synapto- and dendritogenesis is novel. There is some exploration of parameters space with the motivation of keeping the parameters as well as the generated outcomes close to anatomical data of real dendrites. The paper is also scholarly in its comparison of this approach to previous generative models. This work represented an important advance to our understanding of how learning rules can contribute to dendrite morphogenesis.

We thank the reviewer for the positive evaluation of the work and the suggestions below.

To improve the clarity of the manuscript, we adjusted and fixed some figures and corresponding paragraphs as follows:

(1) We increased the number of ticks and their corresponding numbers in all the figures to make them easier to read and interpret.

(2) In Figure 3 panel d, showing the evolution of synaptic weight, we corrected the upper limit at the yaxis to 1 (from previously 2).

(3) Due to a typo in the implementation of the BDNF concentration, we had to correct the used BDNF concentrations from 49%, 45% and 40%, to 49%, 46.5% and 43% respectively.

(4) The y-axis labels of Figure 6 (old Figure 5) panel e and f were changed to make the plots clearer (e: “morphology change explained (%)” to "effect on morphology (%)", and f: “synapse connection explained (%)” to "effect on connected synapses (%)").

(5) The values for the eta and tau-w in the supplementary Table were corrected. Previously tau-w was falsely 6000 time steps which was corrected to 3000 time steps, and eta was 45% and is now 46.5%.

We believe that all the changes to the manuscript will address the reviewer’s concerns and enhance the clarity and accuracy of the findings described in the manuscript.

Author response:

We thank the reviewers for their thoughtful comments. We are working to revise our manuscript and address each of the reviewers comments. A summary of our planned revisions and responses to some of the reviewers’ major concerns are included below.

Cultivation Density: Reviewers #1 and #2 suggested that additional studies testing the effects of varying bacterial density during animal development (cultivation) would strengthen our findings. While we agree with the reviewers that this is a very interesting experiment, it is not feasible. Indeed, we attempted this experiment but found it nontrivial to maintain stable bacterial density conditions over long timescales as this requires matching the rate of bacterial growth with the rate of bacterial consumption. Despite our best efforts, we have not been able to identify conditions that satisfy these requirements. We will focus our revised manuscript to include only assertions about the effects of recent experiences.

Transfer Method: Reviewers #1 and #2 expressed concern that the stress of transferring animals to a new plate may have resulted in an increased arousal state and thus a greater probability of rejecting patches. We thank the reviewers for this thoughtful remark and plan to conduct additional analyses to address this hypothesis. We did, however, anticipate this possibility and, to mitigate the stress of moving, we used an agar plug method where animals were transferred using the flat surface of small cylinders of agar. Importantly, the use of agar as a medium to transfer animals provides minimal disruption to their environment as all physical properties (e.g. temperature, humidity, surface tension) are maintained. Qualitatively, we observe no marked change in behavior from before to after transfer with the agar plug method, especially as compared to the often drastic changes observed when using a metal or eyelash pick.

Time Parameter: Related to the transfer method, Reviewer #1 expressed concern that the simplest time parameter (time since start of the assay) might better predict animal behavior. We thank the reviewer for pointing out the need to specifically test whether the time-dependent change in explore-exploit decision-making corresponds better with satiety (time off patch) or arousal (time since transfer/start of assay) state. We will conduct additional analyses to address these alternative hypotheses.

Parameter Initialization: Reviewer #1 pointed out an oversight in our methods section regarding the model parameter values used for the first encounter. We plan to clarify the initialization of parameters in the manuscript. In short, for the first patch encounter where k = 1:

● ρk is the relative density of the first patch.

● τs is the duration of time spent off food since the beginning of the recorded experiment. For the first patch, this is equivalent to the total time elapsed.

● ρh is the approximated relative density of the bacterial patch on the acclimation plates (see Assay preparation and recording in Methods). Acclimation plates contained one large 200 µL patch seeded with OD600 = 1 and grown for a total of ~48 hours. As with all patches, the relative density was estimated from experiments using fluorescent bacteria OP50-GFP as described in Bacterial patch density estimation in Methods.

● ρe is equivalent to ρh.

Sensing vs. non-sensing: Reviewer #3 suggested that the term “non-sensing” may not be ethologically accurate. We thank the reviewer for their comment and agree that we do not know for certain whether the animals sensed these patches or were merely non-responsive to them. We are, however, confident that these encounters lack evidence of sensing. Specifically, we note that our analyses used to classify events as sensing or non-sensing examined whether an animal’s slow-down upon patch entry could be distinguished from either that of events where animals exploited or that of encounters with patches lacking bacteria. We found that  “non-sensing” encounters are indeed indistinguishable from encounters with bacteria-free patches where there are no bacteria to be sensed (see Figure 2 - Supplement 7C-D and Patch encounter classification as sensing or non-sensing in Methods). Regardless, we agree with the reviewer that all that can be asserted for certain about these events is that animals do not respond to the bacterial patch in any way that we measured. Therefore, we will replace the term “non-sensing” with “non-responding” to better indicate the ethological interpretation of these events.

Time-dependent changes in sensing vs. non-sensing: Reviewer #1 remarked that the sensation of dilute patches increases with time. We agree with the reviewer that we observe increased responsiveness to dilute patches with time. Although this is interesting, our primary focus was on what decision an animal made given that they clearly sensed the presence of the bacterial patch. Nonetheless, we will add this observation to the discussion as an area of future work to investigate the sensory mechanisms behind this effect.

Classification of sensing vs. non-sensing: Reviewers #2 and #3 expressed concerns about the validity of the two clusters identified using the semi-supervised QDA approach described. We are grateful to the reviewers for pointing out the difficulty in visualizing the clusters and the need for additional clarity in explaining the supervised labeling. We will use additional visualizations and methods to validate the clusters we have discovered. Specifically, we aim to provide additional evidence that the sensing vs. nonsensing data is bi-modal (i.e. a two-cluster classification method fits best). Further, it seems that there may be some confusion as to how we arrived at 3 encounter types (i.e. search, sample, exploit) that we plan to clarify in the manuscript. Specifically, it’s important to note that two methods were used on two different (albeit related) sets of parameters. We first used a two-cluster GMM to classify encounters as explore or exploit. We then used a two-cluster semi-supervised QDA to classify encounters as sensing or non-sensing (to be changed to “non-responding”, see above response) using a different set of parameters. We thus separated the explore cluster into two (sensing and non-sensing exploratory events) resulting in three total encounter types: exploit, sample (explore/sensing), and search (explore/non-sensing). We will clarify this in the text. Additionally, we will clarify the labelling used for “supervising” QDA. Specifically, we made two simple assumptions: 1) animals must have sensed the patch if they exploited it and 2) animals must not have sensed the patch if there were no bacteria to sense. Thus, we labeled encounters as sensing if they were found to be exploitatory as we assume that sensation is prerequisite to exploitation; and we labeled encounters as non-sensing for events where animals encountered patches lacking bacteria (OD600 = 0). All other points were non-labeled prior to learning the model. In this way, our labels were based on the experimental design and results of the GMM, an unsupervised method; rather than any expectations we had about what sensing should look like. The semi-supervised QDA method then used these initial labels to iteratively fit a paraboloid that best separated these clusters, by minimizing the posterior variance of classification.

Accept-reject vs. stay-switch: Reviewers #1 and #2 ask for additional discussion on how the accept-reject decision-making framework differs from the stay-switch framework. We thank the reviewers for alerting us to this gap in our discussion. We intend to clarify that these frameworks ask two different types of questions (i.e. “Do you want to eat it?” versus “If so, how long do you want to eat it for?”). These concepts are well described in canonical foraging theory literature (see Pyke, Pulliam & Charnov 1977 for a review on the subject) and are easily distinguishable for animals that forage using the following framework: 1) search for prey, 2) encounter prey from a distance, 3) identify prey type, 4) decide to pursue (accept-reject decision), 5) pursue and capture the prey, 6) exploit prey, and 7) decide to stop exploiting and start searching again (stay-switch decision). In this case, it is easy to see the distinction between accept-reject and stay-switch decisions. However, in some scenarios, animals must physically encounter prey prior to identification and then must make an accept-reject decision. In these cases where pursuit and capture are not visualized, it is harder to distinguish between accept-reject and stay-switch decisions. In our experiments, we find significant bimodality in encounter duration (see Figure 2H) where short duration (exploratory) encounters appear to represent a lower bound where animals spend the minimum amount of time possible on a patch (less than 2 minutes), which we interpret as a rejection of the patch. On the other hand, exploitatory encounters span a large range of durations from 2 to 60+ minutes which we interpret as an initial acceptance of the patch followed by a series of stay-switch decisions which determine the overall duration of the encounter. While one could certainly model our data using only stay-switch decision-making, we ascertain that an encounter of minimal duration is better interpreted ethologically as a rejection than as an immediate switch decision. We will revise the text to further extrapolate upon our point of view on this somewhat philosophical distinction and what it predicts about C. elegans behavior.

Sensory mutant behavior: Reviewers #1 and #3 ask for further speculation on the observed behavior of osm-6 and mec-4 animals. We will further elaborate on our findings, how they relate to previous studies, and what they suggest about the mechanisms behind these foraging decisions.

Model design: Reviewer #3 suggested several alterations to the behavioral model. While the proposed model seems entirely reasonable and could aid in elucidating the time component of how prior experience affects decision-making, we chose the present model based on our experience with model selection using these data. Indeed, as the reviewer suggested, we did a great number of analyses involving model selection including model selection criteria (AIC, BIC) and optimization with regularization techniques (LASSO and elastic nets). We found that the problem of model selection was compounded by the enormous array of highly correlated variables we had to choose from. Additionally, we found that both interaction terms and non-linear terms of our task variables could be predictive of accept-reject decisions but that the precise set of terms selected depended sensitively on which model selection technique was used and generally made rather small contributions to prediction. The diverse array of results and combinatorial number of predictors to possibly include failed to add anything of interpretable value. We therefore chose to take a different approach to this problem. Rather than trying to determine what the “best” model was we instead asked whether a minimal model could be used to answer a set of core questions. Indeed, our goal was not maximal predictive performance but rather to distinguish between the effects of different influences enough to determine if encounter history had a significant, independent effect on decision making. We thus chose to only include task variables that spanned the most basic components of behavioral mechanisms to ask very specific questions. For example, we selected a time variable that we thought best encapsulated satiety. While we could have included many additional terms, or made different choices about which terms to include, based on our analyses these choices would not have qualitatively changed our results. Further, we sought to validate the parameters we chose with additional studies (i.e. food-deprived and sensory mutant animals). We regard our study as an initial foray into demonstrating accept-reject decision-making in nematodes. The exact mechanisms and, consequently, the best model design is therefore beyond the scope of this study. Lastly, Reviewer #3 criticized the use of only sensed patches in the model. While we acknowledge that we are not certain as to whether the “non-sensing” encounters are truly not sensed, we find qualitatively similar results when including all exploratory patches in our analyses. In fact, when all encounters are used, we find stronger correlations between our task variables and the accept-reject decision. However, we take the position that sensation is necessary for decision-making and thus believe that while our model’s predictive performance may be better using all encounters, the interpretation of our findings is stronger when we only include sensing events.

Author response:

First of all, I'd like to express my heartfelt thanks to you for your meticulous and professional review comments. Your feedback is very important to our work. It not only helps us identify the shortcomings in the paper, but also provides valuable guidance for improving the quality of the paper.

We carefully read every suggestion you made and were deeply inspired. Please rest assured that we will carefully consider and revise each opinion to ensure that our research work is more rigorous and clear. We promise to revise the manuscript accordingly to meet the standards of the journal and enhance the credibility and influence of the research.

The main modifications include the experiment of A Mid1 supplementation experiment in Mid1 knockout micesupplementing Mid1 in Mid1 knockout mice; Detection of kinases such as CaMKII, PKA and ERK1/2; Supplementary references; Supplement the behavioral experiment of new object recognition; Electrophysiological measurement experiment of supplementing LTP; Supplementary neuron-specific immunohistochemical staining experiment; Supplementing the information of knockout mice used in the study; Modify the language expression of the article and the problem of too few pictures.

Thank you again for your valuable time and professional advice. We look forward to submitting the revised manuscript to you for further review.

Author response:

Reviewer #1 (Public review):

Summary:

Cesar, Santos & Cogni use a meta-analysis to report on the direction and magnitude of three fundamental fitness components in defensive symbioses. Specifically, the work focuses on interactions between three arthropod host families (Aphididae, Culicidae, Drosophilidae, and others) and common bacterial endosymbionts (Wolbachia, Serratia, Hamiltonella, Spiroplasma, Rickettsia, Regiella X-type and Arsenophonus). The results of the overall analysis confirm common assumptions and previous work on such fitness components, showing that defensive symbionts provide strong protection to hosts and cause detectable costs to both hosts and the enemy. The analysis provides insight into the extent of the cost/benefit tradeoff for hosts, reporting that the cost is six times lower than the protective effect. The confirmation that natural enemies attacking hosts infected with symbionts have a reduction in their fitness is also an interesting one, as this shows that the majority of defensive symbionts provide protection by resisting enemy infection, as opposed to tolerating it. This finding has important consequences for evolutionary counter-responses in the enemy species. Of course, this result has less relevance for certain types of enemies (such as parasitoids) where successful infection is dependent upon host killing.

Interesting results also emerge from the subgroup analysis. For the full dataset, both natural and introduced symbionts were similarly effective in positively influencing the fitness of hosts. However, in the Wolbachia-specific analysis, the artificially introduced symbionts caused costs to the hosts where the natural strain did not. These findings have potentially important ramifications for schemes that use endosymbionts for biocontrol or vector competence, suggesting that (in some cases) natural strains may be the more stable choice for deploying (as they are associated with lower costs).

The analysis draws from an impressively large dataset, but the interpretation of the full impact of the results would be helped by greater detail on the species/strain level systems included, the data extraction approach, and inclusion criteria. Accounting for phylogenetic nonindependence and alternative coding of one of the moderator variables could also strengthen the biological relevance of the models. Suggestions and thoughts are outlined below.

We sincerely thank Reviewer #1 for the time and effort dedicated to reviewing our manuscript. The suggestions provided are highly constructive and will greatly assist us in improving both our analyses and the manuscript overall.

Strengths & Potential Improvements:

An impressively large number of effect sizes (3000) from only 226 studies is collected, robustly confirming common assumptions on the magnitude of fundamental fitness components. However the paper would benefit from a clear breakdown in the main text of the specificities of each system included (e.g. a table at the host species/symbiont strain level, where it is possible). Currently, there is not enough detail for those who want a deep dive to understand what data was extracted for the analysis from these 226 studies, or those who want to understand the underlying diversity in the dataset.

We thank the reviewer for the suggestion, and we will add this information to our revised manuscript.

Currently, when the 'natural enemy group' is tested as a moderator it is coded broadly by type of organism (e.g. virus, bacterium, fungi, parasitoid). But this doesn't adequately capture the mode of killing/fitness reduction by the enemy, which would be the much more biologically relevant categorisation for your questions. For example, parasitoid infection is dependent upon host death (thus host fecundity is not relevant, because the host either survived or did not). Among bacterial and viral pathogens antagonists there is scope for both fecundity and survival to be affected. This in turn may be a very influential factor for the outcome. You could consider recoding this enemy moderator.

We agree, and we will implement this in the analysis to our revised manuscript.

The analysis is restricted to arthropod hosts and defensive symbionts that are also classed as endosymbionts. This focus should be made clear early on in the paper, as there are many systems (that are classed by many as defensive symbioses) that are not part of the analysis.

We agree, and we will implement this to our revised manuscript.

There is fairly minimalistic testing of moderators/sub-groups (which probably has its statistical strengths) but perhaps there are also some missed opportunities for testing other ecological contributors to variance, including coinfection (although perhaps limited by power) and other approaches to coding enemy group (as detail above).

We agree, and we will implement this in the analysis to our revised manuscript.

Looking at the overview of systems included, there's likely a high degree of phylogenetic non-independence in the dataset. Where it is possible, using phylogenetically controlled models could strengthen this analysis.

We thank the reviewer for the suggestion. We will explore the possibility of using phylogenetically controlled models in our analyses, although we recognize the challenges associated with their implementation, particularly in the case of the natural enemies, given the great diversity of distant related groups included in our study - viruses, bacteria, fungi, protozoans, nematodes and parasitoids wasps.

Looking at your included systems (Table S5), you might be able to test the effect of coinfection on the 3 variables of interest. For example, it would be particularly important to see if the effects of two symbionts are additive or not.

We agree, and we will implement this in the analysis to our revised manuscript.

No code for the analysis is provided for review at this stage and full details of the dataset are also not available. This slightly limits the ability to assess the full scope and robustness of the study. It would be helpful to have an extensive table in the supplementary detailing (minimum) the reference, study, experiment, host species, symbiont strain, and a description of the exact data extraction source (e.g.table/figure/in text), and method of extraction.

The code for the analysis and the full raw data with the suggested information are available at https://github.com/cassiasqr/MetaSymbiont (The link is available at the end of the manuscript).

Reviewer #2 (Public review):

Summary:

In this exciting study, Cesar and co-authors perform a meta-analysis on the influence of arthropod symbionts on the fitness of their hosts when they are exposed or not to natural enemies. These so-called defensive symbionts are increasingly recognized as key elements in arthropod survival against natural enemies, with effects that ripple through entire terrestrial ecosystems. The topic is timely, the approach is sound, and the manuscript is well-written. I believe this manuscript will attract the attention of entomologists and of microbiologists interested in symbiosis. This study builds on a previous meta-analysis that I was involved in, which was based on phloem-feeding insects. This novel data set is much larger and includes flies (including the model system Drosophila) and mosquitoes (a group of high medical interest). While the previous metaanalysis considered only parasitoids as natural enemies, this study also includes fungi, bacteria, and viruses.

Strengths:

The authors compile a very large dataset and provide a broad quantitative overview of the effects of defensive symbionts in insects. By measuring symbiont effects in the presence and absence of natural enemies, the authors are able to infer whether a trade-off between defense and the costs of mutualism in the absence of enemy pressure exists. Defensive symbioses are an important research topic that had its initial "momentum" a decade ago, so the timing for such a systematic review is very appropriate.

We sincerely thank Reviewer #2 for dedicating their time and effort to reviewing our manuscript. The suggestions are very insightful and will significantly contribute to improving our manuscript.

Weaknesses:

I think the manuscript could be improved by clarifying several sections, particularly the introduction and methods. The introduction section is too specific and heavily reliant on particular examples. In my view, the theoretical background of the study could be made clearer, and the knowledge gap identified more explicitly. A focus on how widespread defensive symbioses are, along with a brief, up-to-date review of the groups possessing such symbionts, would help. This lack of focus is also observed in the methods section, where more details are needed in many instances to better understand how data was collected and analyzed. Regarding the analyses, the multi-level analysis contains many moderators, but it's unclear why these moderators were included. While this may seem a minor issue, it highlights a disconnection between the analyses, the conceptual background, and the hypotheses tested. 

We thank the reviewer for the suggestions, and we will try to make the introduction and the methods section clearer. 

Another important weakness is that the analyses are too general, and much-hidden information is not immediately apparent. For instance, readers cannot easily identify which species of symbionts are studied (and the effects they have), or which natural enemies are involved. Although this information is found in the supplementary material, including it in the main body would significantly improve the manuscript.

We agree, and we will implement this to our   revised manuscript.

Author response:

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

Reviewer #1 (Public Review):

In this revision, the authors significantly improved the manuscript. They now address some of my concerns. Specifically, they show the contribution of end-effects on spreading the inputs between dendrites. This analysis reveals greater applicability of their findings to cortical cells, with long, unbranching dendrites than other neuronal types, such as Purkinje cells in the cerebellum.

They now explain better the interactions between calcium and voltage signals, which I believe improve the take-away message of their manuscript. They modified and added new figures that helped to provide more information about their simulations.

However, some of my points remain valid. Figure 6 shows depolarization of ~5mV from -75. This weak depolarization would not effectively recruit nonlinear activation of NMDARs. In their paper, Branco and Hausser (2010) showed depolarizations of ~10-15mV.

More importantly, the signature of NMDAR activation is the prolonged plateau potential and activation at more depolarized resting membrane potentials (their Figure 4). Thus, despite including NMDARs in the simulation, the authors do not model functional recruitment of these channels. Their simulation is thus equivalent to AMPA only drive, which can indeed summate somewhat nonlinearly.

In the current study, we used short sequences of 5 inputs, since the convergence of longer sequences is extremely unlikely in the network configurations we have examined. This resulted in smaller EPSP amplitudes of ~5mV (Figure 6 - Supplement 2A, B). Longer sequences containing 9 inputs resulted in larger somatic depolarizations of ~10mV (Figure 6 - Supplement 2E, F). Although we had modified the (Branco, Clark, and Häusser 2010) model to remove the jitter in the timing of arrival of inputs and made slight modifications to the location of stimulus delivery on the dendrite, we saw similar amplitudes when we tested a 9-length sequence using (Branco, Clark, and Häusser 2010)’s published code (Figure 6 - Supplement 2I, J). In all the cases we tested (5 input sequence, 9 input sequence, 9 input sequence with (Branco, Clark, and Häusser 2010) code repository), removal of NMDA synapses lowered both the somatic EPSPs (Figure 6 - Supplement 2C,D,G,H,K,L) as well as the selectivity (measured as the difference between the EPSPs generated for inward and outward stimulus delivery) (Figure 6 Supplement 2M,N,O). Further, monitoring the voltage along the dendrite for a sequence of 5 inputs showed dendritic EPSPs in the range of 20-45 mV (Figure 6 - Supplement 2P, Q), which came down notably (10-25mV) when NMDA synapses were abolished (Figure 6 - Supplement 2R, S). Thus, even sequences containing as few as 5 inputs were capable of engaging the NMDA-mediated nonlinearity to show sequence selectivity, although the selectivity was not as strong as in the case of 9 inputs.

Reviewer #1 (Recommendations for the authors):

Minor points:

Figure 8, what does the scale in A represent? I assume it is voltage, but there are no units. Figure 8, C, E, G, these are unconventional units for synaptic weights, usually, these are given in nS / per input.

We have corrected these. The scalebar in 8A represents membrane potential in mV. The units of 8C,E,G are now in nS.

Reviewer #2 (Public Review):

Summary:

If synaptic input is functionally clustered on dendrites, nonlinear integration could increase the computational power of neural networks. But this requires the right synapses to be located in the right places. This paper aims to address the question of whether such synaptic arrangements could arise by chance (i.e. without special rules for axon guidance or structural plasticity), and could therefore be exploited even in randomly connected networks. This is important, particularly for the dendrites and biological computation communities, where there is a pressing need to integrate decades of work at the single-neuron level with contemporary ideas about network function.

Using an abstract model where ensembles of neurons project randomly to a postsynaptic population, back-of-envelope calculations are presented that predict the probability of finding clustered synapses and spatiotemporal sequences. Using data-constrained parameters, the authors conclude that clustering and sequences are indeed likely to occur by chance (for large enough ensembles), but require strong dendritic nonlinearities and low background noise to be useful.

Strengths:

(1) The back-of-envelope reasoning presented can provide fast and valuable intuition. The authors have also made the effort to connect the model parameters with measured values. Even an approximate understanding of cluster probability can direct theory and experiments towards promising directions, or away from lost causes.

(2) I found the general approach to be refreshingly transparent and objective. Assumptions are stated clearly about the model and statistics of different circuits. Along with some positive results, many of the computed cluster probabilities are vanishingly small, and noise is found to be quite detrimental in several cases. This is important to know, and I was happy to see the authors take a balanced look at conditions that help/hinder clustering, rather than to just focus on a particular regime that works.

(3) This paper is also a timely reminder that synaptic clusters and sequences can exist on multiple spatial and temporal scales. The authors present results pertaining to the standard `electrical' regime (~50-100 µm, <50 ms), as well as two modes of chemical signaling (~10 µm, 100-1000 ms). The senior author is indeed an authority on the latter, and the simulations in Figure 5, extending those from Bhalla (2017), are unique in this area. In my view, the role of chemical signaling in neural computation is understudied theoretically, but research will be increasingly important as experimental technologies continue to develop.

Weaknesses:

(1) The paper is mostly let down by the presentation. In the current form, some patience is needed to grasp the main questions and results, and it is hard to keep track of the many abbreviations and definitions. A paper like this can be impactful, but the writing needs to be crisp, and the logic of the derivation accessible to non-experts. See, for instance, Stepanyants, Hof & Chklovskii (2002) for a relevant example.

It would be good to see a restructure that communicates the main points clearly and concisely, perhaps leaving other observations to an optional appendix. For the interested but time-pressed reader, I recommend starting with the last paragraph of the introduction, working through the main derivation on page 7, and writing out the full expression with key parameters exposed. Next, look at Table 1 and Figure 2J to see where different circuits and mechanisms fit in this scheme. Beyond this, the sequence derivation on page 15 and biophysical simulations in Figures 5 and 6 are also highlights.

We appreciate the reviewers' suggestions. We have tightened the flow of the introduction. We understand that the abbreviations and definitions are challenging and have therefore provided intuitions and summaries of the equations discussed in the main text.

Clusters calculations

Our approach is to ask how likely it is that a given set of inputs lands on a short segment of dendrite, and then scale it up to all segments on the entire dendritic length of the cell.

Thus, the probability of occurrence of groups that receive connections from each of the M ensembles (PcFMG) is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative zone-length with respect to the total dendritic arbor (Z/L) and the number of ensembles (M).

Sequence calculations

Here we estimate the likelihood of the first ensemble input arriving anywhere on the dendrite, and ask how likely it is that succeeding inputs of the sequence would arrive within a set spacing.

Thus, the probability of occurrence of sequences that receive sequential connections (PcPOSS) from each of the M ensembles is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative window size with respect to the total dendritic arbor (Δ/L) and the number of ensembles (M).

(2) I wonder if the authors are being overly conservative at times. The result highlighted in the abstract is that 10/100000 postsynaptic neurons are expected to exhibit synaptic clustering. This seems like a very small number, especially if circuits are to rely on such a mechanism. However, this figure assumes the convergence of 3-5 distinct ensembles. Convergence of inputs from just 2 ense mbles would be much more prevalent, but still advantageous computationally. There has been excitement in the field about experiments showing the clustering of synapses encoding even a single feature.

We agree that short clusters of two inputs would be far more likely. We focused our analysis on clusters with three of more ensembles because of the following reasons:

(1) The signal to noise in these clusters was very poor as the likelihood of noise clusters is high.

(2) It is difficult to trigger nonlinearities with very few synaptic inputs.

(3) At the ensemble sizes we considered (100 for clusters, 1000 for sequences), clusters arising from just two ensembles would result in high probability of occurrence on all neurons in a network (~50% in cortex, see p_CMFG in figures below.). These dense neural representations make it difficult for downstream networks to decode (Foldiak 2003).

However, in the presence of ensembles containing fewer neurons or when the connection probability between the layers is low, short clusters can result in sparse representations (Figure 2 - Supplement 2). Arguments 1 and 2 hold for short sequences as well.

(3) The analysis supporting the claim that strong nonlinearities are needed for cluster/sequence detection is unconvincing. In the analysis, different synapse distributions on a single long dendrite are convolved with a sigmoid function and then the sum is taken to reflect the somatic response. In reality, dendritic nonlinearities influence the soma in a complex and dynamic manner. It may be that the abstract approach the authors use captures some of this, but it needs to be validated with simulations to be trusted (in line with previous work, e.g. Poirazi, Brannon & Mel, (2003)).

We agree that multiple factors might affect the influence of nonlinearities on the soma. The key goal of our study was to understand the role played by random connectivity in giving rise to clustered computation. Since simulating a wide range of connectivity and activity patterns in a detailed biophysical model was computationally expensive, we analyzed the exemplar detailed models for nonlinearity separately (Figures 5, 6, and new figure 8), and then used our abstract models as a proxy for understanding population dynamics. A complete analysis of the role played by morphology, channel kinetics and the effect of branching requires an in-depth study of its own, and some of these questions have already been tackled by (Poirazi, Brannon, and Mel 2003; Branco, Clark, and Häusser 2010; Bhalla 2017). However, in the revision, we have implemented a single model which incorporates the range of ion-channel, synaptic and biochemical signaling nonlinearities which we discuss in the paper (Figure 8, and Figure 8 Supplement 1, 2,3). We use this to demonstrate all three forms of sequence and grouped computation we use in the study, where the only difference is in the stimulus pattern and the separation of time-scales inherent in the stimuli.

(4) It is unclear whether some of the conclusions would hold in the presence of learning. In the signal-to-noise analysis, all synaptic strengths are assumed equal. But if synapses involved in salient clusters or sequences were potentiated, presumably detection would become easier? Similarly, if presynaptic tuning and/or timing were reorganized through learning, the conditions for synaptic arrangements to be useful could be relaxed. Answering these questions is beyond the scope of the study, but there is a caveat there nonetheless.

We agree with the reviewer. If synapses receiving connectivity from ensembles had stronger weights, this would make detection easier. Dendritic spikes arising from clustered inputs have been implicated in local cooperative plasticity (Golding, Staff, and Spruston 2002; Losonczy, Makara, and Magee 2008). Further, plasticity related proteins synthesized at a synapse undergoing L-LTP can diffuse to neighboring weakly co-active synapses, and thereby mediate cooperative plasticity (Harvey et al. 2008; Govindarajan, Kelleher, and Tonegawa 2006; Govindarajan et al. 2011). Thus if clusters of synapses were likely to be co-active, they could further engage these local plasticity mechanisms which could potentiate them while not potentiating synapses that are activated by background activity. This would depend on the activity correlation between synapses receiving ensemble inputs within a cluster vs those activated by background activity. We have mentioned some of these ideas in a published opinion paper (Pulikkottil, Somashekar, and Bhalla 2021). In the current study, we wanted to understand whether even in the absence of specialized connection rules, interesting computations could still emerge. Thus, we focused on asking whether clustered or sequential convergence could arise even in a purely randomly connected network, with the most basic set of assumptions. We agree that an analysis of how selectivity evolves with learning would be an interesting topic for further work.

References

Bhalla, Upinder S. 2017. “Synaptic Input Sequence Discrimination on Behavioral Timescales Mediated by Reaction-Diffusion Chemistry in Dendrites.” Edited by Frances K Skinner. eLife 6 (April):e25827. https://doi.org/10.7554/eLife.25827.

Branco, Tiago, Beverley A. Clark, and Michael Häusser. 2010. “Dendritic Discrimination of Temporal Input Sequences in Cortical Neurons.” Science (New York, N.Y.) 329 (5999): 1671–75. https://doi.org/10.1126/science.1189664.

Foldiak, Peter. 2003. “Sparse Coding in the Primate Cortex.” The Handbook of Brain Theory and Neural Networks. https://research-repository.st-andrews.ac.uk/bitstream/handle/10023/2994/FoldiakSparse HBTNN2e02.pdf?sequence=1.

Golding, Nace L., Nathan P. Staff, and Nelson Spruston. 2002. “Dendritic Spikes as a Mechanism for Cooperative Long-Term Potentiation.” Nature 418 (6895): 326–31. https://doi.org/10.1038/nature00854.

Govindarajan, Arvind, Inbal Israely, Shu-Ying Huang, and Susumu Tonegawa. 2011. “The Dendritic Branch Is the Preferred Integrative Unit for Protein Synthesis-Dependent LTP.” Neuron 69 (1): 132–46. https://doi.org/10.1016/j.neuron.2010.12.008.

Govindarajan, Arvind, Raymond J. Kelleher, and Susumu Tonegawa. 2006. “A Clustered Plasticity Model of Long-Term Memory Engrams.” Nature Reviews Neuroscience 7 (7): 575–83. https://doi.org/10.1038/nrn1937.

Harvey, Christopher D., Ryohei Yasuda, Haining Zhong, and Karel Svoboda. 2008. “The Spread of Ras Activity Triggered by Activation of a Single Dendritic Spine.” Science (New York, N.Y.) 321 (5885): 136–40. https://doi.org/10.1126/science.1159675.

Losonczy, Attila, Judit K. Makara, and Jeffrey C. Magee. 2008. “Compartmentalized Dendritic Plasticity and Input Feature Storage in Neurons.” Nature 452 (7186): 436–41. https://doi.org/10.1038/nature06725.

Poirazi, Panayiota, Terrence Brannon, and Bartlett W. Mel. 2003. “Pyramidal Neuron as Two-Layer Neural Network.” Neuron 37 (6): 989–99. https://doi.org/10.1016/S0896-6273(03)00149-1.

Pulikkottil, Vinu Varghese, Bhanu Priya Somashekar, and Upinder S. Bhalla. 2021. “Computation, Wiring, and Plasticity in Synaptic Clusters.” Current Opinion in Neurobiology, Computational Neuroscience, 70 (October):101–12. https://doi.org/10.1016/j.conb.2021.08.001.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) The technology requires a halo-tagged derivation of the active compound, and the linked position will have a huge impact on the potential "target hits" of the molecules. Given the fact that most of the active molecules lack of structure-activity relationship information, it is very challenging to identify the optimal position of the halo tag linkage.

We appreciate your insightful comment. While finding the optimal position to attach a chemical linker to a small molecule of interest is indeed a challenging but necessary step, this is a common difficulty across all target-ID methods, except for those that are modification-free, as we described in Discussion. However, modification-free approaches such as DARTS, CETSA, and TPP have their own limitations, such as low sensitivity and a high false-positive rate. Additionally, DARTS and SPROX are limited to use with cell lysates. Please refer to the introduction in our manuscript for more details on these approaches. On the other hand, synthesizing HTL derivatives is relatively straightforward compared to other modifications, and we provide helpful guidelines for chemical linker design, provided the optimal chemical moiety has been identified, which is crucial for target identification. We selected dasatinib and HCQ/CQ as model compounds because previous studies offered insights into their derivative synthesis. Our data also show that DH5 retains strong kinase inhibitory activity (Figure 4—figure supplement 2), and DC661-H1 demonstrates potent inhibition of autophagy (Figure 6—figure supplement 1). For novel compounds, conducting a thorough structure-activity relationship (SAR) study is essential to determine the optimal position for HTL derivative synthesis.

(2) Although POST-IT works in zebrafish embryos, there is still a long way to go for the broad application of the technology in other animal models.

Thank you for your constructive comment. Yes, there is still a long way to go in developing the POST-IT system for broader applications in other animal models, especially in mice. However, we hope that our study provides valuable insights and inspiration to scientists and experts for applying the POST-IT system in various models. We are also committed to further improving its applicability.

(3) The authors identified SEPHS2 as a new potential target of dasatinib and further validated the direct binding of dasatinib with this protein. However, considering the super strong activity of dasatinib against c-Src (sub nanomolar IC50 value), it is hard to conclude the contribution of SEPHS2 binding (micromolar potency) to its antitumor activity.

Thank you for your insightful comment. We agree that the anticancer activity of dasatinib primarily results from inhibiting tyrosine kinases such as SRC and ABL. However, SEPHS2 contains an “opal" termination codon, UGA, at the 60th amino acid residue, which codes for selenocysteine. Due to the technical challenge of expressing selenoproteins in E. coli, we mutated it to cysteine for expression in E. coli to avoid premature translation termination, as described in the Materials and Methods section. Although the purified recombinant SEPHS2 shows a Kd of about 10 µM for dasatinib, the binding affinity to endogenous SEPHS2 may be higher since selenocysteine is larger and more electronegative than cysteine. This presents an interesting area for future investigation. Furthermore, our study of dasatinib’s binding to SEPHS2 could help facilitate the development of new SEPHS2 inhibitors, potentially targeting the active site of SEPHS2.

Reviewer #3 (Public review):

(1) Target Specificity: It is crucial for the authors to differentiate between the primary targets of the POST-IT system and those identified as side effects. This distinction is essential for assessing the specificity and utility of the technology.

Thank you for your insightful comment. Drugs inevitably bind to various proteins with differing affinities, which can contribute to both side effects and beneficial outcomes. Typically, the primary targets exhibit high affinities. In this manuscript, we ranked the identified protein targets of DH5 based on affinity from mass spectrometry and p-values (Fig. 5A), and for DC661-H1, we used the SILAC ratio (Fig. 6A). We also individually assessed many drug-protein binding affinities using the MST assay, as well as in vitro and in cellulo assays, demonstrating their specificity. Moreover, we believe it is essential to identify as many protein targets as possible at physiological drug concentrations to better understand the drug’s side effects. Of course, further investigation is required to assess the roles and effects of these target proteins.

(2) In Vivo Target Identification: The manuscript lacks detailed clarity on which specific targets were successfully identified in the in vivo experiments. Expanding on this information would provide a clearer view of the system's effectiveness and scope in complex biological settings.

Thank you for your insightful comment regarding in vivo target identification. In this manuscript, we utilized a cell line as the primary method for in vivo target identification and validation after optimizing our system in test tubes. We successfully validated many of the targets identified using our POST-IT system (Figure 6—figure supplement 3). To demonstrate the proof of principle for in vivo application, we employed zebrafish embryos as an in vivo model, showing that endogenous SRC can be effectively pulled down by DH5 treatment (Fig. 7). While we could have explored the entire proteome to identify endogenous target proteins in zebrafish that bind to DH5 or dasatinib, we felt this would extend beyond our original scope, given that we have already demonstrated POST-IT’s ability to identify target proteins for dasatinib. Specific target identification and validation are crucial when using zebrafish for drug discovery. Additionally, we acknowledge that drugs likely interact with a range of protein targets in living organisms and may undergo metabolism and interactions within the circulatory system, which we address in our discussion.

(3) Reproducibility and Scalability: Discussion on the reproducibility of the POST-IT system across various experimental setups and biological models, as well as its scalability for larger-scale drug discovery programs, would be beneficial.

Thank you for the suggestion. While our system has shown  high reproducibility in our experiments, further improving both reproducibility and scalability would be advantageous. One potential approach to address this is through the generation of stable-expressing cell lines and transgenic zebrafish lines, which we have discussed in the revised manuscript. Establishing stable cell lines with robust POST-IT expression could enhance scalability for drug discovery applications.

(4) Quantitative Analysis: A more detailed quantitative analysis of the protein interactions identified by POST-IT, including statistical significance and comparative data against other technologies, would enhance the manuscript.

Thank you for your suggestion. In our assessment of drug-protein affinity, we included Kd values as quantitative measures using MST assays. The protein targets of dasatinib identified through mass spectrometry are also accompanied by p-values for quantitative analysis (Fig. 5A), and the detailed procedures are described in the Material and methods section. While it is challenging to provide direct comparative data against other technologies, our system successfully identified many known target proteins for dasatinib, as well as SEPHS2 and VPS37C as new targets for dasatinib and for HCQ/CQ, respectively, which were not detected by other methods.

(5) Technological Limitations: The authors should discuss any limitations or potential pitfalls of the POST-IT system, which would be crucial for future users and for guiding subsequent improvements.

Thank you for your insightful suggestion We agree that clearly defining the technological limitations is important. Therefore, we have expanded our original discussion on the limitations of our POST-IT system (Discussion section, paragraph 6).

(6) Long-Term Stability and Activity: Information on the long-term stability and activity of the POST-IT components in different biological environments would ensure the reliability of the system in prolonged experiments.

Yes, this is an important question. We did not notice any stability or toxicity issues with Halo-PafA and Pup substrates in HEK293T cells or zebrafish, which is an important factor for stable cell lines and transgenic zebrafish lines. However, HTL derivatives of the drug could be toxic or unstable due to the nature of the drug or its metabolism, which needs to be taken into account when designing experiments, and we have included this in the Discussion.

(7) Comparison with Existing Technologies: A detailed comparison with existing proximity tagging and target identification technologies would help position POST-IT within the current landscape, highlighting its unique advantages and potential drawbacks.

We appreciate your valuable feedback and agree that such comparisons are crucial. We have included a detailed overview and comparison of existing proximity-tagging systems and their related target identification technologies in the Introduction (lines 78-100) and Discussion (lines 391-412), highlighting their respective pros and cons. Additionally, we have expanded the discussion to further compare these technologies with our POST-IT system, addressing its advantages and limitations (lines 378-390, lines 448-467). We hope this provides sufficient context and information to effectively position POST-IT among the landscape of proximity-tagging target identification technologies.

(8) Concerns Regarding Overexposed Bands: Several figures in the manuscript, specifically Figure 3A, 3B, 3C, 3F, 3G, Figure 4D, and the second panels in Figure 7C as well as some figures in the supplementary file, exhibit overexposed bands.

We appreciate your astute observation regarding the overexposed bands and apologize for any confusion. The “overexposed” bands represent the unpupylated proteins, while the bands above them correspond to the pupylated proteins. We intended to clearly show both pupylated and unpupylated bands, although the latter are generally much weaker. We are currently working on further improving our POST-IT system to enhance pupylation efficiency.

(9) Innovation Concern: There is a previous paper describing a similar approach: Liu Q, Zheng J, Sun W, Huo Y, Zhang L, Hao P, Wang H, Zhuang M. A proximity-tagging system to identify membrane protein-protein interactions. Nat Methods. 2018 Sep;15(9):715-722. doi: 10.1038/s41592-018-0100-5. Epub 2018 Aug 13. PMID: 30104635. It is crucial to explicitly address the novel aspects of POST-IT in contrast to this earlier work.

Thank you for bringing this to our attention. Proximity-tagging systems like BioID, TurboID, NEDDylator, and PafA (Lui Q et al., Nat Methods 2018) were initially developed to study protein-protein interactions or identify protein interactomes, as these applications are of broader interest and generally easier to implement. However, applying proximity-tagging systems for small molecule target identification requires significant optimization. As described in the introduction (lines 78-100), target protein identification systems have since been developed using TurboID and NEDDylator (Tao AJ et al., Nat Commun 2023; Hill ZB et al., J Am Chem Soc 2016). It is conceivable that a PafA-based proximity-tagging system could also be adapted for target-ID, and other groups may pursue this approach in the future. Although the PafA-Pup system shows great promise for target-ID applications, extensive optimization was needed to enable its use for this purpose. Finally, we demonstrate that POST-IT offers distinct advantages over other proximity-tagging-based target-ID systems. For more details, please refer to the introduction and discussion sections.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Figure 1- Figure Supplement 1A: The Pup substrate "HB-Pup" is mentioned, but the main text or figure legend provides no introduction or description.

We appreciate your astute observation. We have added a description in the main text and figure legend as follows: “…and used HB-Pup as a control, which contains 6´His and BCCP at the N terminus of Pup” in the main text (line 142) and “HB, TS, and SBP refer to 6´His and BCCP, twin-STII (Strep-tag II), and streptavidin binding peptide, respectively.” in the Figure 1-figure supplement 1A.

(2) Figure 1 - Figure Supplement 3B: The authors used TS-sPupK61R as a substrate but did not explain why. The main text mentions that mutating sPup alone did not affect polypupylation, raising the question of why TS-sPupK61R was used in this figure. Furthermore, while the authors state that polypupylation becomes evident after 1 hour of incubation (more pronounced after 2 or 3 hours), the reactions here were conducted for only 30 minutes.

Thank you for your question. Figure 1 - Figure Supplement 3B was conducted to test self-pupylation levels in the different Halo-PafA derivatives. For this purpose, we could use any Pup substrate such as SBP-sPup and SBPK4R-sPupK61R, instead of Ts-sPup and TS-sPupK61R, as they do not show any differences in pupylation activity. We chose Ts-sPup and TS-sPupK61R simply because any Pup substrates could be used for this purpose. Similarly, we did not need to incubate the reaction for a longer time to detect polypupylation, as our intention was to test “self-pupylation”. We demonstrated in Figure 1 – figure supplement 2 that polypupylation is dependent on the number or position of lysine residues in Pup substrate or tags. The results clearly showed that self-pupylation was almost completely abolished by the Halo8KR mutation. To clarify this, we added the following description in lines 168-169: “Ts-sPup and TS-sPupK61R were chosen as sPup substrates for this experiment, although any Pup substrates could have been used. The levels of self-pupylation were assessed.”

(3) Line 156: The statement that "the TS-tag completely abolished polypupylation in TS-sPup" is inaccurate. Using TSK8R-sPupK61R as the substrate, several bands appear, which likely represent Halo-PafA with varying degrees of polypupylation. Some bands also appear to correspond to those seen when using TS-sPup as a substrate. The authors should clarify how they distinguish between multipupylation and polypupylation in this case.

We sincerely appreciate your insight into clarifying the distinction between multipupylation and polypupylation. Polypupylation refers to the addition of a new Pup onto a previously linked Pup on the target protein, akin to polyubiquitination. In contrast, multipupylation involves multiple single pupylations at different positions on the target proteins. Since pupylation occurs exclusively at lysine residues in tag-Pup substrates, mutating all lysine residues to arginine, as in TSK48R-sPupK61R, prevents the mutant tag-Pup from linking to another Pup. This means that only single pupylation can proceed with this type of mutant Pup substrate. If multiple pupylated bands are observed with this mutant substrate, it indicates “multipupylation” rather than “polypupylation”, as shown in Figure 1-figure supplement 2D. The same applies to the pupylation bands in Figure 1-figure supplement 2E and F, as sSBP-sPupK61R and SBPK4R-sPupK61R lack lysine residues. By comparing these multipupylation bands, it is also possible to distinguish them from polypupylation bands, which are marked by yellow arrows. However, after 2-3 pupylation bands, higher-order bands become increasingly difficult to distinguish.

To clarify the mutation in the TS-tag, we revised the sentence in line 156 from “However, further mutations within the TS-tag completely abolished polypupylation in TS-sPup” to “However, further mutations of two lysine residues within the TS-tag, creating TSK8R-sPupK61R, completely abolished polypupylation in TS-sPup”. Additionally, we have inserted sentences in line 152 to define polypupylation and multipupylation, as described here.

(4) Line 160: Similar to the above concern about line 156, the claim that SBPK4R and sSBP completely prevented polypupylation is unconvincing and requires more supporting evidence.

Thank you for raising this concern. As mentioned above, both SBPK4R and sSBP lack lysine residues required for pupylation. As a result, these mutants can only undergo multiple single pupylations on the lysine residues of the target protein, which leads to “multipupylation”. In Figure 1-figure supplement 2E and F, pupylation bands by sSBP-sPupK61R or SBPK4R-sPupK61R do not display doublet bands (one from multipupylation and the other from polypupylation), as seen with SBP-sPup, marked by yellow arrows. Notably, Halo-PafA containing polypupylated branches migrates more slowly than one with an equal number of multipupylation events. To clarify this point, we have added the phrase “as shown in sSBP-sPupK61R and SBP4KR-sPupK61R” at the end of the sentence in line 160.

(5) Lines 176-177: The authors claim that PafAS126A exhibited reduced polypupylation compared to PafA, but given that PafAS126A may reduce depupylase activity, how could it reduce polypupylation levels? Moreover, it is hard to find any data supporting this conclusion in Figure 1 - Figure Supplement 3B.

We appreciate your insightful comment. At this point, we do not fully understand how the mutation that reduces depupylase activity also decreases polypupylation. It is possible that PafAS126A has a lower preference for pupylated Pup as a prey, which is required for polypupylation, since depupylase activity depends on recognizing pupylated Pup as a prey to remove it. Nonetheless, Halo-PafAS126A shows reduced levels of higher molecular weight bands compared to Halo-PafA, as shown in Figure 1-figure supplement 3B, while exhibiting increased pupylation in lower molecular weight bands, which represent either multipupylation or low-degree polypupylation. Since higher molecular weight bands (> 150 kD) are likely due to polypupylation, this result suggests reduced polypupylation and increased multipupylation in Halo-PafAS126A. To clarify this in the main text, we have added the following description in line 177: “as evidenced by the decreased levels of high molecular weight bands and an increase in low molecular weight bands”

(6) POST-IT system in cellulo validation: The system was developed using the Halo-tag, yet the in-cell validation uses FRB and FKBP instead, without explaining this switch. This inconsistency makes the logic of the experiment unclear.

We appreciate your insightful comment. The interaction between rapamycin and FRB or FKBP is known to be highly specific and robust, making this system useful in various biological contexts. Due to this property, rapamycin can induce interaction between two proteins when one is fused with FRB and the other with FKBP. Before testing or optimizing the POST-IT system in cells, we hypothesized that using the rapamycin-induced interaction between FRB and FKBP could introduce pupylation of the target protein, provided that PafA is fused with FRB or FKBP and the target protein is fused with the other. The results demonstrate that PafA can introduce pupylation of the target protein in a proximity-dependent manner via this chemically induced interaction. To further clarify this in the main text, we modified the original sentence in lines 214-216 as follows: “To mimic drug-target interaction-induced pupylation in live cells and assess the potential of PafA as a proximity-tagging system for target-ID, we incorporated the rapamycin-induced interaction between FRB and FKBP into our PL system, as this interaction between a small molecule and a protein is known to be highly specific and robust (Figure 3—figure supplement 1A).”

(7) Line 209: The authors decided to use the SBP-tag for further studies due to better performance, but in Figure 3 - Figure supplement 1, they still used the unintroduced HB-Pup as the substrate, which is confusing and lacks explanation.

Thank you for raising your question. The SBP-tag is not superior to the TS-tag in terms of pupylation activity. However, the TSK8R mutant cannot bind to Strep-Tactin beads, while the SBP mutants, SBPK4R and sSBP, can bind to streptavidin. Therefore, we chose the SBP-tag instead of the TS-tag for further studies as a Pup substrate in POST-IT system, as we needed to pull down the target proteins. HB-Pup is consistently used as a control throughout various experiments, as it is the original Pup substrate. In Figure 3-figure supplement 1B and C, HB-Pup was used to test chemically induced pupylation by PafA. In these cases, it was not so critical which Pup substrate was chosen. Furthermore, we compared HB-Pup and different SBP-sPup substrates in Figure 3-figure supplement 1D, where HB-Pup was used as a control or for comparison. Although pupylation bands with HB-Pup appear more robust, this substrate contains multiple lysine residues, leading to high levels of polypupylation. To make it clear, we modified the sentence in line 209 to “Therefore, we decided to use the SBP-tag as a Pup substrate in the POST-IT system for further studies.”.

(8) Line 220: Both SBP-sPup and SBPK4R-sPupK61R are described as exhibiting efficient pupylation, but the data show mostly self-pupylation and little to no pupylation of the target protein.

Thank you for your concern. However, pupylation of the target protein is actually quite substantial, as the intensities of the free form and pupylated proteins are relatively similar, as shown in the upper panel of Figure 3-figure supplement 1D. Self-pupylation is always much higher than target pupylation, because PafA constantly pupylates itself, whereas pupylation of the target protein occurs only through interaction. Furthermore, V5-FRB-mKate2-PafA contains many lysine residues, which increases the levels of self-pupylation.

(9) Lines 222-224: The authors chose SBPK4R-sPupK61R to avoid polypupylation, although SBP-sPup did not cause detectable polypupylation. Neither substrate caused pupylation of the target protein, so the rationale behind this choice is unclear.

Thank you for raising your question. Similar to the above comment (#8), please refer to the pupylation bands of the target protein, as shown in the upper panel of Figure 3-figure supplement 1D. The pupylation band of the target protein is quite remarkable, as the intensities of the free form and pupylated proteins are comparable. Additionally, there are no multiple pupylation bands in either case, except for one additional weak multipupylation band, indicating no polypupylation by SBP-sPup, which does not have K-to-R mutations. Of course, SBPK4R-sPupK61R can only undergo single pupylation, as it does not contain lysine residues. Although we did not observe polypupylation by SBP-sPup in this experimental condition, it is possible that SBP-sPup may cause polypupylation under different experimental conditions or with other target proteins. Since SBPK4R-sPupK61R exhibits comparable pupylation of the target protein at least in this experiment setting as SBP-sPup, we selected SBPK4R-sPupK61R as the Pup substrate for POST-IT system to avoid any potential polypupylation that could be caused by SBP-sPup in other cases. We believe that polypupylation can introduce bias into the analysis and hinder the comprehensive discovery of additional target proteins for small molecules.

(10) Line 224: The authors conclude that rapamycin greatly reduced self-pupylation, but the supporting data are unclear.

Thank you for your constructive comments on our manuscript. Please refer to the lower panel of Figure 3-figure supplement 1D. When using either SBPK4R-sPupK61R or SBP-sPup, rapamycin treatment results in reduced levels of self-pupylation compared to the no-treatment control. However, we did not observe this reduction with HB-Pup and do not know the reason. To clarify this in the main text, we added the following description to the end of the sentence: “when using either SBPK4R-sPupK61R or SBP-sPup, as shown in the lower panel of Figure 3—figure supplement 1D”

(11) Line 234: The authors selected an 18-amino acid linker, but given that linkers longer than 10 amino acids enhance labeling, this choice should be explained.

Thank you for raising your question. In fact, a linker of 10 amino acids (aa) or longer is likely to behave similarly. We chose an 18 aa linker instead of a 40 aa linker primarily for the convenience of cloning and to reduce the potential for DNA sequence recombination associated with longer repeats. Additionally, a longer, flexible linker may behave like an intrinsically disordered protein (Harmon et al., 2017), which can lead to unwanted protein-protein interactions or phase separation. To elaborate on this, we added the following sentences after the sentence in line 233-235: “We chose the 18-amino acid linker instead of the 40-amino acid linker for easier cloning and to lower the risk of DNA recombination from longer repeats. Additionally, a longer, flexible linker may behave like an intrinsically disordered protein (Harmon et al., 2017), an unwanted feature for target-ID.”

(12) S126A and K172R mutations: The authors claim that these mutations additively enhanced pupylation under cellular conditions, but in Figure 3B, the band intensities appear similar for the wild-type and mutant versions.

Thank you for raising your concern. Although a single pupylation band appears similar among the three different Halo-PafA proteins, multipupylation bands are slightly but noticeably increased by the S126A and K172R mutations compared to Halo8KR-PafA. Since we used SBPK4R-sPupK61R as a Pup substrate, all higher molecular weight bands result from multipupylation rather than polypupylation. This illustrates why it is preferable to use SBPK4R-sPupK61R over SBP-sPup, as the pupylation bands with SBP-sPup are mixtures of poly- and multipupylation, making it difficult to assess levels of target labeling. To clarify this in the main text, we added the following description after the sentence in line 236: “as the higher molecular weight multipupylation bands are slightly but noticeably increased with these mutations compared to Halo8KR-PafA”

(13) Line 263: The authors selected DH5 for further experiments due to its efficiency, but the data suggest that the performance of DH1 to DH5 is similar.

We appreciate your question about the different dasatinib HTL derivatives. However, our data clearly show that DH2-5 derivatives bind significantly more effectively to Halo-PafA in vitro and in live cells compared to DH1 (Figure 4A and B). Additionally, the DH2-5 derivatives result in dramatically increased pupylation of the target protein in vitro and noticeable enhancement in live cells (Figure 4C and D). Among DH2 to DH5, there is no obvious difference in binding to Halo-PafA or pupylation of the target protein. Therefore, we chose DH5, as we believe that the longer linker in DH5 may facilitate the binding of a more diverse range of target proteins to dasatinib, enabling the discovery of additional target proteins.

(14) Line 309: The authors introduce HCQ and CQ as important drugs but then investigate the mechanism using DC661 without introducing or justifying the choice of this compound.

Thank you for your point. We explained the reason to choose DC661, a dimer form of CQ, instead of CQ for the synthesis of an HTL derivative in line 310. “assuming that a dimer would enhance binding affinity as previously described.” As the dimer forms of a drug or a small molecule such as testosterone dimers, estrogen dimers, and numerous anticancer drug dimers have been often developed to enhance drug effects (Paquin A et., Molecules 2021). Similarly, dimer forms of HCQ/CQ have been introduced and shown to be more potent (Hrycyna CA et al., ACS Chem Biol 2014; Rebecca VW et al., Cancer Discovery 2019). We expected that using a dimer form might offer higher probability to identify target proteins for HCQ/CQ.

(15) The authors suggest that multipupylation levels were enhanced but do not explain whether this might benefit the system or introduce other issues. Clarifying this point would provide valuable insight for potential users of this system.

Thank you for your thoughtful suggestion. Polypupylation likely leads to biased enrichment of a limited set of target proteins, and its levels may not correlate with the binding affinity of target proteins to the small molecule of interest, features that can negatively impact target-ID. In contrast, multipupylation may be correlated with binding affinity or interaction frequency, as we observed increased levels of multipupylation with higher Pup concentrations and longer incubation times. This suggests that target proteins with multiple lysines in proximity to PafA can be sequentially pupylated, starting with the most accessible lysine. However, if a target protein has only one accessible lysine, pupylation will occur only once, regardless of the protein’s affinity to the small molecule. In summary, while polypupylation may be a drawback for target-ID, multipupylation could be useful for both target-ID and understanding binding mode. To elaborate on this, we added the following additional explanation after the sentence in line 152: “, whereas multipupylation is more likely correlated with binding affinity or interaction frequency.”

(16) The author should address whether the Halotag ligand modification of the drug alters the binding properties between the drug and targets. That may be causing artifact binding of the drug and other proteins.

Thank you for your insightful comment. Yes, it is true that chemical modifications of the small molecule of interest, such as linker derivatization (e.g., HTL) or photo-affinity labeling, generally lead to reduced activity or affinity compared to the original molecule. Synthesizing a derivative is a common challenge across all target-ID methods, except for modification-free approaches, as we mentioned in the Discussion. However, modification-free methods like DARTS, CETSA, and TPP have their own limitations, including low sensitivity or high false positive rates. Identifying the optimal position for chemical modification on the small molecule of interest is critical. We chose dasatinib and HCQ/CQ as model compounds, because previous studies provided insights into their derivative synthesis. In addition, our data show that DH5 retains robust kinase inhibitory activity (Figure 4-figure supplement 2), and DC661-H1 exhibits potent autophagy inhibition (Figure 6-figure supplement 1). For novel compounds, a thorough structure-activity relationship study is essential to identify the optimal position for HTL derivative synthesis.

(17) The author stated there is no observable toxicity in zebrafish without providing a detailed analysis or enough data. Further analysis of the expression of Halo-PafA and its substrate sPup influence on toxicity or side effects to the living cells or animals would be needed. It is important for in vivo applications.

Thank you for your constructive suggestion. We have now included additional experimental data in Figure 7-figure supplement 1, showing no toxicity in zebrafish embryos expressing the POST-IT system. We assessed toxicity in two ways: by injecting the POST-IT DNA plasmid into one-cell-stage embryos for acute expression, and by using embryos from transgenic zebrafish expressing POST-IT under a heat-shock inducible promoter. Neither the injection nor the heat-shock activation of POST-IT expression resulted in any noticeable toxicity.

Author response:

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

eLife Assessment

This important work presents two studies on predictive processes in subjects with and without tinnitus. The evidence supporting the authors' claims is compelling, as their second study serves as an independent replication of the first. Rigorous matching between study groups was performed, especially in the second study, increasing the probability that the identified differences in predictive processing can truly be attributed to the presence of tinnitus. This work will be of interest to researchers, especially neuroscientists, in the tinnitus field.

We thank the editors at elife very much for their favorable assessment of our manuscript. Based upon the comments of the reviewer, we aimed to further improve our manuscript to be a valuable addition to the tinnitus research field.

Public Reviews:

Reviewer #2 (Public review):

Summary:

This study aimed to test experimentally a theoretical framework that aims to explain the perception of tinnitus, i.e., the perception of a phantom sound in the absence of external stimuli, through differences in auditory predictive coding patterns. To this aim, the researchers compared the neural activity preceding and following the perception of a sound using MEG in two different studies. The sounds could be highly predictable or random, depending on the experimental condition. They revealed that individuals with tinnitus and controls had different anticipatory predictions. This finding is a major step in characterizing the top-down mechanisms underlying sound perception in individuals with tinnitus.

Strengths:

This article uses an elegant, well-constructed paradigm to assess the neural dynamics underlying auditory prediction. The findings presented in the first experiment were partially replicated in the second experiment, which included 80 participants. This large number of participants for an MEG study ensures very good statistical power and a strong level of evidence. The authors used advanced analysis techniques - Multivariate Pattern Analysis (MVPA) and classifier weights projection - to determine the neural patterns underlying the anticipation and perception of a sound for individuals with or without tinnitus. The authors evidenced different auditory prediction patterns associated with tinnitus. Overall, the conclusions of this paper are well supported, and the limitations of the study are clearly addressed and discussed.

Weaknesses:

Even though the authors took care of matching the participants in age and sex, the control could be more precise. Tinnitus is associated with various comorbidities, such as hearing loss, anxiety, depression, or sleep disorders. The authors assessed individuals' hearing thresholds with a pure tone audiogram, but they did not take into account the high frequencies (6 kHz to 16 kHz) in the patient/control matching. Moreover, other hearing dysfunctions, such as speech-in-noise deficits or hyperacusis, could have been taken into account to reinforce their claim that the observed predictive pattern was not linked to hearing deficits. Mental health and sleep disorders could also have been considered more precisely, as they were accounted for only indirectly with the score of the 10-item mini-TQ questionnaire evaluating tinnitus distress. Lastly, testing the links between the individuals' scores in auditory prediction and tinnitus characteristics, such as pitch, loudness, duration, and occurrence (how often it is perceived during the day), would have been highly informative.

Thank you very much for your careful evaluation of our manuscript. We agree with you that our study design has some limitations such as the assessment of higher frequencies, comorbidities, and tinnitus characteristics. In our discussion, we aimed to acknowledge these issues for future research to improve this study design and gain more insights into neural tinnitus processes.

See e.g.:

Line 946-949:

“Additionally, we rigorously controlled for hearing loss in Study 2, however, pure-tone audiometric testing was solely performed up to 8kHz and we were therefore not able to draw conclusions regarding hearing impairments in higher frequencies and their influence on the effects.”

Line 949-954:

“Moreover, we did not screen our participants for hyperacusis. This hypersensitivity to mild sounds is widely correlated with the sensation of tinnitus and underlying neural mechanisms are potentially intertwined with tinnitus processes (Schilling et al., 2023; Yukhnovich et al., 2023; Zheng, 2020). Screening for hyperacusis in future work can therefore reveal more details on participant characteristics influencing predictive processing.”

Line 955-958:

“In both studies, tinnitus distress was not correlated with the reported prediction effects. Nevertheless, tinnitus can also be characterized by other features such as its loudness, pitch or duration which were not included in the experimental assessment.”

Line 958-963:

“Additionally, we solely used a short version of the Mini-TQ (Goebel and Hiller, 1992) in Study 2, which did not allow us to relate prediction scores to subscales like sleep disturbances which potentially influence cognitive functioning and thus predictive processing. Next to sleeping disorders and distress, tinnitus is often also accompanied by psychological comorbidities such as depression or anxiety (Langguth, 2011) which are potential confounds of the results.”

Comments on revisions:

Thank you for your responses. There are a few remaining points that, if addressed, could further enhance the manuscript:

- While the manuscript acknowledges the limitation of not matching groups on hearing thresholds in Study 1, a deeper analysis of participants' hearing abilities and their impact on MEG results, similar to that conducted in Study 2, would be valuable. Specifically, including a linear model that considers all frequencies, group membership, and their interactions could highlight differences across groups. Additionally, examining the effect of high-frequency hearing loss on prediction scores, as performed in Study 2, would strengthen the analysis, particularly given the trend noted (line 719). Such an addition could make a significant contribution to the literature by exploring how hearing abilities may influence prediction patterns.

We appreciate your feedback and agree with you that it is a crucial question how hearing abilities influence prediction patterns in tinnitus. However, as hearing status was not assessed in the control group in study 1, we are unfortunately not able to include linear models to investigate differences across groups in this sample. This led us to the implementation of study 2 with a comprehensive hearing assessment to investigate group differences. We highlighted this issue in our methods section.

Line 170-172:

“As pure-tone audiometric testing was not included for the control subjects, group comparisons between hearing thresholds were not feasible.”

- The connection with the hippocampal regions (line 864) remains somewhat unclear. While the inclusion of the Paquette reference appropriately links temporal region activity with tinnitus, it does not fully support the statement: "An increased focus on hippocampal regions, e.g., in fMRI, patient, or animal studies, could be a worthwhile complement to our MEG work, given the outstanding relevance of medial temporal areas in the formation of associations in statistical learning paradigms"

Thank you for your constructive input. This section is purely speculative, and we do not aim to provide strong claims or expected results but solely point out potential future research directions.

- Authors should add a comparison of participants mini-TQ scores on both studies

We appreciate your input and added a comparison of mini TQ-scores between samples. For study 1, all subscales were included, however, we computed the comparison solely based on the items of the mini-TQ to increase comparability. The results were not significant, i.e., tinnitus distress values did not differ between studies.

Line 629-632:

“We additionally compared tinnitus distress values assessed by the mini-TQ (Goebel and Hiller, 1992) between study 1 and study 2 to detect potential differences between the samples, however, results of the Welch’s t-test were not significant with t(30.7)=1.27, p\=.214.”

- Authors should add significant level on Fig 6.B as in Fig 3.C, and a n.s on Fig 6.D

Thank you very much for your input, we added significance levels and a n.s. to the Figures 6B and 6D.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary of the work: In this work, Fruchard et. al. study the enzyme Tgt and how it modifies guanine in tRNAs to queuosine (Q), essential for Vibrio cholerae's growth under aminoglycoside stress. Q's role in codon decoding efficiency and its proteomic effects during antibiotic exposure is examined, revealing Q modification impacts tyrosine codon decoding and influences RsxA translation, affecting the SoxR oxidative stress response. The research proposes Q modification's regulation under environmental cues reprograms the translation of genes with tyrosine codon bias, including DNA repair factors, crucial for bacterial antibiotic response.

The experiments are well-designed and conducted and the conclusions, for the most part, are well supported by the data. However, a few clarifications will significantly strengthen the manuscript.

Thank you.

Major:

Figure S4 A-D. These growth curves are important data and should be presented in the main figures. Moreover, given that it is not possible to make a rsxA mutant, I wonder if it would be possible to connect rsx and tgt using the following experiment: expression of tgt results in resistance to TOB (in B), while expression of only rsx lower resistance to TOB (in D). Then simultaneous overexpression of both tgt/rsx in the WT strain should have either no effect on TOB resistance or increased resistance, relative to the WT. Perhaps the authors have done this, and if so, the data should be included as it will significantly strengthen their model.

We thank the reviewer for this suggestion, we have tried to overexpress both tgt and rsxA simultaneously. However, this appears to be toxic as cells form small colonies and cannot grow well in liquid. We think that the presence of 2 plasmids and corresponding selection antibiotics amplify the toxicity of overexpressing rsxA, and even tgt. In fact, it can be seen that tgt overexpression in WT is already slightly deleterious, in the absence of tobramycin (figure 1B).

Figure S4 - Is there a rationale for why it is possible to make rsx mutants in E. coli, but not in V. cholerae? For example, does E. coli have a second gene/protein that is redundant in function to rsxA, while V. cholerae does not? I think your data hint at this, since in the right panel growth data, your double mutant does not fully rescue back to rsx single mutant levels, suggesting another factor in tgt mutant also acts to lower resistance to TOB. If so, perhaps a line or two in text will be helpful for readers.

This point raised by the referee is an interesting one that we have also asked ourselves at multiple occasions. In fact, the Rsx operon is linked with oxidative stress and respiration. Vibrio cholerae and E. coli show differences on genes involved in these pathways. V. cholerae lacks the cyo/nuo respiratory complex genes, and does not encode a Suf operon. Moreover, deletion of the anaerobic respiration Frd pathway leads to strong decrease of V. cholerae growth even in aerobic conditions. (10.1128/spectrum.01730-23). We have previously also generally seen differences between the 2 species in response to stress (10.1128/AAC.01549-10) and the way they deal with ROS (10.1371/journal.pgen.1003421). Therefore, we think that the fact that rsx is essential in V. cholerae and not E. coli could either be due to the presence of an additional redundant pathway in E. coli as suggested by the referee, or to more general differences in respiration and treatment of ROS. We thank the referee for highlighting this and we have now included a comment about this in the manuscript.

- For growth curves in Figure 2 and relative comparisons like in Figure 5D and Figure S4 (and others in the paper), statistics and error bars, along with replicate information should be provided.

We had mentioned this in the methods section, we have now added the specific information also on figure legends.

- Figure 6A - Is the transcript fold change in linear or log? If linear, then tgt expression should not be classified as being upregulated in TOB. It is barely up by ~2-fold with TOB- 0.6....which is a mild phenotype, at best.

We think that 2-fold change of tgt expression can be sufficient to lead to changes in tRNA modification levels. We agree that this is a mild induction, we have thus changed “increase” to “mildly increase” in the results.  

- Line 779- 780: "This indicates that sub-MIC TOB possibly induces tgt expression through the stringent response activation." To me, the data presented in this figure, do not support this statement. The experiment is indirect.

We agree, we rephrased: “Tobramycin may induces tgt expression through stringent response activation or through an independent pathway. “

- Figure 3B and D. - These samples only have tobramycin, correct? The legend says both carbenicillin and tobramycin.

The legend is correct, samples also have carbenicillin because we are testing here the growth with 2 synonymous beta-lactamase genes in presence of beta-lactams.

- Figure 5. The color schemes in bars do not match up with the color scheme in cartoons below panels B and C. That makes it confusing to read. Please fix.

Fixed.

- A lot of abbreviations have been used. This makes reading a bit cumbersome. Ideally, less abbreviations will be used.

Fixed

Reviewer #2 (Public Review):

Fruchard et al. investigate the role of the queuosine (Q) modification of the tRNA (Q-tRNA) in the human pathogen Vibrio cholerae. First, the authors state that the absence of Q-modified tRNAs (tgt mutant) increases the translation of TAT codons and proteins with a high TAT codon bias. Second, the absence of Q increases rsxA translation, because rsxA gene has a high TAT codon bias. Third, increased RsxA in the absence of Q inhibits SoxR response, reducing resistance towards the antibiotic tobramycin (TOB). Authors also predict in silico which genes harbor a higher TAT bias and found that among them are some involved in DNA repair, experimentally observing that a tgt mutant is more resistant to UV than the wt strain. It is worth noting that authors employ a wide variety of techniques, both experimental and bioinformatic. However, some aspects of the work need to be clarified or reevaluated.

(1) The statement that the absence of Q increases the translation of TAT codons and proteins encoded by TAT-enriched genes presents the following problems that should be addressed:

(1.1) The increase in TAT codon translation in the absence of Q is not supported by proteomics, since there was no detected statistical difference for TAT codon usage in proteins differentially expressed. Furthermore, there are some problems regarding the statistics of proteomics. Some proteins shown in Table S1 have adjusted p-values higher than their pvalues, which makes no sense. Maybe there is a mistake in the adjusted p-value calculation.

We appreciate the reviewer’s thorough examination of our findings. In our study, we employed an adaptive Benjamini-Hochberg (BH) procedure to control the false discovery rate in our list of selected proteins, as explained in the Data Analysis part of the Proteomics MS and analysis part of our material and methods. The classical BH procedure (10.1111/j.2517-6161.1995.tb02031.x) calculates the 𝑚×𝑝(𝑗) adjusted p-value for the i-th ranked p-value as min where 𝑝(𝑗) is the j-th ranked pvalue and 𝑚 is the number of tests (e.g. number of proteins) (see 10.1021/acs.jproteome.7b00170 for details). Since m/j > 1 and 𝑝(𝑗) > 𝑝(𝑖) for 𝑗≥𝑚, it follows that for 𝑗≥i, resulting in adjusted p-values being higher or equal than the original p-values. Therefore, contrary to the reviewer's comment, it is a mathematical property that the adjusted p-value is greater than the original p-value when using the classical Benjamini-Hochberg procedure. 

However, we want to underline that we used an « adaptive » BH procedure, which calculates the adjusted p-value for the i-th ranked p-value as min , where 𝜋0 is an estimate of the proportion of true null hypotheses (see 10.1021/acs.jproteome.7b00170 for details). Indeed, the classical BH procedure makes the assumption that 𝜋0 \= 1, which is a strong assumption in MS-based proteomics context.  Consequently, the mathematical property that the adjusted p-value is greater than the original p-value does not always hold true in our approach (that depends also on the 𝜋0 parameter).

In addition, it is not common to assume that proteins that are quantitatively present in one condition and absent in another are differentially abundant proteins. Proteomics data software typically addresses this issue and applies some corrections. It would be advisable to review that.

We thank the reviewer for highlighting this point. Indeed, some software impute a random small value to replace missing values and then produces statistics based on this imputed data (10.1038/nmeth.3901). However, the validity and relevance of generating statistics in the absence of actual data is questionable. 

There are no universally accepted guidelines for handling this situation, and we believe it is more logical to set these values aside as potential interesting proteins. It is well-established that intensity values are often missing due to the detection limits of the spectrometer, suggesting that the missing values observed in several replicates of a condition are actually due to low values (see 10.1093/bioinformatics/btp362 and 10.1093/bioinformatics/bts193 for instance). It is thus logical to consider the associated proteins as potentially differentially abundant when comparing their complete absence in all replicates of one condition to their presence in several replicates of another condition.

(1.2) Problems with the interpretation of Ribo-seq data (Figure 4D). On the one hand, the Ribo-seq data should be corrected (normalized) with the RNA-seq data in each of the conditions to obtain ribosome profiling data, since some genes could have more transcription in some of the conditions studied. In other articles in which this technique is used (such as in Tuorto et al., EMBO J. 2018; doi: 10.15252/embj.201899777), it is interpreted that those positions in which the ribosome moves most slowly and therefore less efficiently translated), are the most abundant. Assuming this interpretation, according to the hypothesis proposed in this work, the fragments enriched in TAT codons should have been less abundant in the absence of Q-tRNA (tgt mutant) in the Rib-seq experiment. However, what is observed is that TAT-enriched fragments are more abundant in the tgt mutant, and yet the Ribo-seq results are interpreted as RNA-seq, stating that this is because the genes corresponding to those sequences have greater expression in the absence of Q. 

As recommended by the reviewer, we normalized the RiboSeq data with the RNAseq data to account for potential RNA variations. The updated Figure 4 demonstrates that this normalization does not alter our findings, confirming that variations at the RNAseq level do not contradict changes at the translational level. 

The reviewer's observation that pauses at TAT codons would lead to ribosome accumulation and subsequent categorization as "up" genes is accurate. We must emphasize, however, that this category of “up genes” is probably quite diverse. The effect of ribosome stalling at TAT codons on total mRNA ribosome occupancy is likely highly variable, depending on the location of the TAT codon(s) within the CDS and the gene's expression level. We therefore think that genes in the "Up" category mainly correspond to genes that are more translated because the impact of pausing at TAT codons is probably not strong enough. Note that unlike what is usually done in bacterial riboseq experiments, we did not use any antibiotics to artificially freeze the ribosomes.

On the other hand, it would be interesting to calculate the mean of the protein levels encoded by the transcripts with high and low ribosome profiling data.

While this is a common request, we believe that comparing RiboSeq and proteomics data is not particularly informative. RiboSeq data directly measures translation, while proteomics provides information about protein abundance at steady state, reflecting the balance between protein synthesis and degradation. Furthermore, the number of proteins detectable by mass spectrometry is significantly smaller than the number of genes quantified by RiboSeq. Given these factors, there is often a low correlation between translation and protein abundance, making a direct comparison less relevant 

(1.3) This statement is contrary to most previously reported studies on this topic in eukaryotes and bacteria, in which ribosome profiling experiments, among others, indicate that translation of TAT codons is slower (or unaffected) than translation of the TAC codons, and the same phenomenon is observed for the rest of the NAC/T codons. This is completely opposed to the results showed in Figure 4. However, the results of these studies are either not mentioned or not discussed in this work. Some examples of articles that should be discussed in this work:

- "Queuosine-modified tRNAs confer nutritional control of protein translation" (Tuorto et al., 2018; 10.15252/embj.201899777)

- "Preferential import of queuosine-modified tRNAs into Trypanosoma brucei mitochondrion is critical for organellar protein synthesis" (Kulkarni et al., 2021; doi:10.1093/nar/gkab567.

- "Queuosine-tRNA promotes sex-dependent learning and memory formation by maintaining codonbiased translation elongation speed" (Cirzi et al., 2023; 10.15252/embj.2022112507)

- "Glycosylated queuosines in tRNAs optimize translational rate and post-embryonic growth" (Zhao et al., 2023; 10.1016/j.cell.2023.10.026)

- "tRNA queuosine modification is involved in biofilm formation and virulence in bacteria" (Diaz-Rullo and Gonzalez-Pastor, 2023; doi: 10.1093/nar/gkad667). In this work, the authors indicate that QtRNA increases NAT codon translation in most bacterial species. Could the regulation of TAT codonenriched proteins by Q-tRNAs in V. cholerae an exception? In addition, authors use a bioinformatic method to identify genes enriched in NAT codons similar to the one used in this work, and to find in which biological process are involved the genes whose expression is affected by Q-tRNAs (as discussed for the phenotype of UV resistance). It will be worth discussing all of this.

Thank you for detailed suggestions, we agree that this discussion was missing and this comment gives us a chance to address that in the revised version of the manuscript.

About the references above suggested by the referee, 4 of these papers were not mentioned in our manuscript, these were published while our manuscript was previously in review and we realize we have not cited them in the latest version of our manuscript. We thank the referee for highlighting this. We have now included a discussion about this. 

We included the following in the discussion:

“However, the opposite codon preference was shown in E. coli {Diaz-Rullo, 2023 #1888}. In eukaryotes also, several recent studies indicate slower translation of U-ending codons in the absence of Q34 {Cirzi, 2023 #1887;Kulkarni, 2021 #1886;Tuorto, 2018 #1268}. It’s important to note here, that in V. cholerae ∆tgt, increased decoding of U-ending codons is observed only with tyrosine, and not with the other three NAC/U codons (Histidine, Aspartate, Asparagine). This is interesting because it suggests that what we observe with tyrosine may not adhere to a general rule about the decoding efficiency of U- or C-ending codons, but instead seems to be specific to Tyr tRNAs, at least in the context of V. cholerae. Exceptions may also exist in other organisms. For example, in human cells, queuosine increases efficiency of decoding for U- ending codons and slows decoding of C- ending codons except for AAC {Zhao, 2023 #1889}. In this case, the exception is for tRNA Asparagine. Moreover, in mammalian cells {Tuorto, 2018 #1268}, ribosome pausing at U-ending codons is strongly seen for Asp, His and Asn, but less with Tyr. In Trypanosoma {Kulkarni, 2021 #1886}, reporters with a combination of the 4 NAC/NAU codons for Asp, Asn, Tyr, His have been tested, showing slow translation at U- ending version of the reporter in the absence of Q, but the effect on individual codons (e.g. Tyr only) is not tested. In mice {Cirzi, 2023 #1887}, ribosome slowdown is seen for the Asn, Asp, His U-ending codons but not for the Tyr U-ending codon. In summary, Q generally increases efficiency of U- ending codons in multiple organisms, but there appears to be additional unknown parameters which affect tyrosine UAU decoding, at least in V. cholerae. Additional factors such as mRNA secondary structures or mistranslation may also contribute to the better translation of UAU versions of tested genes. Mistranslation could be an important factor. If codon decoding fidelity impacts decoding speed, then mistranslation could also contribute to decoding efficiency of Tyr UAU/UAC codons and proteome composition.”

(1.4) It is proposed that the stress produced by the TOB antibiotic causes greater translation of genes enriched in TAT codons. 

Actually, it’s the opposite because in presence of TOB, in the wt, tgt would be induced leading to more Q on tRNA-Tyr and less translation of TAT.

On the one hand, it is shown that the GFP-TAT version (gene enriched in TAT codons) and the RsxATAT-GFP protein (native gene naturally enriched in TAT) are expressed more, compared to their versions enriched in TAC in a tgt mutant than in a wt, in the presence of TBO (Fig. 5C). 

Figure 5C shows relative fluorescence, ie changes of fluorescence in delta-tgt compared to WT. So it’s not necessarily more expressed but “more increased”

However, in the absence of TOB, and in a wt context, although the two versions of GFP have a similar expression level (Fig. 3SD), the same does not occur with RsxA, whose RsxA-TAT form (the native one) is expressed significantly more than the RsxA-TAC version (Fig. 3SA). How can it be explained that in a wt context, in which there are also tRNA Q-modification, a gene naturally enriched in TAT is translated better than the same gene enriched in TAC?

We thank the referee for this question based on careful assessment of our data. We agree, there appears to be significantly more RsxA-TAT in WT than RsxA-TAC. This could be due to other effects such as secondary structure formation on mRNA when the wt RsxA is recoded with TAC codons. This does not hinder the conclusion that the translation of the TAT version is increased in delta-tgt compared to WT.  

It would be expected that in the presence of Q-tRNAs the two versions would be translated equally (as happens with GFP) or even the TAT version would be less translated. On the other hand, in the presence of TOB the fluorescence of WT GFP(TAT) is higher than the fluorescence of WT GFP(TAC) (Figure S3E) (mean fluorescence data for RsxA-GFP version in the presence of TOB is not shown). These results may indicate that the apparent better translation of TAT versions could be due to indirect effects rather from TAT codon translation.

This is now mentioned in the manuscript

“We cannot exclude, however, that additional factors such as mRNA secondary structures also contributes to the better translation of UAU versions of tested genes. “

(2) Another problem is related to the already known role of Q in prevention of stop codon readthrough, which is not discuss at all in the work. In the absence of Q, stop codon readthrough is increased. In addition, it is known that aminoglycosides (such as tobramycin) also increase stop codon readthrough ("Stop codon context influences genome-wide stimulation of termination codon readthrough by aminoglycosides"; Wanger and Green, 2023; 10.7554/eLife.52611). Absence of Q and presence of aminoglycosides can be synergic, producing devastating increases in stop codon readthrough and a large alteration of global gene expression. All of these needs to be discussed in the work. Moreover, it is known that stop codon readthrough can alter gene expression and mRNA sequence context all influence the likelihood of stop codon readthrough. Thus, this process could also affect to the expression of recoded GFP and RsxA versions.

We included the following in the revised version of the manuscript (results):

“Q modification impacts decoding fidelity in V. cholerae.

To test whether a defect in Q34 modification influences the fidelity of translation in the presence and absence of tobramycin, previously developed reporter tools were used (Fabret & Namy, 2021), to measure stop codons readthrough in V. cholerae ∆tgt and wild-type strains. The system consists of vectors containing readthrough promoting signals inserted between the lacZ and luc sequences, encoding β-galactosidase and luciferase, respectively. Luciferase activity reflects the readthrough efficiency, while β-galactosidase activity serves as an internal control of expression level, integrating a number of possible sources of variability (plasmid copy number, transcriptional activity, mRNA stability, and translation rate).  We found increased readthrough at stop codons UAA and to a lesser extent at UAG for ∆tgt, and this increase was amplified for UAG in presence of tobramycin (Fig. S2, stop readthrough). In the case of UAA, tobramycin appears to decrease readthrough, this may be artefactual, due to the toxic effect of tobramycin on ∆tgt.

Mistranslation at specific codons can also impact protein synthesis. To further investigate mistranslation levels by tRNATyr in WT and ∆tgt, we designed a set of gfp mutants where the codon for the catalytic tyrosine required for fluorescence (TAT at position 66) was substituted by nearcognate codons (Fig. S2). Results suggest that in this sequence context, particularly in the presence of tobramycin, non-modified tRNATyr mistakenly decodes Asp GAC, His CAC and also Ser UCC, Ala GCU, Gly GGU, Leu CUU and Val GUC codons, suggesting that Q34 increases the fidelity of tRNATyr. 

In parallel, we replaced Tyr103 of the β-lactamase described above, with Asp codons GAT or GAC. The expression of the resulting mutant β-lactamase is expected to yield a carbenicillin sensitive phenotype. In this system, increased tyrosine misincorporation (more mistakes) by tRNATyr at the mutated Asp codon, will lead to increased synthesis of active β-lactamase, which can be evaluated by carbenicillin tolerance tests. As such, amino-acid misincorporation leads here to phenotypic (transient) tolerance, while genetic reversion mutations result in resistance (growth on carbenicillin). The rationale is summarized in Fig. 3C. When the Tyr103 codon was replaced with either Asp codons, we observe increased β-lactamase tolerance (Fig. 3D, left), suggesting increased misincorporation of tyrosine by tRNATyr at Asp codons in the absence of Q, again suggesting that Q34 prevents misdecoding of Asp codons by tRNATyr.

In order to test any effect on an additional tRNA modified by Tgt, namely tRNAAsp, we mutated the Asp129 (GAT) codon of the β-lactamase. When Asp129 was mutated to Tyr TAT (Fig. 3D, right), we observe reduced tolerance in ∆tgt, but not when it was mutated to Tyr TAC, suggesting less misincorporation of aspartate by tRNAAsp at the Tyr UAU codon in the absence of Q. In summary, absence of Q34 increases misdecoding by tRNATyr at Asp codons, but decreases misdecoding by tRNAAsp at Tyr UAU. 

This supports the fact that tRNA Q34 modification is involved in translation fidelity during antibiotic stress, and that the effects can be different on different tRNAs, e.g. tRNATyr and tRNAAsp tested here.”

Added figures: Figure S2, Figure 3CD

(3) The statement about that the TOB resistance depends on RsxA translation, which is related to the presence of Q, also presents some problems:

(3.1) It is observed that the absence of tgt produces a growth defect in V. cholerae when exposed to TOB (Figure 1A), and it is stated that this is mediated by an increase in the translation of RsxA, because its gene is TAT enriched. However, in Figure S4F, it is shown that the same phenotype is observed in E. coli, but its rsxA gene is not enriched in TAT codons. Therefore, the growth defect observed in the tgt mutant in the presence of TOB may not be due to the increase in the translation of TAT codons of the rsxA gene in the absence of Q. This phenotype is very interesting, but it may be related to another molecular process regulated by Q. Maybe the role of Q in preventing stop codon readthrough is important in this process, reducing cellular stress in the presence of TOB and growing better.

FigS4F (now figure 5D) shows that rsxA can be toxic during growth in presence of tobramycin, but it does not show that rsxA translation is increased in E. coli in delta-tgt. However, we agree with the referee that there are probably additional processes regulated by Q which are also involved in the response to TOB stress. We already had mentioned this briefly in the discussion (“Note that, our results do not exclude the involvement of additional Q-regulated MoTTs in the response to sub-MIC TOB, since Q modification leads to reprogramming of the whole proteome. “), we further discussed it as follows:

“As a consequence, transcripts with tyrosine codon usage bias are differentially translated. One such transcript codes for RsxA, an anti-SoxR factor. SoxR controls a regulon involved in oxidative stress response and sub-MIC aminoglycosides trigger oxidative stress in V. cholerae{Baharoglu, 2013 #720}, pointing to an involvement of oxidative stress response in the response to sub-MIC tobramycin stress.

A link between Q34 and oxidative stress has also been previously found in eukaryotic organisms {Nagaraja, 2021 #1466}. Note that our results do not exclude the involvement of additional Qregulated translation of other transcripts in the response to tobramycin. Q34 modification leads to reprogramming of the whole proteome, not only for other transcripts with codon usage bias, but also through an impact on the levels of stop codon readthrough and mistranslation at specific codons, as supported by our data.”

(3.2) All experiments related to the effect of Q on the translation of TAT codons have been performed with the tgt mutant strain. Considering that the authors have a pSEVA-tgt plasmid to overexpress this gene, they would have to show whether tgt overexpression in a wt strain produces a decrease in the translation of proteins encoded by TAT-enriched genes such as RsxA. This experiment would allow them to conclude that Q reduces RsxA levels, increasing resistance to TOB.

We agree that this would be interesting to test, however, as it can be seen in figure 1B, delta-tgt pSEVAtgt (complemented strain) grows better than WT pSEVA-tgt (tgt overexpression). In fact, overexpression of tgt negatively impacts cell growth and yield smaller colonies, especially when cells carry a second plasmid (e.g with gfp constructs). We have also seen this with other RNA modification gene overexpressions in the lab (unpublished). We believe that the expression of tgt is tuned and since overexpression affects fitness, it is generally difficult to conduct experiments with overexpression plasmid for RNA modifications.  Nevertheless, we have done the experiment (with slow growing bacteria) and when we normalize expression of gfp in the presence of tgt overexpressing plasmid to the condition with no plasmid, we see little (1.5 fold) or no effect of tgt overexpression on fluorescence (see graph below). This is probably due to a toxic effect of ooverexpression and we do not believe these results are biologically relevant. 

Author response image 1.

(3.3) On the other hand, Fig. 1B shows that when the wt and tgt strains compete, both overexpressing tgt, the tgt mutant strain grows better in the presence of TOB. This result is not very well understood, since according to the hypothesis proposed, the absence of modification by Q of the tRNA would increase the translation of genes enriched in TAT, therefore, a strain with a higher proportion of Q-modified tRNAs as in the case of the wt strain overexpressing tgt would express the rsxA gene less than the tgt strain overexpressing tgt and would therefore grow better in the presence of TOB. For all these reasons, it would be necessary to evaluate the effect of tgt overexpression on the translation of RsxA.

See our answer above about negative effect of tgt overexpression.

(3.4) According to Figure 1I, the overexpression of tRNA-Tyr(GUA) caused a better growth of tgt mutant in comparison to WT. If the growth defect observed in tgt mutant in the presence of TOB is due to a better translation of the TAT codons of rsxA gene, the overexpression of tRNA-Tyr(GUA) in the tgt mutant should have resulted in even better RsxA translation a worse growth, but not the opposite result.

We agree, we think that rsxA is not the only factor responsible for growth defect of tgt in presence of TOB (as now further discussed in the discussion). Overexpression of tRNAtyr possibly changes the equilibrium between the decoding of TAC vs TAT and may restore translation of TAC enriched genes. As also suggested by rev3, we have measured decoding reporters for TAT/TAC while overexpressing tTNA-tyr. This is now added to the results in fig S2C and the following:

“We also tested decoding reporters for TAT/TAC in WT and ∆tgt overexpressing tRNATyr in trans (Fig. S1C). The presence of the plasmid (empty p0) amplified differences between the two strains with decreased decoding of TAC (and increased TAT, as expected) in ∆tgt compared to WT. Overexpression of tRNATyrGUA did not significantly impact decoding of TAT and increased decoding of TAC, as expected. Since overexpression of tRNATyrGUA rescues ∆tgt in tobramycin (Fig. 1I) and facilitates TAC decoding, this suggests that issues with TAC codon decoding contribute to the fitness defect observed in ∆tgt upon growth with tobramycin. Overexpression of tRNATyrAUA increased decoding of TAT in WT but did not change it in ∆tgt where it is already high. Unexpectedly, overexpression of tRNATyrAUA also increased decoding of TAC in WT. Thus, overexpression of tRNATyrAUA possibly changes the equilibrium between the decoding of TAC vs TAT and may restore translation of TAC enriched transcripts.” 

Added figure: figure S1C

(4) It cannot be stated that DNA repair is more efficient in the tgt mutant of V. cholerae, as indicated in the text of the article and in Fig 7. The authors only observe that the tgt mutant is more resistant to UV radiation and it is suggested that the reason may be TAT bias of DNA repair genes. To validate the hypothesis that UV resistance is increased because DNA repair genes are TAT biased, it would be necessary to check if DNA repair is affected by Q. UV not only produces DNA damage, but also oxidative stress. Therefore, maybe this phenotype is due to the increase in proteins related to oxidative stress controlled by RsxA, such as the superoxide dismutase encoded by sodA. It is also stated that these repair genes were found up for the tgt mutant in the Ribo-seq data, with unchanged transcription levels. Again, it is necessary to clarify this interpretation of the Ribo-seq data, since the fact that they are more represented in a tgt mutant perhaps means that translation is slower in those transcripts. Has it been observed in proteomics (wt vs tgt in the absence of TOB) whether these proteins involved in repair are more expressed in a tgt mutant?

We agree that our results do not directly show that DNA repair is more efficient, but that delta-tgt responds better to UV. This has been modified in the manuscript. About oxidative stress, we did not see a better or worse response to H202 of delta-tgt. Moreover, since we see better response of deltatgt  to UV only in V. cholerae and not in E. coli, we did not favor the hypothesesi of response to stressox. In proteomics, we do not detect changes for DNA repair genes except for RuvA which is more abundant in delta-tgt. We have toned down the statement about DNA repair in the paper.

(5) The authors demonstrate that in E. coli the tgt mutant does not show greater resistance to UV radiation (Fig. 7D), unlike what happens in V. cholerae. It should be discussed that in previous works it has been observed that overexpression in E. coli of the tgt gene or the queF gene (Q biosynthesis) is involved in greater resistance to UV radiation (Morgante et al., Environ Microbiol, 2015 doi: 10.1111/1462-2920.12505; and Díaz-Rullo et al., Front Microbiol. 2021 doi: 10.3389/fmicb.2021.723874). As an explanation, it was proposed (Diaz-Rullo and Gonzalez-Pastor, NAR 2023 doi: 10.1093/nar/gkad667) that the observed increase in the capacity to form biofilms in strains that overexpress genes related to Q modification of tRNA would be related to this greater resistance to UV radiation.

We now mention the previous observations suggesting a link between tgt and UV. We thank the referee for the reference which we had overlooked. Note that in the case of our experiments, all cultures are in planktonic form and are not allowed to form biofilms. We thus prefer not to biofilmlinked processes in this study.

Reviewer #3 (Public Review):

Summary:

In this manuscript the authors begin with the interesting phenotype of sub-inhibitory concentrations of the aminoglycoside tobramycin proving toxic to a knockout of the tRNA-guanine transglycosylase (Tgt) of the important human pathogen, Vibrio cholerae. Tgt is important for incorporating queuosine (Q) in place of guanosine at the wobble position of GUN codons. The authors go on to define a mechanism of action where environmental stressors control expression of tgt to control translational decoding of particularly tyrosine codons, skewing the balance from TAC towards TAT decoding in the absence of the enzyme. The authors use advanced proteomics and ribosome profiling to reveal that the loss of tgt results in increased translation of proteins like RsxA and a cohort of DNA repair factors, whose genes harbor an excess of TAT codons in many cases. These findings are bolstered by a series of molecular reporters, mass spectrometry, and tRNA overexpression strains to provide support for a model where Tgt serves as a molecular pivot point to reprogram translational output in response to stress.

Strengths:

The manuscript has many strengths. The authors use a variety of strains, assays, and advanced techniques to discover a mechanism of action for Tgt in mediating tolerance to sub-inhibitory concentrations of tobramycin. They observe a clear phenotype for a tRNA modification in facilitating reprogramming of the translational response, and the manuscript certainly has value in defining how microbes tolerate antibiotics.

We thank the referee for their time and comments. 

Weaknesses:

The conclusions of the manuscript are mostly very well-supported by the data, but in some places control experiments or peripheral findings cloud precise conclusions. Some additional clarification, discussion, or even experimental extension could be useful in strengthening these areas.

(1) The authors have created and used a variety of relevant molecular tools. In some cases, using these tools in additional assays as controls would be helpful. For example, testing for compensation of the observed phenotypes by overexpression of the Tyrosine tRNA(GUA) in Figure 2A with the 6xTAT strain, Figure 5C with the rxsA-GFP fusion, and/or Figure 7B with UV stress would provide additional information of the ability of tRNA overexpression to compensate for the defect in these situations.

Thank you for the suggestions. Since overexpression of tRNA tyr is not expected to decrease decoding of TAT, we do not necessarily expect any effect for UV and rsxA expression. Overexpression of tRNA_GUA restores fitness of delta-tgt in TOB, but this is probably independent of RsxA. As ref2 also suggested above, we included in the discussion that the effect seen in delta-tgt with TOB is not only due to RsxA expression but also additional processes. However, these suggestions are interesting and we performed the following experiments in order to have an answer for these questions: 

- “testing for compensation of the observed phenotypes by overexpression of the Tyrosine tRNA(GUA) in Figure 2A with the 6xTAT strain”: 

This is now included in figure S2C and results as follows: 

“We also tested decoding reporters for TAT/TAC in WT and ∆tgt overexpressing tRNA-Tyr in trans (Fig. S1C). The presence of the plasmid amplified differences between the two strains with decreased decoding of TAC (and increased TAT, as expected) in ∆tgt with empty plasmid compared to WT. Overexpression of tRNA_TyrGUA did not significantly impact decoding of TAT and increased decoding of TAC as expected. Since overexpression of tRNA_TyrGUA rescues ∆tgt in tobramycin (Fig. 1I) and facilitates TAC decoding, this suggests that issues with TAC codon decoding contribute to the fitness defect observed in ∆tgt upon growth with tobramycin. Overexpression of tRNA_TyrAUA increased decoding of TAT in WT but did not change it in ∆tgt where it is already high. Interestingly, overexpression of TyrAUA also increased decoding of TAC in WT. Thus, overexpression of tRNA_TyrAUA possibly changes the equilibrium between the decoding of TAC vs TAT and may restore translation of TAC enriched transcripts. “  

-  Figure 5C with the rxsA-GFP fusion: 

When we overexpress tRNA_GUA, rsxA fluorescence is 2-fold higher in delta-tgt compared to wt. However, the fluorescence is highly decreased compared to the condition with no tRNA overexpression. While we are not sure whether this apparent decrease is a technical issue or not (e.g. due to the presence of additional plasmid), we prefer not to further explore this in this manuscript. Note that we could not obtain delta-tgt strain carrying both plasmids expressing tRNA_GUA and rsxA, suggesting toxic overproduction of rsxA in this context.

Author response image 2.

- Figure 7B with UV stress: 

Here again, delta-tgt overexpressing tRNA_GUA is still more UV resistant than WT overexpressing tRNA_GUA.

Author response image 3.

(2) The authors present a clear story with a reprogramming towards TAT codons in the knockout strain, particularly regarding tobramycin treatment. The control experiments often hint at other codons also contributing to the observed phenotypes (e.g., His or Asp), yet these effects are mostly ignored in the discussion. It would be helpful to discuss these findings at a minimum in the discussion section, or possibly experimentally address the role of His or Asp by overexpression of these tRNAs together with Tyrosine tRNA(GUA) in an experiment like that of Figure 1I to see if a more "wild type" phenotype would present. In fact, the synergy of Tyr, His, and/or Asp codons likely helps to explain the effects observed with the DNA repair genes in later experiments.

We thank the referee for the suggestion. We agree that there could be synergies between these codons, and that’s probably why proteomics data does not clearly reflect tyrosine codons usage bias. This is now further discussed in the ideas and speculation section. 

Moreover, we have added Figure S3G and the following result:

“Since not all TAT biased proteins are found to be enriched in ∆tgt proteomics data, the sequence context surrounding TAT codons could affect their decoding. To illustrate this, we inserted after the gfp start codon, various tyrosine containing sequences displayed by rsxA (Fig. S3G). The native tyrosines were all TAT codons, our synthetic constructs were either TAT or TAC, while keeping the remaining sequence unchanged.  We observe that the production of GFP carrying the TEYTATLLL sequence from RsxA is increased in Δtgt compared to WT, while it is unchanged with TEYTACLLL. However, production of the GFP with the sequences LYTATRLL/LYTACRLL and EYTATLR/ EYTACLR was not unaffected (or even decreased for the latter) by the absence of tgt. Overall, our results demonstrate that RsxA is upregulated in the ∆tgt strain at the translational level, and that proteins with a codon usage bias towards tyrosine TAT are prone to be more efficiently translated in the absence of Q modification, but this is also dependent on the sequence context. “

(3) Regarding Figure 6D, the APB northern blot feels like an afterthought. It was loaded with different amounts of RNA as input and some samples are repeated three times, but Δcrp only once. Collectively, it makes this experiment very difficult to assess.

A different amount of RNA was used only for ∆tgt in which we have only one band because of the absence of modification. For all the other conditions, the same amount of RNA was used (0.9 µg). Additional replicates of crp were in an additional gel but only a representative gel was shown in the manuscript. This is now specified in the legend.

We also attach below the picture of the gel with total RNA (syber Gold labelling of total RNA), where it can be seen that the lanes contain an equivalent quantity of RNA, except for ∆tgt.

Author response image 4.

Minor Points:

(3) Fig S2B, do the authors have a hypothesis why the Asp and Phe tRNAs lead to a growth decrease in the untreated samples? It appears like Phe(GAA) partially compensates for the defect.

Yes we agree, at this stage we do not have any satisfactory answer for this unfortunately. This would be interesting to study further but this is beyond the scope of the present study.

(5) Lines 655 to 660 seem more appropriate as speculation in the discussion rather than as a conclusion in the results, where no direct experiments are performed. The authors might take advantage of the "Ideas and Speculation" section that eLife allows.

Thank you very much for this suggestion, we added this section to the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor.

- Figure 6 - Fonts on several mutants is different size/type. fixed

- What is the Pm promoter. Please expand and give enough details so reader can follow. Especially as it is less used in V. cholerae (typical being pBAD or pTAC promoters). done

- Spacing where references are inserted should be checked. done

- Line 860-863 - "V. cholerae's response to sub-MIC antibiotic stress is transposable to other Gramnegative pathogens" . This reads awkard. Consider rephrasing. done

- Figure 7 - Text in A and C is very small and is very hard to read. Font for tgt is different.

Fixed. Tgt is in italics.

Reviewer #2 (Recommendations For The Authors):

As specified in the public review, more evidence would be necessary to affirm that tRNAs not modified by Q have a greater preference for translating TAT codons, since there are several previous studies in which it is shown that Q-tRNAs have a greater preference for NAT codons (including TAT). For example, it is suggested to explore what happens with other recoded genes (enriched in TAT or TAC) if there is a high level of Q-tRNAs (overexpression of tgt in a wt context). It is also necessary to clarify how to interpret the Ribo-seq results, which apparently is different from how they have been interpreted in other studies.

Please see above our responses and changes made to the manuscript.

Minor corrections

In Figure 8, replace "Epitranscriptomic adapation to stress" with "Epitranscriptomic adaptation to stress".

Fixed, thank you for noticing!

Reviewer #3 (Recommendations For The Authors):

(1) Lines 48-50, and 110 to 112, the authors have a nice mechanism and story, yet the lines mentioned feel very qualified (e.g., "possibly", "plausibly") and lead to the abstract hiding the value and major conclusions of the study. The authors could consider to revise or even remove these lines to focus on the take-home message in the abstract and end of introduction/discussion. 

Thank you for this comment, we modified the text.  

(2) Additional description for the samples in the results section for Figure 1 would be helpful to the reader.

Done

(3) Figure S1, the line of experiments with rluF is interesting, but in the end the choice seems a little random. Have the authors assessed knockouts of other modifications on the ASL for effects? Since the modification is not well characterized in V. cholerae according to the authors, it might make sense to save this for a future paper.

We removed S1, as we agree that this experiment does not really add something to the paper.

(4) Line 334 and 353 are redundant.

Fixed

(5) It is likely beyond the scope of the study, but it would strengthen the paper to repeat Figure 3 with His and/or Asp based on the findings of 2C and 4E to better understand the contribution of His and Asp to Q biology.

We repeated figure 3 with Asp. Based on Fig 2C (less efficient decoding of GAC in deta-tgt in TOB) and 4E (positive GAT codon bias in proteins up in riboseq in delta-tgt TOB), we would expect that beta-lactamase with asp GAC would be less efficiently decoded than GAT in delta-tgt. 

This was added to the manuscript

“Like Tyr103, Asp129 was shown to be important for resistance to β-lactams (Doucet et al., 2004; Escobar et al., 1994; Jacob et al., 1990). When we replaced the native Asp129 GAT with the synonymous codon Asp129 GAC, the GAC version did not appear to produce functional β-lactamase in ∆tgt (Fig. 3B), suggesting increased mistranslation or inefficient decoding of the GAC codon by tRNAAsp in the absence of Q. Decoding of GAT codon was also affected in ∆tgt in the presence of tobramycin.”

Added figure: Figure 3B

(6) The authors could consider replacing 5D with S4A-D, which is easier to understand in our opinion.

Done

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This article identifies ADGR3 as a candidate GPCR for mediating beige fat development. The authors use human expression data from Human Protein Atlas and Gtex databases and combine this with experiments performed in mice and a murine cell line. They refer to a GPCR bioactivity screening tool PRESTO-Salsa, with which it was found that Hesperetin activates ADGR3. From their experiments, authors conclude that Hesperetin activates ADGR3, inducing a Gs-PKA-CREB axis resulting in adipose thermogenesis.

Strengths:

The authors analyze human data from public databases and perform functional studies in mouse models. They identify a new GPCR with a role in thermogenic activation of adipocytes.

Considerations:

Selection of ADGRA3 as a candidate GPCR relevant for mediating beiging in humans:

The authors identify GPCRs that are expressed more highly in murine iBAT compared to iWAT in response to cold and assess which of these GPCRs are expressed in human subcutaneous or visceral adipocytes. Although this strategy will identify GPCRs that are expressed at higher levels in brown fat compared to beige and thus possibly more active in thermogenic function, the relevance in choosing GPCRs that also are expressed in unstimulated human white adipocytes should be considered. Thermogenic activity is not normally present in human white adipocytes. It would have strengthened the GPCR selection if the authors instead had assessed the intersection with human brown adipocytes that were activated with norepinephrine.

We appreciate your constructive feedback and believe that by adopting this refined strategy, we will strengthen our selection of GPCRs related to adipose thermogenesis in other ongoing studies. We look forward to continuing our research in this area and contributing to the understanding of adipose thermogenesis and its potential therapeutic applications. Thank you once again for your valuable input. 

Strategy to investigate the role of ADGRA3 in WAT beiging:

Having identified ADGRA3 as their candidate receptor, the authors investigated the receptor in mouse models, the murine inguinal adipocyte cell line 3T3 and in human subcutaneous adipose progenitors (HAdsc) differentiated in vitro. Calling the human cells "beige" is a stretch as these cells are derived from a white adipose depot. The authors do observe regulation in UCP1 and abundance of mitochondria following modification of ADGRA3 in the cells. However, in future studies, it should be considered if the receptor rather plays a role in differentiation per se, and perhaps not specifically in thermogenic differentiation/activity.

Regarding the reviewer's suggestion to consider whether ADGRA3 plays a role in differentiation per se, rather than specifically in thermogenic differentiation/activity, we acknowledge that this is an important consideration. Our current studies have focused on the role of ADGRA3 in regulating UCP1 expression and mitochondrial abundance, which are hallmarks of adipose thermogenic activity. However, we recognize that ADGRA3 may also have broader roles in adipocyte differentiation and function that are not limited to thermogenesis.

To address this point, in future studies, we plan to conduct additional experiments to investigate the potential role of ADGRA3 in adipocyte differentiation, including its effects on the expression of markers of adipocyte differentiation and its impact on adipocyte metabolism and function. These studies will provide further insights into the mechanisms by which ADGRA3 regulates adipocyte biology.

According to the Human Protein Atlas and Gtex databases, ADGRA3 is not only expressed in adipocytes, but also in other tissues and cell types. The authors address this by measuring the expression in a panel of these tissues, demonstrating a knockdown not only in the adipose tissue, but also in the liver and less pronounced in the muscle (Figure S2). It should thus be emphasized that the decreased TG levels in serum and liver in the mice might in fact depend on Adgra3 overexpression in the liver. Even though this might not have been the purpose of the experiment, it is important to highlight this as it could serve as hypothesis building for future studies of the function of this receptor.

Thank you for your thoughtful comments and feedback. We appreciate the insight provided by the Human Protein Atlas and Gtex databases regarding the tissue distribution of ADGRA3. We fully acknowledge that the decreased TG levels observed in both the serum and liver of the mice might be linked to the overexpression of Adgra3 in the liver.

Although this was not the primary objective of our experiment, we agree that this observation is worth highlighting as it could serve as a basis for future hypothesis-driven research on the functional role of ADGRA3 in different tissues. In light of your comments, we emphasized this potential link between Adgra3 overexpression in the liver and reduced TG levels in discussion, as follows.

“…the precise mechanisms underlying the influence of on adipose thermogenesis. Furthermore, it is crucial to highlight that the observed decrease in TG levels in both serum and liver (Figure 4-figure supplement 2C-D) might be attributed to the significant increase in Adgra3 expression in the liver, which is a consequence of the nanoparticle-mediated overexpression of Adgra3. While the exact mechanism remains to be fully elucidated, this correlation suggests a potential link between Adgra3 overexpression in the liver and reduced TG levels in the serum. We will employ more sophisticated models in subsequent studies to further…”

Reviewer #3 (Public Review):

Summary:

The manuscript by Zhao et al. explored the function of adhesion G protein-coupled receptor A3 (ADGRA3) in thermogenic fat biology.

Strengths:

Through both in vivo and in vitro studies, the authors found that the gain function of ADGRA3 leads to browning of white fat and ameliorates insulin resistance.

Weaknesses:

There are several lines of weak methodologies such as using 3T3-L1 adipocytes and intraperitoneal(i.p.) injection of virus. Moreover, as the authors stated that ADGRA3 is constitutively active, how could the authors then identify a chemical ligand?

Comments on revised version:

The revised manuscript by Zhao et al. has limited improvement. The authors refused to perform revised experiments using primary cultures even though two reviewers pointed out the same weakness (3T3-L1 adipocytes are unsuitable). Using infrared thermography to measure body temperature is also problematic.

Thanks for your comments. We regret that human adipocytes induced from human adipose-derived stem cells (hADSCs) were not recognized as primary cultures by multiple reviewers. Therefore, we have included relevant experimental results of mouse primary adipocytes induced from stromal vascular fraction (SVF) in Figure 8E-H as a supplement. The thermal imaging device was used to measure the temperature of BAT, while the body temperature was measured at 9:00 using a rectal probe connected to a digital thermometer.

Author response:

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

Reviewer #1 (Public review):

Summary:

This paper presents a data processing pipeline to discover causal interactions from time-lapse imaging data, and convicingly illustrates it on a challenging application for the analysis of tumor-on-chip ecosystem data. The core of the discovery module is the original tMIIC method of the authors, which is shown in supplementary material to compare favourably to two state-of-the-art methods on synthetic temporal data on a 15 nodes network.

Strengths:

This paper tackles the problem of learning causal interactions from temporal data which is an open problem in presence of latent variables. The core of the method tMIIC of the authors is nicely presented in connection to Granger- Schreiber causality and to the novel graphical conditions used to infer latent variables and based on a theorem about transfer entropy. tMIIC compares favourably to PC and PCMCI+ methods using different kernels on synthetic datasets generated from a network of 15 nodes. A full application to tumor-onchip cellular ecosystems data including cancer cells, immune cells, cancer-associated fibroblasts, endothelial cells and anti cancer drugs, with convincing inference results with respect to both known and novel effects between those components and their contact.

The code and dataset are available online for the reproducibility of the results.

We thank Reviewer #1 for highlighting the main results and strengths of our paper, as well as, for his/her recommendations below to further improve the manuscript.

Weaknesses:

The references to ”state-of-the-art methods” concerning the inference of causal networks should be more precise by giving citations in the main text, and better discussed in general terms, both in the first section and in the section of presentation of CausalXtract. It is only in the legend of the figures of the supplementary material that we get information. Of course, comparison on our own synthetic datasets can always be criticized but this is rather due to the absence of common benchmark and I would recommend the authors to explicitly propose their datasets as benchmark to the community.

Following Reviewer #1’s suggestion, we now compare tMIIC’s performance to other state-of-the-art causal discovery methods for time series data in the main text and in a new Figure 2. This Figure 2 also highlights the relation between graph-based causal discovery methods for time series data and Granger-Schreiber temporal causality, as discussed in more details in Methods (Theorem 1).

We also agree about the importance of sharing benchmark datasets with the community. This is the reason why we provide the dynamical equations of the 15-node benchmarks in Supplementary Tables 1 & 2, so that anyone can generate equivalent time series datasets of any desired length.

Reviewer #2 (Public review):

Summary:

The authors propose a methodology to perform causal (temporal) discovery. The approach appears to be robust and is tested in the different scenarios: one related with live-cell imaging data, and another one using synthetic (mathematically defined) time series data. They compare the performance of their findings against another well-know method by using metrics like F-score, precision and recall,

Strengths:

Performance, robustness, the text is clear and concise, The authors provide the code to review.

We thank Reviewer #2 for his/her positive assessment of our work and the suggestions below to improve the manuscript.

Weaknesses:

One concern could be the applicability of the method in other areas like climate, economy. For those areas, public data are available and might be interesting to test how the method performs with this kind of data.

While our main expertise concerns the analysis of biological and biomedical data, we agree that tMIIC (which is included in MIIC R package) could in principle be applied to other areas, like climate, economy.

We have not included benchmarks on such diverse types of datasets in the present manuscript, which focuses on CausalXtract’s pipeline for the analysis and causal interpretation of live-cell time-lapse imaging data from complex cellular systems.

Author response:

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

Reviewer 1:

We thank Reviewer 1 for their helpful comments and hope that the changes made to the revised manuscript have addressed their points.

This study presents a novel application of the inverted encoding (i.e., decoding) approach to detect the correlates of crossmodal integration in the human EEG (electrophysiological) signal. The method is successfully applied to data from a group of 41 participants, performing a spatial localization task on auditory, visual, and audiovisual events. The analyses clearly show a behavioural superiority for audio-visual localization. Like previous studies, the results when using traditional univariate ERP analyses were inconclusive, showing once more the need for alternative, more sophisticated approaches. Instead, the principal approach of this study, harnessing the multivariate nature of the signal, captured clear signs of super-additive responses, considered by many as the hallmark of multisensory integration. Unfortunately, the manuscript lacks many important details in the descriptions of the methodology and analytical pipeline. Although some of these details can eventually be retrieved from the scripts that accompany this paper, the main text should be self-contained and sufficient to gain a clear understanding of what was done. (A list of some of these is included in the comments to the authors). Nevertheless, I believe the main weakness of this work is that the positive results obtained and reported in the results section are conditioned upon eye movements. When artifacts due to eye movements are removed, then the outcomes are no longer significant. 

Therefore, whether the authors finally achieved the aims and showed that this method of analysis is truly a reliable way to assess crossmodal integration, does not stand on firm ground. The worst-case scenario is that the results are entirely accounted for by patterns of eye movements in the different conditions. In the best-case scenario, the method might truly work, but further experiments (and/or analyses) would be required to confirm the claims in a conclusive fashion.

One first step toward this goal would be, perhaps, to facilitate the understanding of results in context by reporting both the uncorrected and corrected analyses in the main results section. Second, one could try to support the argument given in the discussion, pointing out the origin of the super-additive effects in posterior electrode sites, by also modelling frontal electrode clusters and showing they aren't informative as to the effect of interest.

We performed several additional analyses to address concerns that our main result was caused by different eye movement patterns between conditions. We re-ran our key analyses using activity exclusively from frontal electrodes, which revealed poorer decoding performance than that from posterior electrodes. If eye movements were driving the non-linear enhancement in the audiovisual condition, we would expect stronger decoding using sensors closer to the source, i.e., the extraocular muscles. We also computed the correlations between average eye position and stimulus position for each condition to evaluate whether participants made larger eye movements in the audiovisual condition, which might have contributed to better decoding results. Though we did find evidence for eye movements toward stimuli, the degree of movement did not significantly differ between conditions.

Furthermore, we note that the analysis using a stricter eye movement criterion, acknowledged in the Discussion section of the original manuscript, resulted in very similar results to the original analysis. There was significantly better decoding in the AV condition (as measured by d') than the MLE prediction, but this difference did not survive cluster correction. The most likely explanation for this is that the strict eye movement criterion combined with our conservative measure of (mass-based) cluster correction led to reduced power to detect true differences between conditions. Taken together with the additional analyses described in the revised manuscript and supplementary materials, the results show that eye movements are unlikely to account for differences between the multisensory and unisensory conditions. Instead, our decoding results likely reflect nonlinear neural integration between audio and visual sensory information.

“Any experimental design that varies stimulus location needs to consider the potential contribution of eye movements. We computed correlations between participants’ average eye position and each stimulus position between the three sensory conditions (auditory, visual and audiovisual; Figure S1) and found evidence that participants made eye movements toward stimuli. A re-analysis of the data with a very strict eye-movement criterion (i.e., removing trials with eye movements >1.875º) revealed that the super-additive enhancement in decoding accuracy no longer survived cluster correction, suggesting that our results may be impacted by the consistent motor activity of saccades towards presented stimuli. Further investigation, however, suggests this is unlikely. Though the correlations were significantly different from 0, they were not significantly different from each other. If consistent saccades to audiovisual stimuli were responsible for the nonlinear multisensory benefit we observed, we would expect to find a higher positive correlation between horizontal eye position and stimulus location in the audiovisual condition than in the auditory or visual conditions. Interestingly, eye movements corresponded more to stimulus location in the auditory and audiovisual conditions than in the visual condition, indicating that it was the presence of a sound, rather than a visual stimulus, that drove small eye movements. This could indicate that participants inadvertently moved their eyes when localising the origin of sounds. We also re-ran our analyses using the activity measured from the frontal electrodes alone (Figure S2). If the source of the nonlinear decoding accuracy in the audiovisual condition was due to muscular activity produced by eye movements, there should be better decoding accuracy from sensors closer to the source. Instead, we found that decoding accuracy of stimulus location from the frontal electrodes (peak d' = 0.08) was less than half that of decoding accuracy from the more posterior electrodes (peak d' = 0.18). These results suggest that the source of neural activity containing information about stimulus position was located over occipito-parietal areas, consistent with our topographical analyses (inset of Figure 3).” 

The univariate ERP analyses an outdated contrast, AV <> A + V to capture multisensory integration. A number of authors have pointed out the potential problem of double baseline subtraction when using this contrast, and have recommended a number of solutions, experimental and analytical. See for example: [1] and [2]. 

(1) Teder-Salejarvi, W. A., McDonald, J. J., Di Russo, F., & Hillyard, S. A. (2002). Cognitive Brain Research, 14, 106-114. 

(2) Talsma, D., & Woldorff, M. G. (2005). Journal of cognitive neuroscience, 17(7), 1098-1114.

We thank the reviewer for raising this point. Comparing ERPs across different sensory conditions requires careful analytic choices to discern genuine sensory interactions within the signal. The AV <> (A +V) contrast has often been used to detect multisensory integration, though any non-signal related activity (i.e. anticipatory waves; Taslma & Woldorff, 2005) or pre-processing manipulation (e.g. baseline subtraction; Teder-Sälejärvi et al., 2002) will be doubled in (A + V) but not in AV. Critically, we did not apply a baseline correction during preprocessing and thus our results are not at risk of double-baseline subtraction in (A + V). Additionally, we temporally jittered the presentation of our stimuli to mitigate the potential influence of consistent overlapping ERP waves (Talsma & Woldorff, 2005). 

The results section should provide the neurometric curve/s used to extract the slopes of the sensitivity plot (Figure 2B). 

We thank the reviewer for raising this point of clarification. The sensitivity plots for Figures 2B and 2C were extracted from the behavioural performance of the behavioural and EEG tasks, respectively. The sensitivity plot for Figure 2B was extracted from individual psychometric curves, whereas the d’ values for Figure 2C were calculated from the behavioural data for the EEG task. This information has been clarified in the manuscript.

“Figure 1. Behavioural performance is improved for audiovisual stimuli. A) Average accuracy of responses across participants in the behavioural session at each stimulus location for each stimulus condition, fitted to a psychometric curve. Steeper curves indicate greater sensitivity in identifying stimulus location. B) Average sensitivity across participants in the behavioural task, estimated from psychometric curves, for each stimulus condition. The red cross indicates estimated performance assuming optimal (MLE) integration of unisensory cues. C) Average behavioural sensitivity across participants in the EEG session for each stimulus condition. Error bars indicate ±1 SEM.”

The encoding model was fitted for each electrode individually; I wonder if important information contained as combinations of (individually non-significant) electrodes was then lost in this process and if the authors consider that this is relevant. 

Although the encoding model was fitted for each electrode individually for the topographic maps (Figure 4B), in all other analyses the encoding model was fitted across a selection of electrodes (see final inset of Figure 3). As this electrode set was used for all other neural analyses, our model would allow for the detection of important information contained in the neural patterns across electrodes. This information has been clarified in the manuscript.

“Thus, for all subsequent analyses we only included signals from the central-temporal, parietal-occipital, occipital and inion sensors for computing the inverse model (see final inset of Figure 2). As the model was fitted for multiple electrodes, subtle patterns of neural information contained within combinations of sensors could be detected.”

Neurobehavioral correlations could benefit from outlier rejection and the use of robust correlation statistics. 

We thank the reviewer for raising this issue. Note, however, that the correlations we report are resistant to the influence of outliers because we used Spearman’s rho1 (as opposed to Pearson’s). This information has been communicated in the manuscript.

(1) Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069

“Neurobehavioural correlations. As behavioural and neural data violated assumptions of normality, we calculated rank-order correlations (Spearman’s rho) between the average decoding sensitivity for each participant from 150-250 ms poststimulus onset and behavioural performance on the EEG task. As Spearman’s rho is resistant to outliers (Wilcox, 2016), we did not perform outlier rejection.”

“Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069”

Many details that are important for the reader to evaluate the evidence and to understand the methods and analyses aren't given; this is a non-exhaustive list:  

We thank the reviewer for highlighting these missing details. We have updated the manuscript where necessary to ensure the methods and analyses are fully detailed and replicable.

- specific parameters of the stimuli and performance levels. Just saying "similarly difficult" or "marginally higher volume" is not enough to understand exactly what was done.  

“The perceived source location of auditory stimuli was manipulated via changes to interaural level and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992). The precise timing of when each speaker delivered an auditory stimulus was calculated from the following formula:

where x and z are the horizontal and forward distances in metres between the ears and the source of the sound on the display, respectively, r is the head radius, and s is the speed of sound. We used a constant approximate head radius of 8 cm for all participants. r was added to x for the left speaker and subtracted for the right speaker to produce the interaural time difference. For ±15° source locations, interaural timing difference was 1.7 ms. To simulate the decrease in sound intensity as a function of distance, we calculated interaural level differences for the left and right speakers by dividing the sounds by the left and right distance vectors. Finally, we resampled the sound using linear interpolation based on the calculations of the interaural level and timing differences. This process was used to calculate the soundwaves played by the left and right speakers for each of the possible stimulus locations on the display. The maximum interaural level difference between speakers was 0.14 A for ±15° auditory locations, and 0.07 A for ±7.5°.”

- where are stimulus parameters adjusted individually or as a group? Which method was followed?  

To clarify, stimulus parameters (frequency, size, luminance, volume, location, etc.) were manipulated throughout pilot testing only. Parameters were adjusted to achieve similar pilot behavioural results between the auditory and visual conditions. For the experiment proper, parameters remained constant for both tasks and were the same for all participants.

“During pilot testing, stimulus features (size, luminance, volume, frequency etc.) were manipulated to make visual and auditory stimuli similarly difficult to spatially localize. These values were held constant in the main experiment.”

- specify which response buttons were used.

“Participants were presented with two consecutive stimuli and tasked with indicating, via button press, whether the first (‘1’ number-pad key) or second (‘2’ number-pad key) interval contained the more leftward stimulus.”

“At the end of each sequence, participants were tasked with indicating, via button press, whether more presentations appeared on the right (‘right’ arrow key) or the left (‘left’ arrow key) of the display.”

- no information is given as to how many trials per condition remained on average, for analysis.  

The average number of remaining trials per condition after eye-movement analysis is now included in the Methods section of the revised manuscript.

“We removed trials with substantial eye movements (>3.75 away from fixation) from the analyses. After the removal of eye movements, on average 2365 (SD \= 56.94), 2346 (SD \= 152.87) and 2350 (SD \= 132.47) trials remained for auditory, visual and audiovisual conditions, respectively, from the original 2400 per condition.”

- no information is given on the specifics of participant exclusion criteria. (even if the attrition rate was surprisingly high, for such an easy task).  

The behavioural session also served as a screening task. Although the task instructions were straightforward, perceptual discrimination was not easy due to the ambiguity of the stimuli. Auditory localization is not very precise, and the visual stimuli were brief, dim, and diffuse. The behavioural results reflect the difficulty of the task. Attrition rate was high as participants who scored below 60% correct in any condition were deemed unable to accurately perform the task, were not invited to complete the subsequent EEG session, and omitted from the analyses. We have included the specific criteria in the manuscript.

“Participants were first required to complete a behavioural session with above 60% accuracy in all conditions to qualify for the EEG session (see Behavioural session for details).”

- EEG pre-processing: what filter was used? How was artifact rejection done? (no parameters are reported); How were bad channels interpolated?  

We used a 0.25 Hz high-pass filter to remove baseline drifts, but no low-pass filter. In line with recent studies on the undesirable influence of EEG preprocessing on ERPs1, we opted to avoid channel interpolation and artifact rejection. This was erroneously reported in the manuscript and has now been clarified. For the sake of clarity, here we demonstrate that a reanalysis of data using channel interpolation and artifact rejection returned the same pattern of results. 

(1) Delorme, A. (2023). EEG is better left alone. Scientific Reports, 13, 2372. https://doi.org/10.1038/s41598-023-27528-0

- specific electrode locations must be given or shown in a plot (just "primarily represented in posterior electrodes" is not sufficiently informative).  

A diagram of the electrodes used in all analyses is included within Figure 3, and we have drawn readers’ attention to this in the revised manuscript.

“Thus, for all subsequent analyses we only included signals from the central-temporal, parietal-occipital, occipital and inion sensors for computing the inverse model (see final inset of Figure 2).” 

- ERP analysis: which channels were used? What is the specific cluster correction method?

We used a conservative mass-based cluster correction from Pernet et al. (2015) - this information has been clarified in the manuscript.

“A conservative mass-based cluster correction was applied to account for spurious differences across time (Pernet et al., 2015).” 

“Pernet, C. R., Latinus, M., Nichols, T. E., & Rousselet, G. A. (2015). Cluster-based computational methods for mass univariate analyses of event-related brain potentials/fields: A simulation study. Journal of Neuroscience Methods, 250, 85-93. https://doi.org/https://doi.org/10.1016/j.jneumeth.2014.08.003” 

- results: descriptive stats on performance must be given (instead of saying "participants performed well").  

The mean and standard deviation of participants’ performance for each condition in the behavioural and EEG experiments are now explicitly mentioned in the manuscript.

“A quantification of the behavioural sensitivity (i.e., steepness of the curves) revealed significantly higher sensitivity for the audiovisual stimuli (M = .04, SD = .02) than for the auditory stimuli alone (M = .03, SD = .01; Z = -3.09, p = .002), and than for the visual stimuli alone (M = .02, SD = .01; Z = -5.28, p = 1.288e-7; Figure 1B). Sensitivity for auditory stimuli was also significantly higher than sensitivity for visual stimuli (Z = 2.02, p = .044).” 

“We found a similar pattern of results to those in the behavioural session; sensitivity for audiovisual stimuli (M = .85, SD = .33) was significantly higher than for auditory (M = .69, SD = .41; Z = -2.27, p = .023) and visual stimuli alone (M = .61, SD = .29; Z = -3.52, p = 4.345e-4), but not significantly different from the MLE prediction (Z = -1.07, p = .285).” 

- sensitivity in the behavioural and EEG sessions is said to be different, but no comparison is given. It is not even the same stimulus set across the two tasks...  

This relationship was noted as a potential explanation for the higher sensitivities obtained in the EEG task, and was not intended to stand up to statistical scrutiny. We agree it makes little sense to compare statistically between the EEG and behavioural results as they were obtained from different tasks. We would like to clarify, however, that the stimuli used in the two tasks were the same, with the exception that in the EEG task the stimuli were presented from 5 locations versus 8 in the behavioural task. To avoid potential confusion, we have removed the offending sentence from the manuscript:

Reviewer 2:

Their measure of neural responses is derived from the decoder responses, and this takes account of the reliability of the sensory representations - the d' statistics - which is an excellent thing. It also means if I understand their analysis correctly (it could bear clarifying - see below), that they can generate from it a prediction of the performance expected if an optimal decision is made combining the neural signals from the individual modalities. I believe this is the familiar root sum of squares d' calculation (or very similar). Their decoding of the audiovisual responses comfortably exceeds this prediction and forms part of the evidence for their claims. 

Yet, superadditivity - including that in evidence in the principle of inverse effectiveness more typically quantifies the excess over the sum of proportions correct in each modality. Their MLE d' statistic can already predict this form of superadditivity. Therefore, the superadditivity they report here is not the same form of superadditivity that is usually referred to in behavioural studies. It is in fact a stiffer definition. What their analysis tests is that decoding performance exceeds what would be expected from an optimally weighted linear integration of the unisensory information. As this is not the common definition it is difficult to relate to behavioral superadditivity reported in much literature (of percentage correct). This distinction is not at all clear from the manuscript. 

But the real puzzle is here: The behavioural data or this task do not exceed the optimal statistical decision predicted by signal detection theory (the MLE d'). Yet, the EEG data would suggest that the neural processing is exceeding it. So why, if the neural processing is there to yield better performance is it not reflected in the behaviour? I cannot explain this, but it strikes me that the behaviour and neural signals are for some reason not reflecting the same processing. 

Be explicit and discuss this mismatch they observe between behaviour and neural responses. 

Thank you, we agree that it is worth expanding on the observed disconnect between MSI in behaviour and neural signals. We have included an additional paragraph in the Discussion of the revised manuscript. Despite the mismatch, we believe the behavioural and neural responses still reflect the same underlying processing, but at different levels of sensitivity. The behavioural result likely reflects a coarse down-sampling of the precision in location representation, and thus less likely to reflect subtle MSI enhancements.

“An interesting aspect of our results is the apparent mismatch between the behavioural and neural responses. While the behavioural results meet the optimal statistical threshold predicted by MLE, the decoding analyses suggest that the neural response exceeds it. Though non-linear neural responses and statistically optimal behavioural responses are reliable phenomena in multisensory integration (Alais & Burr, 2004; Ernst & Banks, 2002; Stanford & Stein, 2007), the question remains – if neural super-additivity exists to improve behavioural performance, why is it not reflected in behavioural responses? A possible explanation for this neurobehavioural discrepancy is the large difference in timing between sensory processing and behavioural responses. A motor response would typically occur some time after the neural response to a sensory stimulus (e.g., 70-200 ms), with subsequent neural processes between perception and action that introduce noise (Heekeren et al., 2008) and may obscure super-additive perceptual sensitivity. In the current experiment, participants reported either the distribution of 20 serially presented stimuli (EEG session) or compared the positions of two stimuli (behavioural session), whereas the decoder attempts to recover the location of every presented stimulus. While stimulus location could be represented with higher fidelity in multisensory relative to unisensory conditions, this would not necessarily result in better performance on a binary behavioural task in which multiple temporally separated stimuli are compared. One must also consider the inherent differences in how super-additivity is measured at the neural and behavioural levels. Neural super-additivity should manifest in responses to each individual stimulus. In contrast, behavioural super-additivity is often reported as proportion correct, which can only emerge between conditions after being averaged across multiple trials. The former is a biological phenomenon, while the latter is an analytical construct. In our experiment, we recorded neural responses for every presentation of a stimulus, but behavioural responses were only obtained after multiple stimulus presentations. Thus, the failure to find super-additivity in behavioural responses might be due to their operationalisation, with between-condition comparisons lacking sufficient sensitivity to detect super-additive sensory improvements. Future work should focus on experimental designs that can reveal super-additive responses in behaviour.”

Re-work the introduction to explain more clearly the relationship between the behavioural superadditivities they review, the MLE model, and the superadditivity it actually tests. 

We agree it is worth discussing how super-additivity is operationalised across neural and behavioural measures. However, we do not believe the behavioural studies we reviewed claimed super-additive behavioural enhancements. While MLE is often used as a behavioural marker of successful integration, it is not necessarily used as evidence for super-additivity within the behavioural response, as it relies on linear operations. 

“It is important to consider the differences in how super-additivity is classified between neural and behavioural measures. At the level of single neurons, superadditivity is defined as a non-linear response enhancement, with the multisensory response exceeding the sum of the unisensory responses. In behaviour, meanwhile, it has been observed that the performance improvement from combining two senses is close to what is expected from optimal integration of information across the senses (Alais & Burr, 2004; Stanford & Stein, 2007). Critically, behavioural enhancement of this kind does not require non-linearity in the neural response, but can arise from a reliability-weighted average of sensory information. In short, behavioural performance that conforms to MLE is not necessarily indicative of neural super-additivity, and the MLE model can be considered a linear baseline for multisensory integration.”

Regarding the auditory stimulus, this reviewer notes that interaural time differences are unlikely to survive free field presentation.

Despite the free field presentation, in both the pilot test and the study proper participants were able to localize auditory stimuli significantly above chance. 

"However, other studies have found super-additive enhancements to the amplitude of sensory event-related potentials (ERPs) for audiovisual stimuli (Molholm et al., 2002; Talsma et al., 2007), especially when considering the influence of stimulus intensity (Senkowski et al., 2011)." - this makes it obvious that there are some studies which show superadditivity. It would have been good to provide a little more depth here - as to what distinguished those studies that reported positive effects from those that did not.

We have provided further detail on how super-additivity appears to manifest in neural measures.

“In EEG, meanwhile, the evoked response to an audiovisual stimulus typically conforms to a sub-additive principle (Cappe et al., 2010; Fort et al., 2002; Giard & Peronnet, 1999; Murray et al., 2016; Puce et al., 2007; Stekelenburg & Vroomen, 2007; Teder- Sälejärvi et al., 2002; Vroomen & Stekelenburg, 2010). However, when the principle of inverse effectiveness is considered and relatively weak stimuli are presented together, there has been some evidence for super-additive responses (Senkowski et al., 2011).”

“While behavioural outcomes for multisensory stimuli can be predicted by MLE, and single neuron responses follow the principles of inverse effectiveness and super- additivity, among others (Rideaux et al., 2021), how audiovisual super-additivity manifests within populations of neurons is comparatively unclear given the mixed findings from relevant fMRI and EEG studies. This uncertainty may be due to biophysical limitations of human neuroimaging techniques, but it may also be related to the analytic approaches used to study these recordings. For instance, superadditive responses to audiovisual stimuli in EEG studies are often reported from very small electrode clusters (Molholm et al., 2002; Senkowski et al., 2011; Talsma et al., 2007), suggesting that neural super-additivity in humans may be highly specific. However, information encoded by the brain can be represented as increased activity in some areas, accompanied by decreased activity in others, so simplifying complex neural responses to the average rise and fall of activity in specific sensors may obscure relevant multivariate patterns of activity evoked by a stimulus.”

P9. "(25-75 W, 6 Ω)." This is not important, but it is a strange way to cite the power handling of a loudspeaker. 

“The loudspeakers had a power handling capacity of 25-75 W and a nominal impedance of 6 Ω.” 

I am struggling to understand the auditory stimulus: 

"Auditory stimuli were 100 ms clicks". Is this a 100-ms long train of clicks? A single pulse which is 100ms long would not sound like a click, but two clicks once filtered by the loudspeaker. Perhaps they mean 100us. 

"..with a flat 850 Hz tone embedded within a decay envelope". Does this mean the tone is gated - i.e. turns on and off slowly? Or is it constant?

We thank the reviewer for catching this. ‘Click’ may not be the most apt way of defining the auditory stimulus. It was a 100 ms square wave tone with decay, i.e., with an onset at maximal volume before fading gradually. Given that the length of the stimulus was 100 ms, the decay occurs quickly and provides a more ‘click-like’ percept than a pure tone. We have provided a representation of the sound below for further clarification. This represents the amplitude from the L and R speakers for maximally-left and maximally-right stimuli. We have added this clarification in the revised manuscript. 

Author response image 1.

“Auditory stimuli were 100 ms, 850 Hz tones with a decay function (sample rate = 44, 100 Hz; volume = 60 dBA SPL, as measured at the ears).”

P10. "Stimulus modality was either auditory, visual, or audiovisual. Trials were blocked with short (~2 min) breaks between conditions".

Presumably the blocks were randomised across participants.

Condition order was not randomised across participants, but counterbalanced. This has been clarified in the manuscript.

“Stimulus modality was auditory, visual or audiovisual, presented in separate blocks with short breaks (~2 min) between conditions (see Figure 6A for an example trial). The order of conditions was counterbalanced across participants.” 

P15. Feels like there is a step not described here: "The d' of the auditory and visual conditions can be used to estimate the predicted 'optimal' sensitivity of audiovisual signals as calculated through MLE." Do they mean sqrt[ (d'A)^2 + (d'V)^2] ? If it is so simple then it may as well be made explicit here. A quick calculation from eyeballing Figures 2B and 2C suggests this is the case.

We thank the reviewer for raising this point of clarification. Yes, the ‘optimal’ audiovisual sensitivity was calculated as the hypotenuse of the auditory and visual sensitivities. This calculation has been made explicit in the revised manuscript.

The d’ from the auditory and visual conditions can be used to estimate the predicted ‘optimal’ sensitivity to audiovisual signals as calculated through the following formula:

"The perceived source location of auditory stimuli was manipulated via changes to interaural intensity and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992)." The stimuli were delivered by a pair of loudspeakers, and the incident sound at each ear would be a product of both speakers. And - if there were a time delay between the two speakers, then both ears could potentially receive separate pulses one after the other at different delays. Did they record this audio stimulus with manikin? If not, it would be very difficult to know what it was at the ears. I don't doubt that if they altered the relative volume of the loudspeakers then some directionality would be perceived but I cannot see how the interaural level and timing differences could be matched - as if the sound were from a single source. I doubt that this invalidates their results, but to present this as if it provided matched spatial and timing cues is wrong, and I cannot work out how they can attribute an azimuthal location to the sound. For replication purposes, it would be useful to know how far apart the loudspeakers were and what the timing and level differences actually were.

The behavioural tasks each had evenly distributed ‘source locations’ on the horizontal azimuth of the computer display (8 for the behavioural session, 5 for the EEG session). We manipulated the perceived location of auditory stimuli through interaural time delays and interaural level differences. By first measuring the forward (z) and horizontal (x) distance of each source location to each ear, the method worked by calculating what the time-course of a sound wave should be at the location of the ear given the sound wave at the source. Then, for each source location, we can calculate the time delay between speakers given the vectors of x and z, the speed of sound and the width of the head.  As the intensity of sound drops inversely with the square of the distance, we can divide the sound wave by the distance for each source location to provide the interaural level difference. Though we did not record the auditory stimulus with a manikin, our behavioural analyses show that participants were able to detect the directions of auditory stimuli from our manipulations, even to a degree that significantly exceeded the localisation accuracy for visual stimuli (for the behavioural session task). This information has been clarified in the manuscript.

“Auditory stimuli were played through two loudspeakers placed either side of the display (80 cm apart for the behavioural session, 58 cm apart for the EEG session).” 

“The perceived source location of auditory stimuli was manipulated via changes to interaural level and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992). The precise timing of when each speaker delivered an auditory stimulus was calculated from the following formula:

where x and z are the horizontal and forward distances in metres between the ears and the source of the sound on the display, respectively, r is the head radius, and s is the speed of sound. We used a constant approximate head radius of 8 cm for all participants. r was added to x for the left speaker and subtracted for the right speaker to produce the interaural time difference. For ±15° source locations, interaural timing difference was 1.7 ms. To simulate the decrease in sound intensity as a function of distance, we calculated interaural level differences for the left and right speakers by dividing the sounds by the left and right distance vectors. Finally, we resampled the sound using linear interpolation based on the calculations of the interaural level and timing differences. This process was used to calculate the soundwaves played by the left and right speakers for each of the possible stimulus locations on the display. The maximum interaural level difference between speakers was 0.14 A for ±15° auditory locations, and 0.07 A for ±7.5°.

I am confused about this statement: "A quantification of the behavioural sensitivity (i.e., steepness of the curves) revealed significantly greater sensitivity for the audiovisual stimuli than for the auditory stimuli alone (Z = -3.09, p = .002)," It is not clear from the methods how they attributed sound source angle to the sounds. Conceivably they know the angle of the loudspeakers, and this would provide an outer bound on the perceived location of the sound for extreme interaural level differences (although free field interaural timing cues can create a wider sound field). 

Our analysis of behavioural sensitivity was dependent on the set ‘source locations’ that were used to calculate the position of auditory and audiovisual stimuli.  In the behavioural task, participants judged the position of the target stimulus relative to a central stimulus. Thus, for each source location, we recorded how often participants correctly discriminated between presentations. The quoted analysis acknowledges that participants were more sensitive to audiovisual stimuli than auditory stimuli in the context of this task. A full explanation of how source location was implemented for auditory stimuli has been clarified in the manuscript. 

It would be very nice to see some of the "channel" activity - to get a feel for the representation used by the decoder. 

We have included responses for the five channels as a Supplemental Figure.

Figure 6 appears to show that there is some agreement between behaviour and neural responses - for the audiovisual case alone. The positive correlation of behavioural and decoding sensitivity appears to be driven by one outlier - who could not perform the audiovisual task (and indeed presumably any of them). Furthermore, if we were simply Bonferonni correct for the three comparisons, this would become non-significant. It is also puzzling why the unisensory behaviour and EEG do not correlate - which seems to again suggest a poor correspondence between them. Opposite to the claim made.

We understand the reviewer’s concern here. We would like to note, however, that each correlation used unique data sets – that is, the behavioural and neural data for each separate condition. In this case, we believe a Bonferroni correction for multiple comparisons is too conservative, as no data set was compared more than once. Neither the behavioural nor the neural data were normally distributed, and both contained outliers. Rather than reduce power through outlier rejection, we opted to test correlations using Spearman’s rho, which is resistant to outliers1. It is also worth noting that, without outlier rejection, the audiovisual correlation (p \= .003) would survive a Bonferroni correction for 3 comparisons. The nonsignificant correlation in the auditory and visual conditions might be due to the weaker responses elicited by unisensory stimuli, with the reduced signal-to-noise ratio obscuring potential correlations. Audiovisual stimuli elicited more precise responses both behaviourally and neurally, increasing the power to detect a correlation. 

(1) Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069

“We also found a significant positive correlation between participants’ behavioural judgements in the EEG session and decoding sensitivity for audiovisual stimuli. This result suggests that participants who were better at identifying stimulus location also had more reliably distinct patterns of neural activity. The lack of neurobehavioural correlation in the unisensory conditions might suggest a poor correspondence between the different tasks, perhaps indicative of the differences between behavioural and neural measures explained previously. However, multisensory stimuli have consistently been found to elicit stronger neural responses than unisensory stimuli (Meredith & Stein, 1983; Puce et al., 2007; Senkowski et al., 2011; Vroomen & Stekelenburg, 2010), which has been associated with behavioural performance (Frens & Van Opstal, 1998; Wang et al., 2008). Thus, the weaker signalto-noise ratio in unisensory conditions may prevent correlations from being detected.”

Further changes:

(1)   To improve clarity, we shifted the Methods section to after the Discussion. This change included updating the figure numbers to match the new order (Figure 1 becomes Figure 6, Figure 2 becomes Figure 1, and so on).

(2)   We also resolved an error on Figure 2 (previously Figure 3). The final graph (Difference between AV and A + V) displayed incorrect values on the Y axis.

This has now been remedied.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to elucidate the diversity and gene expression patterns of marine plankton using innovative collection and sequencing methodologies. Their work investigates the taxonomic and functional profiles of planktonic communities, providing insights into their ecological roles and responses to environmental changes.

Strengths:

The methodology utilized in this study, particularly the combination of single-cell sequencing and advanced bioinformatics techniques, represents a significant advancement in the field of plankton research. The application of the Smart-seq2 protocol for cDNA synthesis, followed by rigorous quality control measures, ensures high-quality data generation. This comprehensive approach not only enhances the resolution of the obtained genetic information but also allows for a more detailed exploration of the diversity and functional potential of the phytoplankton community.

One of the major strengths of this study is the rigorous methodological approach, including precise sampling techniques and robust data analysis protocols, which enhance the reliability of the results. The use of advanced sequencing technologies allows for a comprehensive assessment of gene expression, significantly contributing to our understanding of plankton diversity and its implications for marine ecosystems.

Weaknesses:

While the evidence presented is solid, there are areas where the analysis could be expanded. The authors could further explore the ecological interactions within plankton communities, which would provide a more holistic view of their functional roles. Additionally, a broader discussion of the implications of their findings for marine conservation efforts could enhance the manuscript's impact.

The choice of both the plankton net and filter pore size during the plankton collection process is critical, as these factors directly impact the types of phytoplankton collected. The use of a 25 μm filter paper, in particular, may result in the omission of many eukaryotic phytoplankton species. This limitation, combined with the characteristics of the plankton net, could affect the comprehensiveness and accuracy of the results, potentially influencing the study's conclusions regarding phytoplankton diversity.

The timing of fixation is crucial, as it directly affects whether the measured transcriptome accurately represents the organisms' actual transcriptional state in their native water environment. If fixation occurred a significant time after sample collection, the transcriptomic data may not reflect their true in situ transcriptional activity, which greatly reduces the relevance of this method.

Thank you for your time, effort, and expertise.

We agree that additional analyses could improve our understanding of the plankton communities sampled. We have conducted an array of alternative analyses that were not included in the current manuscript and plan to perform new analyses over the next few months as part of a deeper revision of the manuscript. We are especially interested in “providing a more holistic view of the functions” of individual plankton within the community.

As for the protocol details, the pore size of the filter paper was chosen to focus on ~100 micron-sized organisms as a starting point: they are likely to contain more RNA than smaller organisms, making them well suited for an initial proof of concept of the methodology. That choice, however, is not particularly tightly constrained, therefore smaller plankton could be captured. This is supported by the lack of correlation, in our data, between organismal size and number of detected sequencing reads.

Timing to cell death/fixation is a common question we receive not just in this manuscript but any RNA-Seq from primary samples. In this case, plankton were seen swimming until picking, and after picking each organism was deposited within two seconds into a lysis buffer for fixation. Therefore, we do not have reason to believe that the transcriptional activity sampled in the sequencing reads differs in any major way from the one in living plankton. Nonetheless, a study specifically testing the effect of time between ocean sampling and reverse transcription would provide more quantitative information on this point.

Reviewer #2 (Public review):

Summary:

The paper introduces Ukiyo-e-Seq, a novel method integrating microscopy with single-cell transcriptomics to study individual, uncultured eukaryotic plankton cells. By combining microscopic imaging with transcriptomic analysis, the approach links plankton morphology to gene expression, enabling taxonomic identification and functional protein exploration. Ukiyo-e-Seq was tested on 66 microbial eukaryotic cells, revealing taxonomic diversity across four superkingdoms and allowing analysis of protein complexes and developmental genes in individual species. According to the authors, this method has the potential to advance single-cell marine biodiversity studies by addressing limitations in traditional taxonomy and metatranscriptomics, especially for rare or uncultured organisms.

However, the study's conclusions are often weakly supported by data, particularly given that this is not the first study to combine microscopy and single-cell transcriptomics of eukaryotic plankton using Smart-seq2.

Strengths:

A notable strength is the authors' generation of several single-cell transcriptomes for the diatom Chaetoceros, which could benefit from greater focus rather than broadly addressing eukaryotic single cells.

Weaknesses:

The study lacks comparison with other single-cell transcriptomics studies and it was presented as the first study that combines imaging and single-cell transcriptomics (smart-seq2) of eukaryotic plankton while in fact it is not. The sampling methodology is not replicable as the authors used a tea strainer instead of standard plankton collection equipment to filter larger cells. Terminology throughout the paper is unconventional, such as "public and private contigs," "single-organism genomics," "highly expressed contigs," and "optical methods." Additionally, the authors did not specify which database was used for taxonomic assignments. These issues may stem from the authors' limited background in microbial ecology. Overall, the study has many drawbacks and it could benefit from complete rewriting and focusing mainly on single-cell transcriptomics of diatoms.

Thank you for your time, effort, and expertise.

There might be a bit of confusion between single-cell and single-organism sequencing, likely due to lack of clarity in our initial submission. In particular, in this manuscript no effort was spent trying to dissociate oligocellular plankton into individual cells before sequencing. While probably feasible, we expect that to be technically much harder than single-organism sequencing as performed here. The reviewer does not reference a published paper where combined imaging and RNA-Seq of individual uncultured plankton has been achieved, and we were unable to find one in the scientific literature. As stated in the manuscript, others have already performed some work on cultured plankton and single-organism sequencing (without matching images) of uncultured environmental microorganisms.

The suggestion to focus on a smaller biological niche such as diatoms and adopt language more familiar to that specific community is well received. Indeed, given that organisms as diverse as fish larvae and diatoms could be profiled with Ukiyo-e-Seq, future studies could use the same method to address specific questions with a deeper and more narrow scope. However, this manuscript is demonstrating the feasibility of Ukiyo-e-Seq and its ability to produce usable data for a broad spectrum of organisms: part of the scientific audience might not have a specific interest in diatoms.

The tea strainer was used for coarse pre-filtering: the exact pore size, geometry and factory tolerance on those measurements are inconsequential because each organism is later chosen (or not) based on a high-resolution microscopy image (or multiple, if fluorescence is considered). This really is a strength of Ukiyo-e-Seq over FACS or droplet-based sorters, which can only collect coarse optical information from each organism for (typically) less than 1 millisecond. In Ukiyo-q-Seq, while the actual decision to pick an individual is currently manual (by the operator of the picker), it can be automated in principle. For instance, one could build a machine learning model of plankton taxonomy based on a large collection of labelled images and use predictions from such a model to automatically drive the picker (e.g. focussing on diatoms), increasing throughput. Even in that case, however, the initial filtering stages using tea strainers, plankton nets, filter paper etc. would not be critical for the final selection of individuals as long as they are not too restrictive.

The database used for taxonomic assignment was the NCBI non-redundant nucleotide database, accessed through the reference library provided by Kraken2 (nt).

Reviewer #3 (Public review):

Gatt et al. present a novel take on single-cell RNA-sequencing from complex planktonic samples, introducing an approach they aptly named Ukiyo-e-Seq. This work combines environmental sampling with cell picking, microscopic imaging, and Smart-seq2 single-cell RNA sequencing to profile uncultured eukaryotic plankton. Developing single-cell approaches for such ecosystems is critical, given the poor representation of many planktonic species in cultures and reference databases. This work could help bridge existing technological gaps between morphological and molecular studies of aquatic microeukaryotes

The authors argue that microscopy does not provide information on the biochemistry of species under consideration. At best, it provides taxonomic labeling of species within a sample, yet imaging fails to assess their metabolic state or to disentangle cryptic species. In a standard metatranscriptomic setup, the sequence pool is described by aligning assembled contigs with reference databases to obtain functional and taxonomic information. This complex community-level data is impossible to parse at the single-organism level. Moreover, by relying on reference datasets, a lot of potential information can be missed. The aim of the approach is to combine the strengths of both methods, generating single-cell transcriptomic data linked to individual plankton images.

Strengths:

Ukiyo-e-Seq generated a valuable dataset by combining imaging and transcriptomics for individual planktonic organisms from environmental samples. This multimodal approach has the potential to improve taxonomic predictions and functional insights at the single-organism level. This manuscript demonstrates the technical feasibility of such an approach. Data of this type is rare and thus represents a valuable resource to further advance single-cell sequencing of planktonic species from environmental samples.

Weaknesses:

(1) The merge-split strategy, where single-cell reads are pooled prior to assembly, is counterintuitive. Pooling obscures the single-organism resolution that single-cell methods aim to achieve. The approach might be useful for assembling low-coverage contigs, but risks masking unique expression profiles for transcripts unique to a given well. As an alternative, the authors could assemble each well independently to obtain well-specific transcriptomic bins. Assemblies could then be clustered based on sequence similarity, thereby imposing strict clustering parameters to maintain resolution, to create a common reference for downstream analysis if needed. In my opinion, better results would be obtained by implementing a per-well assembly and read mapping.

(2) The focus on the top five most expressed contigs throughout the manuscripts' data analysis is a limiting choice, as it excludes most contigs. In the preprint, we are presented with a very narrow view of the data. Visualising the entire range of assembled contigs would provide a better picture of the transcriptomic composition and diversity per well. It would be interesting to assess if the full information could be used to preliminary bin transcriptomic sequences from individual wells, for example, by gathering all 'private' contigs with high read coverage in a single well. Does such a set represent a single complete eukaryotic transcriptome?

(3) I missed a verification with (broad-scale) taxonomic assessments based on the associated microscopic images. In their goals, the authors state that a joint approach has the potential to discover new taxonomic biodiversity. I agree, and to me, this is what is exciting about the preprint, yet I miss an example or the right bioinformatic implementation to drive home this claim. Are there organisms in wells where poor taxonomic annotations, based on alignment to a reference database or the LCA approach implemented in Kraken2, would usually result in ignoring the species in classic metatranscriptomics? Can you advance the taxonomic annotation by referring back to the organisms' picture? Can manual assessment of taxonomy advance the results from the LCA approach?

(4) The current use of AlphaFold to predict protein structures does not convincingly add to the study's core objectives.

Overall, Ukiyo-e-Seq presents a promising method for studying single-cell diversity in environmental samples, though the bioinformatic pipeline requires refinement to support some of the claims made by the authors. Additionally, the manuscript would benefit from clarity and additional details in its methods and a more consistent approach to presenting results and summary statistics across all assembled contigs and all sampled wells, rather than focusing on selected wells.

Thank you for your time and effort, and for your expertise on the matter.

The suggestions to conduct additional bioinformatic analyses to explore more fully the criticality and potential of various design choices (e.g. meta-assembly) are well received. We have tried some of those ideas already (e.g. assembling individual wells) and we have considered but not yet conducted or polished others (e.g. a more thorough taxonomic verification). We will endeavour to carry out as many of those analyses as possible during the deeper revision process in the coming months.

AlphaFold 3’s use was designed to demonstrate the ability to investigate protein-protein interactions from individual species. When two peptide sequences are detected within the same well, they are more likely to be potential interacting partners than in a metatranscriptomic study, because the compartmentalisation of reads into tens or hundreds of wells greatly reduces the search space of potential interaction partners (which has a baseline runtime complexity of n squared, where n is the number of peptide sequences identified).

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Author response:

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

We performed multiple new experiments and analyses in response to the reviewers concerns, and incorporated the results of these analyses in the main text, and in multiple substantially revised or new figures. Before embarking on a point-by-point reply to the reviewers’ concerns, we here briefly summarize our most important revisions.

First, we addressed a concern shared by Reviewers #1-3 about a lack of information about our DNA sequences. To this end, we redesigned multiple figures (Figures 3, 4, 5, S8, S9, S10, S11, and S12) to include the DNA sequences of each tested promoter, the specific mutations that occurred in it, the resulting changes in position-weight-matrix (PWM) scores, and the spacing between promoter motifs. Second, Reviewers #1 and #2 raised concerns about a lack of validation of our computational predictions and the resulting incompleteness of the manuscript. To address this issue, we engineered 27 reporter constructs harboring specific mutations, and experimentally validated our computational predictions with them. Third, we expanded our analysis to study how a more complete repertoire of other sigma 70 promoter motifs such as the UP-element and the extended -10 / TGn motif affects gene expression driven by the promoters we study. Fourth, we addressed concerns by Reviewer #3 about the role of the Histone-like nucleoid-structuring protein (H-NS) in promoter emergence and evolution. We did this by performing both experiments and computational analyses, which are now shown in the newly added Figure 5. Fifth, to satisfy Reviewer #3’s concerns about missing details in the Discussion, we have rewritten this section, adding additional details and references. 

We next describe these and many other changes in a point-by-point reply to each reviewer’s comments. In addition, we append a detailed list of changes to each section and figure to the end of this document.

Reviewer #1 (Public Review):

Summary:

This study by Fuqua et al. studies the emergence of sigma70 promoters in bacterial genomes. While there have been several studies to explore how mutations lead to promoter activity, this is the first to explore this phenomenon in a wide variety of backgrounds, which notably contain a diverse assortment of local sigma70 motifs in variable configurations. By exploring how mutations affect promoter activity in such diverse backgrounds, they are able to identify a variety of anecdotal examples of gain/loss of promoter activity and propose several mechanisms for how these mutations interact within the local motif landscape. Ultimately, they show how different sequences have different probabilities of gaining/losing promoter activity and may do so through a variety of mechanisms.

We thank Reviewer #1 for taking the time to read and provide critical feedback on our manuscript. Their summary is fundamentally correct.

Major strengths and weaknesses of the methods and results:

This study uses Sort-Seq to characterize promoter activity, which has been adopted by multiple groups and shown to be robust. Furthermore, they use a slightly altered protocol that allows measurements of bi-directional promoter activity. This combined with their pooling strategy allows them to characterize expressions of many different backgrounds in both directions in extremely high throughput which is impressive! A second key approach this study relies on is the identification of promoter motifs using position weight matrices (PWMs). While these methods are prone to false positives, the authors implement a systematic approach which is standard in the field. However, drawing these types of binary definitions (is this a motif? yes/no) should always come with the caveat that gene expression is a quantitative trait that we oversimplify when drawing boundaries.

The point is well-taken. To clarify this and other issues, we have added a section on the limitations of our work to the Discussion. Within this section we include the following sentences (lines 675-680):

“Additionally, future studies will be necessary to address the limitations of our own work. First, we use binary thresholding to determine i) the presence or absence of a motif, ii) whether a sequence has promoter activity or not, and iii) whether a part of a sequence is a hotspot or not. While chosen systematically, the thresholds we use for these decisions may cause us to miss subtle but important aspects of promoter evolution and emergence.”

Their approach to randomly mutagenizing promoters allowed them to find many anecdotal examples of different types of evolutions that may occur to increase or decrease promoter activity. However, the lack of validation of these phenomena in more controlled backgrounds may require us to further scrutinize their results. That is, their explanations for why certain mutations lead or obviate promoter activity may be due to interactions with other elements in the 'messy' backgrounds, rather than what is proposed.

Thank you for raising this important point. To address it, we have conducted extensive new validation experiments for the newest version of this manuscript. For the “anecdotal” examples you described, we created 27 reporter constructs harboring the precise mutation that leads to the loss or gain of gene expression, and validated its ability to drive gene expression. The results from these experiments are in Figures 3, 4, 5, and Supplemental Figures S8-S11, and are labeled with a ′ (prime) symbol.

These experiments not only confirm the increases and decreases in fluorescence that our analysis had predicted. They also demonstrate, with the exception of two (out of 27) falsepositive discoveries, that background mutations do not confound our analysis. We mention these two exceptions (lines 364-367):

“In two of these hotspots, our validation experiments revealed no substantial difference in gene expression as a result of the hotspot mutation (Fig S8F′ and Fig S8J′). In both of these false positives, new -10 boxes emerge in locations without an upstream -35 box.”

An appraisal of whether the authors achieved their aims, and whether the results support their conclusions:

The authors express a key finding that the specific landscape of promoter motifs in a sequence affects the likelihood that local mutations create or destroy regulatory elements. The authors have described many examples, including several that are non-obvious, and show convincingly that different sequence backgrounds have different probabilities for gaining or losing promoter activity. While this overarching conclusion is supported by the manuscript, the proposed mechanisms for explaining changes in promoter activity are not sufficiently validated to be taken for absolute truth. There is not sufficient description of the strength of emergent promoter motifs or their specific spacings from existing motifs within the sequence. Furthermore, they do not define a systematic process by which mutations are assigned to different categories (e.g. box shifting, tandem motifs, etc.) which may imply that the specific examples are assigned based on which is most convenient for the narrative.

To summarize, Reviewer #1 criticizes the following three aspects of our work in this comment. 1) The mechanisms we proposed are not sufficiently validated. 2) The description of motifs, spacing, and PWM scores are not shown. 3) How mutations are classified into different categories (i.e. box-shifting, tandem motifs, etc.) is not systematically defined. 

These are all valid criticisms. In response, we performed an extensive set of follow-up experiments and analyses, and redesigned the majority of the figures. Here is a more detailed response to each criticism:

(1) Proposed mechanisms for explaining changes in promoter activity are not sufficiently validated. We engineered 27 reporter constructs harboring the specific mutations in the parents that we had predicted to change promoter activity. For each, we compared their fluorescence levels with their wild-type counterpart. The results from these experiments are in Figures 3 and 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12, and are labeled with a ′ (prime) symbol.

(2) No sufficient description of the strength of emergent promoter motifs or their specific spacings. We redesigned the figures to include the DNA sequences of the parent sequences, as well as the degenerate consensus sequences for each mutation. We additionally now highlight the specific motif sequences, their respective PWM scores, and by how much the score changes upon mutation. Finally, we annotated the spacing of motifs. These changes are in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12.

We note that in many cases, high-scoring PWM hits for the same motif can overlap (i.e. two -10 motifs or two -35 motifs overlap). Additionally, the proximity of a -35 and -10 box does not guarantee that the two boxes are interacting. Together, these two facts can result in an ambiguity of the spacer size between two boxes. To avoid any reporting bias, we thus often report spacer sizes as a range (see Figure panels 4F, S8D, S8F-L, S9A, S9H, S10A, and S10E). The smallest spacer we annotate is in Figure 4F with 10 bp, and the largest is in Figure S8D with 26 bp. Any more “extreme” distances are not annotated and for the reader to decide if an interaction is present or not.

(3) No systematic process by which mutations are assigned to different categories such as box shifting, tandem motifs, etc. We opted to reformulate these categories completely, because the phenotypic effects of a previously mentioned “tandem motif” was actually a byproduct of H-NS repression (see the newly added Figure S12). 

We also agree that the categories were ambiguous. We now introduce two terms: homo-gain and hetero-gain of -10 and -35 boxes. The manuscript now clearly defines these terms, and the relevant passage now reads as follows (lines 430-435): 

“We found that these mutations frequently create new boxes overlapping those we had identified as part of a promoter

(Fig S9). This occurs when mutations create a -10 box overlapping a -10 box, a -35 box overlapping a -35 box, a -10 box overlapping a -35 box, or a -35 box overlapping a -10 box. We call the resulting event a “homo-gain” when the new box is of the same type as the one it overlaps, and otherwise a “hetero-gain”. In either case, the creation of the new box does not always destroy the original box.”

Impact of the work on the field, and the utility of the methods and data to the community: From this study, we are more aware of different types of ways promoters can evolve and devolve, but do not have a better ability to predict when mutations will lead to these effects. Recent work in the field of bacterial gene regulation has raised interest in bidirectional promoter regions. While the authors do not discuss how mutations that raise expression in one direction may affect another, they have created an expansive dataset that may enable other groups to study this interesting phenomenon. Also, their variation of the Sort-Seq protocol will be a valuable example for other groups who may be interested in studying bidirectional expression. Lastly, this study may be of interest to groups studying eukaryotic regulation as it can inform how the evolution of transcription factor binding sites influences short-range interactions with local regulator elements. Any additional context to understand the significance of the work:

The task of computationally predicting whether a sequence drives promoter activity is difficult. By learning what types of mutations create or destroy promoters from this study, we are better equipped for this task.

We thank Reviewer #1 again for their time and their thoughtful comments.

Reviewer #2 (Public Review):

Summary:

Fuqua et al investigated the relationship between prokaryotic box motifs and the activation of promoter activity using a mutagenesis sequencing approach. From generating thousands of mutant daughter sequences from both active and non-active promoter sequences they were able to produce a fantastic dataset to investigate potential mechanisms for promoter activation. From these large numbers of mutated sequences, they were able to generate mutual information with gene expression to identify key mutations relating to the activation of promoter island sequences.

We thank Reviewer #2 for reading and providing a thorough review of our manuscript. 

Strengths:

The data generated from this paper is an important resource to address this question of promoter activation. Being able to link the activation of gene expression to mutational changes in previously nonactive promoter regions is exciting and allows the potential to investigate evolutionary processes relating to gene regulation in a statistically robust manner. Alongside this, the method of identifying key mutations using mutual information in this paper is well done and should be standard in future studies for identifying regions of interest.

Thank you for your kind words.

Weaknesses:

While the generation of the data is superb the focus only on these mutational hotspots removes a lot of the information available to the authors to generate robust conclusions. For instance.

(1) The linear regression in S5 used to demonstrate that the number of mutational hotspots correlates with the likelihood of a mutation causing promoter activation is driven by three extreme points.

A fair criticism. In response, we have chosen to remove the analysis of this trend from the manuscript entirely. (Additionally, Pnew and mutual information calculations both relied on the fluorescence scores of daughter sequences, so the finding was circular in its logic.)

(2) Many of the arguments also rely on the number of mutational hotspots being located near box motifs. The context-dependent likelihood of this occurring is not taken into account given that these sequences are inherently box motif rich. So, something like an enrichment test to identify how likely these hot spots are to form in or next to motifs.

Another good point. To address it, we carried out a computational analysis where we randomly scrambled the nucleotides of each parent sequence while maintaining the coordinates for each mutual information “hotspot.” This scrambling results in significantly less overlap with hotspots and boxes. This analysis is now depicted in Figure 2C and described in lines 272-296.

(3) The link between changes in expression and mutations in surrounding motifs is assessed with two-sided Mann Whitney U tests. This method assumes that the sequence motifs are independent of one another, but the hotspots of interest occur either in 0, 3, 4, or 5s in sequences. There is therefore no sequence where these hotspots can be independent and the correlation causation argument for motif change on expression is weakened.

This is a fair criticism and a limitation of the MWU test. To better support our reasoning, we engineered 27 reporter constructs harboring the specific mutations in the parents that we had predicted to change promoter activity. For each, we compared their fluorescence levels with their wild-type counterpart. The results from these experiments are in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12 and are labeled with a ′ (prime) symbol.

These experiments not only confirm the increases and decreases in fluorescence that our analysis had predicted. They also demonstrate, with the exception of two (out of 27) falsepositive discoveries, that background mutations do not confound our analysis. We mention these two exceptions (lines 364-367):

“In two of these hotspots, our validation experiments revealed no substantial difference in gene expression as a result of the hotspot mutation (Fig S8F′ and Fig S8J′). In both of these false positives, new -10 boxes emerge in locations without an upstream -35 box.”

(4) The distance between -10 and -35 was mentioned briefly but not taken into account in the analysis.

We have now included these spacer distances where appropriate. These changes are in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12.

We note that in many cases, high-scoring PWM hits for the same motif can overlap (i.e. two -10 motifs or two -35 motifs overlap). Additionally, the proximity of a -35 and -10 box does not guarantee that the two boxes are interacting. Together, these two facts can result in an ambiguity of the spacer size between two boxes. To avoid any reporting bias, we thus often report spacer sizes as a range (see Figure panels 4F, S8D, S8F-L, S9A, S9H, S10A, and S10E). The smallest spacer we annotate is in Figure 4F with 10 bp, and the largest is in Figure S8D with 26 bp. More “extreme” distances are not annotated, and for the reader to decide if an interaction is present or not.

The authors propose mechanisms of promoter activation based on a few observations that are treated independently but occur concurrently. To address this using complementary approaches such as analysis focusing on identifying important motifs, using something like a glm lasso regression to identify significant motifs, and then combining with mutational hotspot information would be more robust.

This is a great idea, and we pursued it as part of the revision. For each parent sequence, we mapped the locations of all -10 and -35 box motifs in the daughters, then reduced each sequence to a binary representation, either encoding or not encoding these motifs, also referred to as a “hot-encoded matrix.” We subsequently performed a Lasso regression between the hot-encoded matrices and the fluorescence scores of each daughter sequence. The regression then outputs “weights” to each of the motifs in the daughters. The larger a motif’s weight is, the more the motif influences promoter activity. The Author response image 1 describes our workflow.

Author response image 1.

We really wanted this analysis to work, but unfortunately, the computational model does not act robustly, even when testing multiple values for the hyperparameter lambda (λ), which accounts for differences in model biases vs variance.

The regression assigns strong weights almost exclusively to -10 boxes, and assigns weak to even negative weights to -35 boxes. While initially exciting, these weights do not consistently align with the results from the 27 constructs with individual mutations that we tested experimentally. This ultimately suggests that the regression is overfitting the data.

We do think a LASSO-regression approach can be applied to explore how individual motifs contribute to promoter activity. However, effectively implementing such a method would require a substantially more complex analysis. We respectfully believe that such an approach would distract from the current narrative, and would be more appropriate for a computational journal in a future study. 

Because this analysis was inconclusive, we have not made it part of the revised manuscript. However, we hope that our 27 experimentally validated new constructs with individual mutations are sufficient to address the reviewer’s concerns regarding independent verification of our computational predictions.

Other elements known to be involved in promoter activation including TGn or UP elements were not investigated or discussed.

Thank you for highlighting this potentially important oversight. In response, we have performed two independent analyses to explore the role of TGn in promoter emergence in evolution. First, we computationally searched for -10 boxes with the bases TGn immediately upstream of them in the parent sequences, and found 18 of these “extended -10 boxes” in the parents (lines 143145):

“On average, each parent sequence contains ~5.32 -10 boxes and ~7.04 -35 boxes (Fig S1). 18 of these -10 boxes also include the TGn motif upstream of the hexamer.”

However, only 20% of these boxes were found in parents with promoter activity (lines 182-185):

“We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9-RFP, P10-RFP, P11GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25-RFP). “

Second, we computationally searched through all of the daughter sequences to identify new -10 boxes with TGn immediately upstream. We found 114 -10 boxes with the bases TGn upstream. However, only 5 new -10 boxes (2 with TGn) were associated with increasing fluorescence (lines 338-345):

“On average, 39.5 and 39.4 new -10 and -35 boxes emerged at unique positions within the daughter sequences of each mutagenized parent (Fig 3A,B), with 1’562 and 1’576 new locations for -10 boxes and -35 boxes, respectively. ~22% (684/3’138) of these new boxes are spaced 15-20 bp away from their cognate box, and ~7.3% (114/1’562) of the new -10 boxes have the TGn motif upstream of them. However, only a mere five of the new -10 boxes and four of the new 35 boxes are significantly associated with increasing fluorescence by more than +0.5 a.u. (Fig 3C,D).”

In addition, we now study the role of UP elements. This analysis showed that the UP element plays a negligible role in promoter emergence within our dataset.  It is discussed in a new subsection of the results (lines 591-608).

Collectively, these additional analyses suggest that the presence of TGn plus a -10 box is insufficient to create promoter activity, and that the UP element does not play a significant role in promoter emergence or evolution.

Reviewer #3 (Public Review):

Summary:

Like many papers in the last 5-10 years, this work brings a computational approach to the study of promoters and transcription, but unfortunately disregards or misrepresents much of the existing literature and makes unwarranted claims of novelty. My main concerns with the current paper are outlined below although the problems are deeply embedded.

We thank Reviewer #3 for taking the time to review this manuscript. We have made extensive changes to address their concerns about our work.

Strengths:

The data could be useful if interpreted properly, taking into account i) the role of translation ii) other promoter elements, and iii) the relevant literature.

Weaknesses:

(1) Incorrect assumptions and oversimplification of promoters.

- There is a critical error on line 68 and Figure 1A. It is well established that the -35 element consensus is TTGACA but the authors state TTGAAA, which is also the sequence represented by the sequence logo shown and so presumably the PWM used. It is essential that the authors use the correct -35 motif/PWM/consensus. Likely, the authors have made this mistake because they have looked at DNA sequence logos generated from promoter alignments anchored by either the position of the -10 element or transcription start site (TSS), most likely the latter. The distance between the TSS and -10 varies. Fewer than half of E. coli promoters have the optimal 7 bp separation with distances of 8, 6, and 5 bp not being uncommon (PMID: 35241653). Furthermore, the distance between the -10 and -35 elements is also variable (16,17, and 18 bp spacings are all frequently found, PMID: 6310517). This means that alignments, used to generate sequence logos, have misaligned -35 hexamers. Consequently, the true consensus is not represented. If the alignment discrepancies are corrected, the true consensus emerges. This problem seems to permeate the whole study since this obviously incorrect consensus/motif has been used throughout to identify sequences that resemble -35 hexamers.

We respectfully but strongly disagree that our analysis has misrepresented the true nature of -35 boxes. First, accounting for more A’s at position 5 in the PWM is not going to lead to a “critical error.” This is because positions 4-6 of the motif barely have any information content (bits) compared to positions 1-3 (see Fig 1A). This assertion is not just based on our own PWM, but based on ample precedent in the literature. In PMID 14529615, TTG is present in 38% of all -35 boxes, but ACA only in 8%. In PMID 29388765, with the -10 instance TATAAT, the -35 instance TTGCAA yields stronger promoters compared to the -35 instance TTGACA (See their Figure 3B).

In PMID 29745856 (Figure 2), the most information content lies in positions 1-3, with the A and C at position 5 both nearly equally represented, as in our PWM. In PMID 33958766 (Figure 1) an experimentally-derived -35 box is even reduced to a “partial” -35 box which only includes positions 1 and 2, with consensus: TTnnnn.

In addition, we did not derive the PWMs as the reviewer describes. The PWMs we use are based on computational predictions that are in excellent agreement with experimental results. Specifically, the PWMs we use are from PMID 29728462, which acquired 145 -10 and -35 box sequences from the top 3.3% of computationally predicted boxes from Regulon DB. See PMID 14529615 for the computational pipeline that was used to derive the PWMs, which independently aligns the -10 and -35 boxes to create the consensus sequences. The -35 PWMs significantly and strongly correlates with an experimentally derived -35 box (see Supporting Information from Figure S4 of Belliveau et al., PNAS 2017. Pearson correlation coefficient = 0.89). Within the 145 -35 boxes, the exact consensus sequence (TTGACA) that Reviewer #3 is concerned about is present 6 times in our matrix, and has a PWM score above the significance threshold. In other words, TTGACA, is classified to be a -35 box in our dataset.

We now provide DNA sequences for each of the figures to improve accessibility and reproducibility. A reader can now use any PWM or method they wish to interpret the data.

- An uninformed person reading this paper would be led to believe that prokaryotic promoters have only two sequence elements: the -10 and -35 hexamers. This is because the authors completely ignore the role of the TG motif, UP element, and spacer region sequence. All of these can compensate for the lack of a strong -35 hexamer and it's known that appending such elements to a lone -10 sequence can create an active promoter (e.g. PMIDs 15118087, 21398630, 12907708, 16626282, 32297955). Very likely, some of the mutations, classified as not corresponding to a -10 or -35 element in Figure 2, target some of these other promoter motifs.

Thank you for bringing this oversight to our attention. We have performed two independent analyses to explore the role of TGn in promoter emergence in evolution. First, we computationally searched for -10 boxes with the bases TGn immediately upstream of them in the parent sequences, and found 18 of these “extended -10 boxes” in the parents (lines 143145):

“On average, each parent sequence contains ~5.32 -10 boxes and ~7.04 -35 boxes (Fig S1). 18 of these -10 boxes also include the TGn motif upstream of the hexamer.”

However, only 20% of these boxes were found in parents with promoter activity (lines 182-185):

“We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9-RFP, P10-RFP, P11GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25-RFP).”

Second, we computationally searched through all of the daughter sequences to identify new -10 boxes with TGn immediately upstream. We found 114 -10 boxes with the bases TGn upstream. However, only 5 new -10 boxes (2 with TGn) were associated with increasing fluorescence (lines 338-345):

“On average, 39.5 and 39.4 new -10 and -35 boxes emerged at unique positions within the daughter sequences of each mutagenized parent (Fig 3A,B), with 1’562 and 1’576 new locations for -10 boxes and -35 boxes, respectively. ~22% (684/3’138) of these new boxes are spaced 15-20 bp away from their cognate box, and ~7.3% (114/1’562) of the new -10 boxes have the TGn motif upstream of them. However, only a mere five of the new -10 boxes and four of the new 35 boxes are significantly associated with increasing fluorescence by more than +0.5 a.u. (Fig 3C,D).”

In addition, we now study the role of UP elements. This analysis showed that the UP element plays a negligible role in promoter emergence within our dataset.  It is discussed in a new subsection of the results (lines 591-608) and in the newly added Figure S13.

Collectively, these additional analyses suggest that the presence of TGn plus a -10 box is insufficient to create promoter activity, and that the UP element does not play a significant role in promoter emergence or evolution.

- The model in Figure 4C is highly unlikely. There is no evidence in the literature that RNAP can hang on with one "arm" in this way. In particular, structural work has shown that sequencespecific interactions with the -10 element can only occur after the DNA has been unwound (PMID: 22136875). Further, -10 elements alone, even if a perfect match to the consensus, are non-functional for transcription. This is because RNAP needs to be directed to the -10 by other promoter elements, or transcription factors. Only once correctly positioned, can RNAP stabilise DNA opening and make sequence-specific contacts with the -10 hexamer. This makes the notion that RNAP may interact with the -10 alone, using only domain 2 of sigma, extremely unlikely.

This is a valid criticism, and we thank the reviewer for catching this problem. In response, we have removed the model and pertinent figures throughout the entire manuscript.

(2) Reinventing the language used to describe promoters and binding sites for regulators.

- The authors needlessly complicate the narrative by using non-standard language. For example, On page 1 they define a motif as "a DNA sequence computationally predicted to be compatible with TF binding". They distinguish this from a binding site "because binding sites refer to a location where a TF binds the genome, rather than a DNA sequence". First, these definitions are needlessly complicated, why not just say "putative binding sites" and "known binding sites" respectively? Second, there is an obvious problem with the definitions; many "motifs" with also be "bindings sites". In fact, by the time the authors state their definitions, they have already fallen foul of this conflation; in the prior paragraph they stated: "controlled by DNA sequences that encode motifs for TFs to bind". The same issue reappears throughout the paper.

We agree that this was needlessly complicated. We now just refer to every sequence we study as a motif. A -10 box is a motif, a -35 box is a motif, a putative H-NS binding site is an H-NS motif, etc. The word “binding site” no longer occurs in the manuscript.

- The authors also use the terms "regulatory" and non-regulatory" DNA. These terms are not defined by the authors and make little sense. For instance, I assume the authors would describe promoter islands lacking transcriptional activity (itself an incorrect assumption, see below)as non-regulatory. However, as horizontally acquired sections of AT-rich DNA these will all be bound by H-NS and subject to gene silencing, both promoters for mRNA synthesis and spurious promoters inside genes that create untranslated RNAs. Hence, regulation is occurring.

Another fair point. We have thus changed the terminology throughout to “promoter” and “nonpromoter.”

- Line 63: "In prokaryotes, the primary regulatory sequences are called promoters". Promoters are not generally considered regulatory. Rather, it is adjacent or overlapping sites for TFs that are regulatory. There is a good discussion of the topic here (PMID: 32665585). 

We have rewritten this. The sentence now reads (lines 67-69):

“A canonical prokaryotic promoter recruits the RNA polymerase subunit σ70 to transcribe downstream sequences (Burgess et al., 1969; Huerta and Collado-Vides, 2003; Paget and Helmann, 2003; van Hijum et al., 2009).”

(3) The authors ignore the role of translation.

- The authors' assay does not measure promoter activity alone, this can only be tested by measuring the amount of RNA produced. Rather, the assay used measures the combined outputs of transcription and translation. If the DNA fragments they have cloned contain promoters with no appropriately positioned Shine-Dalgarno sequence then the authors will not detect GFP or RFP production, even though the promoter could be making an RNA (likely to be prematurely terminated by Rho, due to a lack of translation). This is known for promoters in promoter islands (e.g. Figure 1 in PMID: 33958766).

We agree that this is definitely a limitation of our study, which we had not discussed sufficiently. In response, we now discuss this limitation in a new section of the discussion (lines 680-686):

“Second, we measure protein expression through fluorescence as a readout for promoter activity. This readout combines transcription and translation. This means that we cannot differentiate between transcriptional and post-transcriptional regulation, including phenomena such as premature RNA termination (Song et al., 2022; Uptain and Chamberlin, 1997), post-transcriptional modifications (Mohanty and Kushner, 2006), and RNA-folding from riboswitch-like sequences (Mandal and Breaker, 2004).”

- In Figure S6 it appears that the is a strong bias for mutations resulting in RFP expression to be close to the 3' end of the fragment. Very likely, this occurs because this places the promoter closer to RFP and there are fewer opportunities for premature termination by Rho.

The reviewer raises a very interesting possibility. To validate it, we have performed the following analysis. We took the RFP expression values from the 9’934 daughters with single mutations in all 25 parent sequences (P1-RFP, P2-RFP, … P25-RFP), and plotted the location of the single mutation (horizontal axis) against RFP expression (vertical axis) in Author response image 2. 

Author response image 2.

The distribution is uniform across the sequences, showing that distance from the RBS is not likely the reason for this observation. Since this analysis was uninformative with respect to distance from the RBS, we chose not to include it in the manuscript.

(4) Ignoring or misrepresenting the literature.

- As eluded to above, promoter islands are large sections of horizontally acquired, high ATcontent, DNA. It is well known that such sequences are i) packed with promoters driving the expression on RNAs that aren't translated ii) silenced, albeit incompletely, by H-NS and iii) targeted by Rho which terminates untranslated RNA synthesis (PMIDs: 24449106, 28067866, 18487194). None of this is taken into account anywhere in the paper and it is highly likely that most, if not all, of the DNA sequences the authors have used contain promoters generating untranslated RNAs.

Thank you for pointing out that our original submission was incomplete in this regard. We address these concerns by new analyses, including some new experiments. First, Rhodependent termination is associated with the RUT motif, which is very rich in Cytosines (PMID: 30845912). Given that our sequences confer between 65%-78% of AT-content, canonical rhodependent termination is unlikely. However, we computationally searched for rho-dependent terminators using the available code from PMID: 30845912, but the algorithm did not identify any putative RUTs. Because this analysis was not informative, we did not include it in the paper.

We analyzed the role of H-NS on promoter emergence and evolution within our dataset using both experimental and computational approaches. These additional analyses are now shown in the newly-added Figure 5 and the newly-added Figure S12. We found that H-NS represses P22-GFP and P12-RFP and affects the bidirectionality of P20. More specifically, to analyze the effects of H-NS, we first compared the fluorescence levels of parent sequences in a Δhns background vs the wild-type (dh5α) background in Figure 5A. We found 6 candidate H-NS targets, with P22-GFP and P12-RFP exhibiting the largest changes in fluorescence (lines 496506):

“We plot the fluorescence changes in Fig 5A as distributions for the 50 parents, where positive and negative values correspond to an increase or decrease in fluorescence in the Δhns background, respectively. Based on the null hypothesis that the parents are not regulated by H-NS, we classified outliers in these distributions (1.5 × the interquartile range) as H-NS-target candidates. We refer to these outliers as “candidates” because the fluorescence changes could also result from indirect trans-effects from the knockout (Mattioli et al., 2020; Metzger et al., 2016). This approach identified 6 candidates for H-NS targets (P2-GFP, P19-GFP, P20-GFP, P22-GFP, P12-RFP, and P20-RFP). For GFP, the largest change occurs in P22-GFP, increasing fluorescence ~1.6-fold in the mutant background (two-tailed t-test, p=1.16×10-8) (Fig 5B). For RFP, the largest change occurs in P12-RFP, increasing fluorescence ~0.5-fold in the mutant background (two-tailed t-test, p=4.33×10-10) (Fig 5B).” 

We also observed that the Δhns background affected the bidirectionality of P20 (lines 507-511):

“We note that for template P20, which is a bidirectional promoter, GFP expression increases ~2.6-fold in the Δhns background (two-tailed t-test, p=1.59×10-6). Simultaneously, RFP expression decreases ~0.42-fold in the Δhns background (two-tailed t-test, p=4.77×10-4) (Fig S12A). These findings suggest that H-NS also modulates the directionality of P20’s bidirectional promoter through either cis- or trans-effects.”

We then searched for regions where losing H-NS motifs in hotspots significantly changed fluorescence. We identified 3 motifs in P12-RFP and P22-GFP (lines 522-528):

“For P22-GFP, a H-NS motif lies 77 bp upstream of the mapped promoter. Mutations which destroy this motif significantly increase fluorescence by +0.52 a.u. (two-tailed MWU test, q=1.07×10-3) (Fig 5E). For P12-RFP, one H-NS motif lies upstream of the mapped promoter’s -35 box, and the other upstream of the mapped promoter’s -10 box. Mutations that destroy these H-NS motifs significantly increase fluorescence by +0.53 and +0.51 a.u., respectively (two-tailed MWU test, q=3.28×10-40 and q=4.42 ×10-50) (Fig 5F,G). Based on these findings, we conclude that these motifs are bound by H-NS.”

We are grateful for the suggestion to look at the role of H-NS in our dataset. Our analysis revealed a more plausible explanation to what we formerly referred to as a “Tandem Motif” in the original submission. Previously, we had shown that in P12-RFP, when a -35 box is created next to the promoter’s -35 box, or a -10 box next to the promoter’s -10 box, that expression decreases. These new -10 and -35 boxes, however, also overlap with the two H-NS motifs in P12-RFP. We tested these exact point mutations in reporter plasmids and in the Δhns background, and found that the Δhns background rescues this loss in expression (see Figure S12). This analysis is in the newly added subsection: “The binding of H-NS changes when new 10 and -35 boxes are gained” and can be found at lines 529-563. We summarize the findings in a final paragraph of the section (lines 556-563):

“To summarize, we present evidence that H-NS represses both P22-GFP and P12-RFP in cis. H-NS also modulates the bidirectionality of P20-GFP/RFP in cis or trans. In P22-GFP, the strongest H-NS motif lies upstream of the promoter. In P12-RFP, the strongest H-NS motifs lie  upstream of the -10 and -35 boxes of the promoter. We note that there are 16 additional H-NS motifs surrounding the promoter in P12-RFP that may also regulate P12-RFP (Fig S12G). Mutations in two of these two H-NS motifs can create additional -10 and -35 boxes that appear to lower expression. However, the effects of these mutations are insignificant in the absence of H-NS, suggesting that these mutations actually modulate H-NS binding.”

We also agree that the majority of these sequences are likely driving the expression of many untranslated RNAs (see Purtov et al., 2014). We thus now define a promoter more carefully as follows (lines 113-119):

“In this study, we define a promoter as a DNA sequence that drives the expression of a (fluorescent) protein whose expression level, measured by its fluorescence, is greater than a defined threshold. We use a threshold of 1.5 arbitrary units (a.u.) of fluorescence. This definition does not distinguish between transcription and translation. We chose it because protein expression is usually more important than RNA expression whenever natural selection acts on gene expression, because it is the primary phenotype visible to natural selection (Jiang et al., 2023).” 

We also state this as a limitation of our study in the Discussion (lines 680-686):

“Second, we measure protein expression through fluorescence as a readout for promoter activity. This readout combines transcription and translation. This means that we cannot differentiate between transcriptional and post-transcriptional regulation, including phenomena such as premature RNA termination (Song et al., 2022; Uptain and Chamberlin, 1997), post-transcriptional modifications (Mohanty and Kushner, 2006), and RNA-folding from riboswitch-like sequences (Mandal and Breaker, 2004).”

- The authors state that GC content does not correlate with the emergence of new promoters. It is known that GC content does correlate to the emergence of new promoters because promoters are themselves AT-rich DNA sequences (e.g. see Figure 1 of PMID: 32297955). There are two reasons the authors see no correlation in this work. First, the DNA sequences they have used are already very AT-rich (between 65 % and 78 % AT-content). Second, they have only examined a small range of different AT-content DNA (i.e. between 65 % and 78 %). The effect of AT-content on promoter emerge is most clearly seen between AT-content of between around 40 % and 60 %. Above that level, the strong positive correlation plateaus.

We respectfully disagree that the reviewer’s point is pertinent because what the reviewer is referring to is the likelihood that the sequence is a promoter, which indeed increases with AT content, but we are focused on the likelihood that a sequence becomes a promoter through DNA mutation. We note that if a DNA sequence is more AT-rich, then it is more likely to have -10 and -35 boxes, because their consensus sequences are also AT-rich. However, H-NS and other transcriptional repressors also bind to AT-rich sequences. This could also explain the saturation observed above 60% AT-content in PMID 32297955. Perhaps we can address this trend in future works.

- Once these authors better include and connect their results to the previous literature, they can also add some discussion of how previous papers in recent years may have also missed some of this important context.

We apologize for this oversight. We have rewritten the Discussion section to include the following points below. Many of the newly added references come from the group of David Grainger, who works on H-NS repression, bidirectional promoters, promoter emergence, promoter motifs, and spurious transcription in E. coli. More specifically:

(1) The role of pervasive transcription and the likelihood of promoter emergence (lines 614-621):

“Instead, we present evidence that promoter emergence is best predicted by the level of background transcription each non-promoter parent produces, a phenomenon also referred to as “pervasive transcription” (Kapranov et al., 2007).

From an evolutionary perspective, this would suggest that sequences that produce such pervasive transcripts – including the promoter islands (Panyukov and Ozoline, 2013) and the antisense strand of existing promoters (Dornenburg et al., 2010; Warman et al., 2021), may have a proclivity for evolving de-novo promoters compared to other sequences (Kapranov et al., 2007; Wade and Grainger, 2014).”

(2) How our results contradict the findings from Bykov et al., 2020 (lines 622-640):

“A previous study randomly mutagenized the appY promoter island upstream of a GFP reporter, and isolated variants with increased and decreased GFP expression. The authors found that variants with higher GFP expression acquired mutations that 1) improve a -10 box to better match its consensus, and simultaneously 2) destroy other -10 and -35 boxes (Bykov et al., 2020). The authors concluded that additional -10 and -35 boxes repress expression driven by promoter islands. Our data challenge this conclusion in several ways. 

First, we find that only ~13% of -10 and -35 boxes in promoter islands actually contribute to promoter activity. Extrapolating this percentage to the appY promoter island, ~87% (100% - 13%) of the motifs would not be contributing to its activity. Assuming the appY promoter island is not an outlier, this would insinuate that during random mutagenesis, these inert motifs might have accumulated mutations that do not change fluorescence. Indeed, Bykov et al. (Bykov et al., 2020) also found that a similar frequency of -10 and -35 boxes were destroyed in variants selected for lower GFP expression, which supports this argument. Second, we find no evidence that creating a -10 or -35 box lowers promoter activity in any of our 50 parent sequences. Third, we also find no evidence that destruction of a -10 or -35 box increases promoter activity without plausible alternative explanations, i.e. overlap of the destroyed box with a H-NS site, destruction of the promoter, or simultaneous creation of another motif as a result of the destruction. In sum, -10 and 35 boxes are not likely to repress promoter activity.”

(3) How other sequence features besides the -10 and -35 boxes may influence promoter emergence and activity (lines 661-671):

“These findings suggest that we are still underestimating the complexity of promoters. For instance, the -10 and -35 boxes, extended -10, and the UP-element may be one of many components underlying promoter architecture. Other components may include flanking sequences (Mitchell et al., 2003), which have been observed to play an important role in eukaryotic transcriptional regulation (Afek et al., 2014; Chiu et al., 2022; Farley et al., 2015; Gordân et al., 2013). Recent studies on E. coli promoters even characterize an AT-rich motif within the spacer sequence (Warman et al., 2020), and other studies use longer -10 and -35 box consensus sequences (Lagator et al., 2022). Another possibility is that there is much more transcriptional repression in the genome than anticipated (Singh et al., 2014). This would also coincide with the observed repression of H-NS in P22-GFP and P12-RFP, and accounts of H-NSrepression in the full promoter island sequences (Purtov et al., 2014).”

(4) The limits of our experimental methodology (lines 675-686):

“Additionally, future studies will be necessary to address the limitations of our own work. First, we use binary thresholding to determine i) the presence or absence of a motif, ii) whether a sequence has promoter activity or not, and iii) whether a part of a sequence is a hotspot or not. While chosen systematically, the thresholds we use for these decisions may cause us to miss subtle but important aspects of promoter evolution and emergence. Second, we measure protein expression through fluorescence as a readout for promoter activity. This readout combines transcription and translation. This means that we cannot differentiate between transcriptional and post-transcriptional regulation, including phenomena such as premature RNA termination (Song et al., 2022; Uptain and Chamberlin, 1997), posttranscriptional modifications (Mohanty and Kushner, 2006), and RNA-folding from riboswitch-like sequences (Mandal and Breaker, 2004) “

(5) An updated take-home message (lines 687-694):

“Overall, our study demonstrates that -10 and -35 boxes neither prevent existing promoters from driving expression, nor do they prevent new promoters from emerging by mutation. It shows how mutations can create new -10 and -35 boxes near or on top of preexisting ones to modulate expression. However, randomly creating a new -10 or -35 box will rarely create a new promoter, even if the new box is appropriately spaced upstream or downstream of a cognate box. Ultimately our study demonstrates that promoter models need to be further scrutinized, and that using mutagenesis to create de-novo promoters can provide new insights into promoter regulatory logic.”

(5) Lack of information about sequences used and mutations.

- To properly assess the work any reader will need access to the sequences cloned at the start of the work, where known TSSs are within these sequences (ideally +/- H-NS, which will silence transcription in the chromosomal context but may not when the sequences are removed from their natural context and placed in a plasmid). Without this information, it is impossible to assess the validity of the authors' work.

Thank you for raising this point. Please see Data S1 for the 25 template sequences (P1-P25) used in this study, and Data S2 for all of the daughter sequences.

For brevity, we have addressed the reviewer’s request to look at the role of H-NS in their comment (4) “Ignoring or misrepresenting the literature.”

We do not have information about the predicted transcription start sites (TSS) for the parent sequences because the program which identified them (Platprom) is no longer available. Regardless, having TSS coordinates would not validate or invalidate our findings, since we already know that the promoter islands produce short transcripts throughout their sequences, and we are primarily interested in promoters which can produce complete transcripts.

- The authors do not account for the possibility that DNA sequences in the plasmid, on either side of the cloned DNA fragment, could resemble promoter elements. If this is the case, then mutations in the cloned DNA will create promoters by "pairing up" with the plasmid sequences. There is insufficient information about the DNA sequences cloned, the mutations identified, or the plasmid, to determine if this is the case. It is possible that this also accounts for mutational hotspots described in the paper.

We agree that these are important points. To address the criticism that we provided insufficient information, we now redesigned all our figures to provide this information. Specifically, the figures now include the DNA sequences, their PWM predictions, and the exact mutations that lead to promoter activity. The figures with these changes are Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12. We now also provide more details about pMR1 in a new section of the methods (lines 740-748):

“Plasmid MR1 (pMR1)

The plasmid MR1 (pMR1) is a variant of the plasmid RV2 (pRV2) in which the kan resistance gene has been swapped with the cm resistance gene (Guazzaroni and Silva-Rocha, 2014). Plasmid pMR1 encodes the BBa_J34801 ribosomal binding site (RBS, AAAGAGGAGAAA) 6 bp upstream of the start codon for GFP(LVA). The plasmid also encodes a putative RBS (AAGGGAGG) (Cazemier et al., 1999) 5 bp upstream of the start codon for mCherry on the opposite strand.

The plasmid additionally contains the low-to-medium copy number origin of replication p15A (Westmann et al., 2018).

A map of the plasmid is available on the Github repository: https://github.com/tfuqua95/promoter_islands “

The reviewer also makes a valid point about promoter elements of the plasmid itself. We addressed it with the following new analyses. First we re-examined each of the examples where new -10 and -35 boxes are gained or lost, to see if any of these hotspots occur on the flanking ends of the parent sequences. We looked specifically at the ends because they could potentially interact with -10 and -35 box-like sequences on the plasmid to form a promoter. 

Only one of these hotspots (out of 27) occurred at the end of the cloned sequences, and is thus a candidate for the phenomenon the reviewer hypothesized. This hotspot occurs in P9-GFP, where gaining a -10 box at the left flank increases expression (see Figure S8E-F’). There is indeed a -35 box 22-23 bp upstream of this -10 box on the plasmid, which could potentially affect promoter activity. 

We tested the GFP expression of a construct harboring the point mutation which creates this -10 box on the left flank of P9-GFP. However, there was no significant difference in fluorescence between this construct and the wile-type P9-GFP (see Figure S8E-F’). Thus, this -35 box on pMR1 is not likely creating a new promoter.

(6) Overselling the conclusions.

Line 420: The paper claims to have generated important new insights into promoters. At the same time, the main conclusion is that "Our study demonstrates that mutations to -10 and -35 boxes motifs are the primary paths to create new promoters and to modulate the activity of existing promoters". This isn't new or unexpected. People have been doing experiments showing this for decades. Of course, mutations that make or destroy promoter elements create and destroy promoters. How could it be any other way?

In hindsight, we agree that the original conclusion was not very novel. Our new conclusion is that -10 and -35 boxes do not repress transcription, and that our current promoter models, even with the additional motifs like the UP-element and the extended -10, are insufficient to understand promoters (lines 687-694):

“Overall, our study demonstrates that -10 and -35 boxes neither prevent existing promoters from driving expression, nor do they prevent new promoters from emerging by mutation. It shows how mutations can create new -10 and -35 boxes near or on top of preexisting ones to modulate expression. However, randomly creating a new -10 or -35 box will rarely create a new promoter, even if the new box is appropriately spaced upstream or downstream of a cognate box. Ultimately our study demonstrates that promoter models need to be further scrutinized, and that using mutagenesis to create de-novo promoters can provide new insights into promoter regulatory logic.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I would like to start by thanking the authors for presenting an interesting and well-written article for review. This paper is a welcome addition to the field, addressing modern questions in the longstanding area of bacterial gene regulation. It is both enlightening and inspiring. While I do have suggestions, I hope these are not perceived as a lack of optimism for the work.

Thank you for your kind words and suggestions, and for providing an astute and constructive review. We feel that manuscript has greatly improved with your suggested changes.

ABSTRACT:

Line 11: The sentence, "It is possible that these motifs influence..." Could be rewritten to be clearer as it is the most important point of the manuscript. It is not obvious that you're talking about how the local landscape of motifs affects the probability of promoters evolving/devolving in this location.

We have changed the sentence to read, “Here, we ask whether the presence of such motifs in different genetic sequences influences promoter evolution and emergence.”

INTRODUCTION:

Line 68: Is the -35 consensus motif not TTGACA? Here it is listed as TTGAAA.

Corrected from TTGAAA to TTGACA

RESULTS:

Line 92-94. In finding that the. The main takeaway from this work is that different sequences have different likelihoods of mutations creating promoters and so I believe this claim could be explored deeper with more quantitative information. Could the authors supplement this claim by including? Could you look at whether there is a correlation between the baseline expression of a parent sequence and Pnew? I expect even the inactive sequences to have some variability in measured expression.

Thank you for this great idea. We followed up on it by plotting the baseline parent sequence fluorescence scores against Pnew. You are indeed correct, i.e., Pnew increases with baseline expression following a sigmoid function, and is now shown in Figure 1D. To report our new observations, we have added the following section to the Results (lines 219-232):

“Although mutating each of the 40 non-promoter parent sequences could create promoter activity, the likelihood Pnew that a mutant has promoter activity, varies dramatically among parents. For each non-promoter parent, Fig 1D shows the percentage of active daughter sequences. The median Pnew is 0.046 (std. ± 0.078), meaning that ~4.6% of all mutants have promoter activity. The lowest Pnew is 0.002 (P25-GFP) and the highest 0.41 (P8-RFP), a 205-fold difference.

We hypothesized that these large differences in Pnew could be explained by minute differences in the fluorescence scores of each parent, particularly if its score was below 1.5 a.u. Plotting the fluorescence scores of each parent (N=50) and their respective Pnew values as a scatterplot (Fig 1E), we can fit these values to a sigmoid curve (see methods). This finding helps to explain why P8-RFP has a high Pnew (0.41) and P25-GFP a low Pnew (0.002), as their fluorescence scores are 1.380 and 1.009 a.u., respectively. The fact that the inflection point of the fitted curve is at 1.51 a.u. further justifies our use of 1.5 a.u. as a cutoff for promoter and non-promoter activity.”

Another potentially interesting analysis would be to see if k-mer content is correlated with Pnew. That is, determine the abundance of all hexamers in the sequence and see if Pnew is correlated with the number of hexamers present that is one nucleotide distance away from the consensus motifs (such as TcGACA or TAcAAT).

We performed the suggested analysis by searching for k-mers that correlate with Pnew and found that no k-mer significantly correlates with Pnew (lines 240-248):

“We then asked whether any k-mers ranging from 1-6 bp correlated with the non-promoter Pnew values (5,460 possible k-mers). 718 of these 1-6 bp k-mers are present 3 or more times in at least one non-promoter parent. We calculated a linear regression between the frequency of these 718 k-mers and each Pnew value, and adjusted the p-values to respective q-values (Benjamini-Hochberg correction, FDR=0.05). This analysis revealed six k-mers: CTTC, GTTG,

ACTTC, GTTGA, AACTTC, TAACTT which correlate with Pnew. However, these correlations are heavily influenced by an outlying Pnew value of 0.41 (P8-RFP) (Fig S5C-H), and upon removing P8-RFP from the analysis, no k-mer significantly correlates with Pnew (data not shown)”

Line 152-157: How did you define the thresholds for 'active' or 'inactive'? It is not clear in the methods how this distinction was made.

We have more clearly defined these thresholds in the text. A sequence with promoter activity has a fluorescence score greater than 1.5 a.u. (lines 168-172):

“We declared a daughter sequence to have promoter activity or to be a promoter if its score was greater than or equal to 1.5 a.u., as this score lies at the boundary between no fluorescence and weak fluorescence based on the sort-seq bins (methods). Otherwise, we refer to a daughter sequence as having no promoter activity or being a non-promoter.”

Lines: 152-157: In trying to find the parent expression levels, no figure was available showing the distribution of parent expression levels. Furthermore, In looking at Data S2 & filtering out for sequences with distance 0 from the parent, I found the most active sequences did not match up with the sequences described as active in this section (e.g. p19 and p20 have a higher topstrand mean over P22, yet are not listed as active top strand sequences).

We really appreciate you taking the time to examine the supplemental data. We previously listed the parents that had only GFP activity but no RFP activity (P22), and only RFP activity but no GFP activity (P6, P12, P13, P18, P21). We then said that P19 and P20 were bidirectional promoters, because they showed both GFP and RFP activity. In hindsight, we realize that our wording was confusing. We thus rewrote the affected paragraph, such that the bidirectional promoters are now in both lists of GFP/RFP active parents. We also now make the distinction between “templates” which comprise our 25 promoter island fragments, and “parents”, where we treat both strands separately (50 parents total). The paragraph in question now reads (lines 173-187):

“Because some sequences in our library are unmutated parent sequences, we determined that 10/50 of the parent sequences already encode promoter activity before mutagenesis. Specifically, three parents drove expression on the top strand (P19-GFP, P20-GFP, P22-GFP), and five did on the bottom strand (P6-RFP, P12-RFP, P13-RFP, P18-RFP, P19-RFP, P20-RFP, P21-RFP). Two parents harbor bidirectional promoters (P19 and P20). The remaining 40 parent sequences are non-promoters, with an average fluorescence score of 1.39 a.u. We note that some of these parents have a fluorescence score higher than 1.39 a.u., but less than 1.50 a.u. such as P8-RFP (1.38 a.u.), P16-RFP (1.39 a.u.), P9-GFP (1.49 a.u.), and P1-GFP (1.47 a.u.). Whether these are truly “promoters” or not, is based solely on our threshold value of 1.5 a.u. We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9RFP, P10-RFP, P11-GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25RFP). See Fig S4 for fluorescence score distributions for each parent and its daughters, and Data S2 for all daughter sequence fluorescence scores.”

Please include a supplementary figure showing the different parent expression levels (GFP mean +/- sd). Also, please explain the discrepancy in the 'active sequences' compared to Data S2 or correct my misunderstanding.

We have added this plot to Figure S4B. The discrepancy arose because we listed the parents that had only GFP activity but no RFP activity (P22), and only RFP activity but no GFP activity (P6, P12, P13, P18, P21). We then said that P19 and P20 were bidirectional promoters, because they showed both GFP and RFP activity. previous response regarding the ambiguity.

Line 182: I do not see 'Fuqua and Wagner 2023' in the references (though I am familiar with the preprint).

We have added Fuqua and Wagner, BiorXiv 2023 to the references.

Lines 197 - 200: The distribution of hotspot locations should be compared to the distribution of mutations in the library. e.g. It is not notable that 17% of mutations are in -10 motifs if 17% of all mutations are in -10 motifs.

Thank you for raising this point. To address it, we carried out a computational analysis where we randomly scrambled the nucleotides of each parent sequence while maintaining the coordinates for each mutual information “hotspot.” This scrambling results in significantly less overlap with hotspots and boxes. This analysis is now depicted in Figure 2C and written in lines 272-296.

Lines 253-264: Examples 3B, 3D, and 3F should indicate the spacing between the new and existing motifs. Are these close to the 15-19 bp spacer lengths preferred by sigma70?

Point well taken. We now annotate the spacing of motifs in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, and S11. We note that in many cases, high-scoring PWM hits for the same motif can overlap (i.e. two -10 motifs or two -35 motifs overlap). Additionally, the proximity of a 35 and -10 box does not guarantee that the two boxes are interacting. Together, these two facts can result in an ambiguity of the spacer size between two boxes. To avoid any reporting bias, we thus often report spacer sizes as a range (see Figure panels 4F, S8D, S8F-L, S9A, S9H, S10A, and S10E). The smallest spacer we annotate is in Figure 4F with 10 bp, and the largest is in Figure S8D with 26 bp. Any more “extreme” distances are not annotated, and for the reader to decide if an interaction is present or not.

Line 255: While fun, I am concerned about the 'Shiko' analogy. My understanding is the prevailing theory is that -35 recognition occurs before -10 recognition (https://doi.org/10.1073/pnas.94.17.9022, 10.1101/sqb.1998.63.141). Given this, the 'Shiko -35' concept in 3H is a bit awkward as it suggests that sigma70 stops at -10 motifs before planting down on the -35. Considering the cited paper is still in the preprint stages (and did not observe these Shiko -35 emergences), I am concerned about how this particular example will be received by the community. Perhaps more care could be done to verify that this example is consistent with generally accepted mechanisms of promoter recognition or a short clarification could be added to clarify the extent of the analogy.

Thank you for raising this point. We decided to remove the Shiko analogy, because several readers assumed that it relates to the physical binding of RNA polymerase, rather than being an evolutionary mechanism of mutations forming complementary motifs in a stepwise manner.

Lines 323-326: It would be helpful to describe a more systematic approach to defining emergence events into different categories. A clear definition of each category in the methods or main text would help others consistently refer to these concepts in the future. This could be helped by showing the actual parent vs daughter sequences as a supplementary figure to figures 4B, 4D, & 4G.

We agree this could have been more clearly communicated. We have addressed this by 1) simplifying the nomenclatures of these categories and  2) clearly defining these categories, and 3) showing the actual parent vs daughter sequences in Figure 4, and Supplemental Figures S9, S10, S11, and S12. More specifically:

(1) Simplifying the nomenclature. We highlight events where gaining new -10 and -35 boxes can modify the promoter activity of parent sequences with promoter activity. This occurs when a new -10 or -35 box appears that partially overlaps with the -10 or -35 box of the actual promoter. Thus, we rename two terms: hetero-gain and homo-gain, shown in Figure 4B:

(2) We clearly define these categories (lines 430-435):

“We found that these mutations frequently create new boxes overlapping those we had identified as part of a promoter (Fig S9). This occurs when mutations create a -10 box overlapping a -10 box, a -35 box overlapping a 35 box, a -10 box overlapping a -35 box, or a -35 box overlapping a -10 box. We call the resulting event a “homogain” when the new box is of the same type as the one it overlaps, and otherwise a “hetero-gain”. In either case, the creation of the new box does not always destroy the original box.”

In the original manuscript, there was an additional third category, where gaining a -35 box upstream of the promoter’s -35 box, and gaining a -10 box upstream of the promoter’s -10 box decreased expression. We referred to this as a “tandem motif” and it can be found in Figure S12C,D. However, in response to comment “(4) Ignoring or misrepresenting the literature” from Reviewer #3, we carried out an analysis of the binding of H-NS (see Figure 5 and Figure S12). This analysis revealed that this “tandem motif” phenomenon was actually the result of changing the affinity of H-NS to these regions. Thus, the “tandem motif” is probably spurious.

DISCUSSION:

Line 378-379: Since hotspots are essentially areas where promoters appear, wouldn't it be obvious that having more hotspots (i.e. areas where more promoters appear) would equate to a higher probability of new promoters? It would be helpful to clarify why this isn't obvious. This could be resolved by adding more complexity to the statement, such as showing that the level of mutual information found in a hotspot or across all hotspots in a sequence is correlated with Pnew.

A fair criticism. In response, we have chosen to remove the analysis of this trend from the manuscript entirely. (Additionally, Pnew and mutual information calculations both relied on the fluorescence scores of daughter sequences, so the finding was circular in its logic.)

Line 394-396: This comparison of findings to Bykov et al should include a bit more justification for the proposed mechanism and how it specifically was observed in this paper. What did they observe and how do these findings relate?

We gladly followed this suggestion, and added the following two paragraphs to the discussion (lines 622-640).

“A previous study randomly mutagenized the appY promoter island upstream of a GFP reporter, and isolated variants with increased and decreased GFP expression. The authors found that variants with higher GFP expression acquired mutations that 1) improve a -10 box to better match its consensus, and simultaneously 2) destroy other -10 and -35 boxes (Bykov et al., 2020). The authors concluded that additional -10 and -35 boxes repress expression driven by promoter islands. Our data challenge this conclusion in several ways. 

First, we find that only ~13% of -10 and -35 boxes in promoter islands actually contribute to promoter activity. Extrapolating this percentage to the appY promoter island, ~87% (100% - 13%) of the motifs would not be contributing to its activity. Assuming the appY promoter island is not an outlier, this would insinuate that during random mutagenesis, these inert motifs might have accumulated mutations that do not change fluorescence. Indeed, Bykov et al. (Bykov et al., 2020) also found that a similar frequency of -10 and -35 boxes were destroyed in variants selected for lower GFP expression, which supports this argument. Second, we find no evidence that creating a -10 or -35 box lowers promoter activity in any of our 50 parent sequences. Third, we also find no evidence that destruction of a -10 or -35 box increases promoter activity without plausible alternative explanations, i.e. overlap of the destroyed box with a H-NS site, destruction of the promoter, or simultaneous creation of another motif as a result of the destruction. In sum, -10 and 35 boxes are not likely to repress promoter activity. “

METHODS:

Line 500: Could you provide more details on PMR1 (e.g. size, copy number, RBS strength) or a reference? I could not find this easily.

Thank you for pointing out this oversight. In response, we have added the following subsection to the methods (lines 740-748):

“Plasmid MR1 (pMR1)

The plasmid MR1 (pMR1) is a variant of the plasmid RV2 (pRV2) in which the kan resistance gene has been swapped with the cm resistance gene (Guazzaroni and Silva-Rocha, 2014). Plasmid pMR1 encodes the BBa_J34801 ribosomal binding site (RBS, AAAGAGGAGAAA) 6 bp upstream of the start codon for GFP(LVA). The plasmid also encodes a putative RBS (AAGGGAGG) (Cazemier et al., 1999) 5 bp upstream of the start codon for mCherry on the opposite strand.

The plasmid additionally contains the low-to-medium copy number origin of replication p15A (Westmann et al., 2018).

A map of the plasmid is available on the Github repository: https://github.com/tfuqua95/promoter_islands.”

Line 581: What was the sequencing instrument &/or depth?

We now report this information as follows (Methods, lines 918-922):

“Illumina sequencing

The amplicon pool was sequenced by Eurofins Genomics (Eurofins GmbH, Germany) using a NovaSeq 6000 (Illumina, USA) sequencer, with an S4 flow cell, and a PE150 (Paired-end 150 bp) run. In total, 282’843’000 reads and 84’852’900’000 bases were sequenced. Raw sequencing reads can be found here: https://www.ncbi.nlm.nih.gov/bioproject/1071572.”

SUPPLEMENT:

Supplementary Figure 2: Why does the GFP control produce a bimodal distribution?

The GFP+ culture was inoculated directly from a glycerol stock. The bimodal distribution probably results from a subset of the bacteria having lost the GFP-coding insert, because the left-most peak coincides with the negative control.

Reviewer #2 (Recommendations For The Authors):

This paper would benefit from a clear definition of what constitutes an active promoter as this is only mentioned as justification for the use of arbitrary values for fluorescence.

Good point. To clarify, we now include this new paragraph in the introduction (lines 112-119):

“In this study, we define a promoter as a DNA sequence that drives the expression of a (fluorescent) protein whose expression level, measured by its fluorescence, is greater than a defined threshold. We use a threshold of 1.5 arbitrary units (a.u.) of fluorescence. This definition does not distinguish between transcription and translation. We chose it because protein expression is usually more important than RNA expression whenever natural selection acts on gene expression, because it is the primary phenotype visible to natural selection (Jiang et al., 2023).”

There needs to be a clear distinction in the use of the word sequences as often interchange sequences when meaning the 25 parent sequences and then the 50 possible sequences directions the promoter can act. It is confusing going from one to the other.

We agree that this distinction is important. To make it clearer, we now introduce an additional term (lines 119-130). Our experiments start from 25 promoter island fragments (P1-P25), which we now call template sequences. Each template sequence comprises both DNA strands. The parent sequences are the top and bottom strands of each template sequence. Therefore, there are now 50 parent sequences (P1-GFP, P1-RFP, P2-GFP…, P25-RFP). By treating each strand as its own sequence, we no longer have to refer to the strand, avoiding the earlier confusion.

The description of the hotspots is often unclear and trying to determine if 3 out of 9 hotspots come from one parent sequence or multiple is not possible. A table denoting this information would be most helpful.

We agree, and now provide this information in Data S3.

Finally, the description of the proposed mechanism of promoter activation via mutation of motifs should not be in the results but in the discussion, as it has insufficient evidence and would require further experimental validation.

We remedied this problem by providing experimental validation of the proposed mechanisms. Specifically, we created the precise mutations that caused a loss or gain of a -10 or a -35 box, and measured the level of gene expression they drive with a plate reader. Because we chose to provide this experimental validation, we opted to leave the mechanisms of promoter activation in the results section.

The (Fuqua and Wagner 20023) paper is not in the references.

We have added Fuqua and Wagner, BiorXiv 2023 to the references.

I enjoyed the paper and wish the authors the best for their future work.

Thank you for taking the time to review our manuscript!

Reviewer #3 (Recommendations For The Authors):

The paper has major flaws. For example:

The data need to be analysed with correct promoter sequence element sequences (TTGACA for the -35 element).

The discrepancy lies in the frequency of A’s vs C’s at position #5 of the PWM. Our PWM was built with more A’s than C’s at this position, but also includes C’s in this position. However, we respectfully disagree that using a different -35 box PWM is going to change the outcomes of our study. First, positions 4-6 of the PWM barely have any information content (bits) compared to positions 1-3 (see Fig 1A). This assertion is not just based on our own PWM, but based on ample precedent in the literature. In PMID 14529615, TTG is present in 38% of all -35 boxes, but ACA only 8%. In PMID 29388765, with the -10 instance TATAAT, the -35 instance TTGCAA yields stronger promoters compared to the -35 instance TTGACA (See their Figure 3B). In PMID 29745856 (Figure 2), the most information content lies in positions 1-3, with the A and C at position 5 both nearly equally represented, as in our PWM. In PMID 33958766 (Figure 1) an experimentally-derived -35 box is even reduced to a “partial” -35 box which only includes positions 1 and 2, with consensus: TTnnnn. Additionally, the -35 box PWM that we used significantly and strongly correlates with an experimentally derived -35 box (see Supporting Information from Figure S4 of Belliveau et al., PNAS 2017. Pearson correlation coefficient = 0.89). We now provide DNA sequences for each of the figures to improve accessibility and reproducibility. A reader can now use any PWM or method they wish to interpret the data.

The data need to be analysed taking into account the role of other promoter elements and sequences for translation.

Point well taken. 

Thank you for bringing this oversight to our attention. We have performed two independent analyses to explore the role of TGn in promoter emergence in evolution. First, we computationally searched for -10 boxes with the bases TGn immediately upstream of them in the parent sequences, and found 18 of these “extended -10 boxes” in the parents (lines 143145):

“On average, each parent sequence contains ~5.32 -10 boxes and ~7.04 -35 boxes (Fig S1). 18 of these -10 boxes also include the TGn motif upstream of the hexamer.”

However, only 20% of these boxes were found in parents with promoter activity (lines 182-185):

“We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9-RFP, P10-RFP, P11GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25-RFP).” 

Second, we computationally searched through all of the daughter sequences to identify new -10 boxes with TGn immediately upstream. We found 114 -10 boxes with the bases TGn upstream. However, only 5 new -10 boxes (2 with TGn) were associated with increasing fluorescence (lines 338-345):

“Mutations indeed created many new -10 and -35 boxes in our daughter sequences. On average, 39.5 and 39.4 new 10 and -35 boxes emerged at unique positions within the daughter sequences of each mutagenized parent (Fig 3A,B), with 1’562 and 1’576 new locations for -10 boxes and -35 boxes, respectively. ~22% (684/3’138) of these new boxes are spaced 15-20 bp away from their cognate box, and ~7.3% (114/1’562) of the new -10 boxes have the TGn motif upstream of them. However, only a mere five of the new -10 boxes and four of the new -35 boxes are significantly associated with increasing fluorescence by more than +0.5 a.u. (Fig 3C,D).”

In addition, we now study the role of UP elements. This analysis showed that the UP element plays a negligible role in promoter emergence within our dataset.  It is discussed in a new subsection of the results (lines 591-608).

“The UP-element does not strongly influence promoter activity in our dataset.

The UP element is an additional AT-rich promoter motif that can lie stream of a -35 box in a promoter sequence (Estrem et al., 1998; Ross et al., 1993). We asked whether the creation of UP-elements also creates or modulates promoter activity in our dataset. To this end, we first identified a previously characterized position-weight matrix for the UP element (NNAAAWWTWTTTTNNWAAASYM, PWM threshold score = 19.2 bits) (Estrem et al., 1998) (Fig S13A). We then computationally searched for UP-element-specific hotspots within the parent sequences, i.e., locations in which mutations that gain or lose UP-elements lead to significant fluorescence increases (Mann-Whitney U-test, Fig S7 and methods. See Data S8 for the coordinates, fluorescence changes, and significance). The analysis did not identify any UP elements whose mutation significantly changes fluorescence. 

We then repeated the analysis with a less stringent PWM threshold of 4.8 bits (1/4th of the PWM threshold score). This time, we identified 74 “UP-like” elements that are created or destroyed at unique positions within the parents. 23 of these motifs significantly change fluorescence when created or destroyed. However, even with this liberal threshold, none of these UP-like elements increase fluorescence by more than 0.5 a.u. when gained, or decrease fluorescence by more than 0.5 a.u. when lost (Fig S13B). This finding ultimately suggests that the UP element plays a negligible role in promoter emergence within our dataset.”

Collectively, these additional analyses suggest that the presence of TGn plus a -10 box is insufficient to create promoter activity, and that the UP element does not play a significant role in promoter emergence or evolution.

The full sequences used need to be provided and mutations resulting in new promoters need to be shown.

To Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12, we have added the sequences which created or the destroyed the promoters, and their PWM scores.

The paper needs to be rewritten to take into account the relevant literature on i) promoter islands (i.e. sections of horizontally acquired AT-rich DNA) ii) generation and loss of promoters by mutation.

We have rewritten the introduction. The majority of these points are now addressed in the following two new paragraphs (lines 92-112):

“Recent work shows that mutations can help new promoters to emerge from promoter motifs or from sequences adjacent to such motifs (Bykov et al., 2020; Fuqua and Wagner, 2023; Yona et al., 2018). However, encoding -10 and -35 boxes is insufficient to drive complete transcription of a gene coding sequence. For instance, the E. coli genome contains clusters of -10 and -35 boxes that are bound by RNA polymerase and produce short oligonucleotide fragments, but rarely create complete transcripts. Such clusters are called promoter islands, and are strongly associated with horizontally-transferred DNA (Bykov et al., 2020; Panyukov and Ozoline, 2013; Purtov et al., 2014; Shavkunov et al., 2009). 

There are two proposed explanations for why promoter islands do not create full transcripts. First, the TF H-NS may repress promoter activity in promoter islands. This is because in a Δhns background, transcript levels from the promoter islands increases (Purtov et al., 2014). However, mutagenizing a specific promoter island (appY) until it transcribes a GFP reporter, reveals that in-vitro H-NS binding does not significantly change when GFP levels increase (Bykov et al., 2020). Thus, it is not clear whether H-NS actually represses the complete transcription of these sequences. The second proposed explanation is that excessive promoter motifs silence transcription. The aforementioned study found that promoter activity increases when mutations improve a -10 box to better match its consensus (TAAAAAT→TATACT), while simultaneously destroying surrounding -10 and -35 boxes (Bykov et al., 2020). However, we note that if these surrounding motifs never contributed to GFP fluorescence to begin with, then mutations could also simply have accumulated in them during random mutagenesis without affecting promoter activity.”

In closing, we would like to thank all three reviewers again for your time to engage with this manuscript.

Summary of specific changes that we have made to each section of the manuscript 

• Abstract

- We updated the abstract to include the finding that more than 1’500 new -10s and 35s are created in our dataset, but only ~0.3% of them actually create de-novo promoter activity.

- We no longer highlight the conclusion that the majority of promoters emerge and evolve from -10 and -35 boxes.

• Introduction

- We have added more background information about the UP-element and the TGn motif.

- We better describe the promoter islands and the results identified by Bykov et al., 2020.

• Results: Promoter island sequences are enriched with motifs for -10 and -35 boxes.

- We clarify how the -10 and -35 PWMs we use were derived.

- We refer to the 25 promoter island fragments as “Template sequences” (P1-P25). The “parent sequences” now correspond to the top and bottom strands of each template (N=50, P1-GFP, P1-RFP, P2-GFP, …, P25-RFP).

- We elaborate that ~7% of the -10 boxes in the template sequences have the TGn motif.

- In the previous version of the manuscript, if there were overlapping -10 boxes or overlapping -35 box, we counted these to be a single -10 box or a single -35 box, respectively. In the new version of the manuscript, we now treat each motif as an independent box. Because of this, the number of -10 and -35 boxes per parent have slightly increased.  

•Results: Non-promoters vary widely in their potential to become promoters.

- We make a clear distinction between promoters and non-promoters, and define the parent sequences.

- We note that only 20% of parents with an “extended -10 box” have promoter activity.

• Results: Promoter emergence correlates with minute differences in background promoter levels.

- We added an analysis where we compare Pnew to the parent fluorescence levels, even if they are below 1.5 a.u. We find that the distribution of Pnew matches a sigmoid function.

• Results: Promoter emergence does not correlate with simple sequence features

- We added an analysis comparing k-mer counts to Pnew.

- We updated the way we count -10 and -35 boxes, and recalculated the correlation with Pnew. The P and R2 values have changed, but Pnew still does not significantly correlate with -10 or -35 box counts.

• Results: Promoters emerge and evolve only from specific subsets of -10 and -35 boxes

- We have added an analysis where we computationally scramble the wild-type parent sequences while maintaining the coordinates of the mutual information hotspots. This reveals that the overlap with -10 and -35 motifs is not a coincidence of dense promoter motif encoding.

We found a computational error in our analysis and updated the percent overlap between -10 boxes and -35 boxes with mutual information hotspots. The results are similar. o 14% of -10 boxes overlap with hotspots with our new way of defining -10 and -35 boxes.

• Results: New -10 and -35 boxes readily emerge, but rarely lead to de-novo promoter activity

- We quantify how often a new -10 and -35 box is created at a unique position within our collection of promoter fragments, and how often this results in a -10 and -35 box being appropriately spaced, and how often this actually leads to de-novo promoter activity. o We quantify how often a TGn sequence lies upstream of a new -10 box.

• Results: Promoters can emerge when mutations create motifs but not by destroying them.

- For each example, we added the DNA sequences of the wild-type region of interest and the mutant region of interest that results in the gain of promoter activity, and their respective PWM scores. 

- We created constructs to validate each example by testing their fluorescence on a plate reader.

- We removed the P1-GFP example from the main figure, as it was a false-positive in the dataset. It is now in Fig S8.

- We removed the Shiko Emergence metaphor because it could be confused with a binding mechanism for RNA polymerase.

• Results – Gaining new motifs over existing motifs increases and decreases promoter activity.

- We removed the “Tandem motif” because it is more likely caused by H-NS binding.

- We renamed the mechanisms to be “hetero-gain” and “homo-gain” for simplicity, and clearly define how we classified each sequence into each category.

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the predicted point mutations.

• Results – Histone-like nucleoid-structuring protein (H-NS) represses P12-RFP and P22-GFP.

- This is a new analysis, which explores the role of the TF H-NS in repressing the parent sequences. 

- We identified putative H-NS motifs in P12-RFP and P22-GFP.

- We show experimentally that in a H-NS null background, a bidirectional promoter (P20) becomes unidirectional, even though P20 does not contain an obvious H-NS motif.

- In the original version of the manuscript, we describe a phenomenon where gaining a -35 box upstream of a promoter’s -35 box, or a -10 box upstream of a promoter’s -10 box significantly decreases expression. We called this phenomenon a “tandem motif.” However, in the newest version of the manuscript, we find that these fluorescence decreases are rescued in a H-NS null background, suggesting the finding was actually due to H-NS binding modulation and not -10 and -35 boxes.

• Results – The UP-element does not strongly influence promoter activity in our dataset.

We used a PWM for the UP element to see if gaining or losing UP motifs was significantly correlated with increasing or decreasing expression. Even with a liberal PWM threshold, the analysis did not find any UP elements.

• Discussion

- We rewrote the discussion to account for the new analyses and the results on H-NS, the UP-element, and the extended -10.

- We better explain how our results clash with the results from the Bykov paper.

- We fit our results into the context of David Grainger’s papers.

• Methods

- Added an explanation about pMR1.

- Added methods describing how we created the point mutation constructs.

- Added the methods for the plate reader.

- Added the methods for Illumina sequencing.

- Added the methods for the sigmoid curve-fitting.

• Figure 1

- Panel E compares how Pnew (the probability of a daughter sequence having a fluorescence score greater than 1.5 a.u.) associates with the fluorescence scores of each parent sequence.

- Panel F was originally in Figure S5. In the originally submitted version of the manuscript, if there were overlapping -10s or overlapping -35s, we counted these to be a single -10 or a single -35, respectively. In the new version of the manuscript, we now treat each motif as an independent box. Because of this, the r2 and p values have changed, but the conclusions have not (Pnew still does not significantly correlate with -10 or -35 box counts).

• Figure 2

- Panel C now includes a stacked barplot showing the percentage of -10 and -35 boxes that overlap with mutual information hotspots when the parent sequences are randomly scrambled computationally.

• Figure 3

- Panels A-C were added to explain how we define a new -10/-35 box, how many such new boxes each parent has. These panels also illustrate how we associate the presence or absence of a motif with significant changes in fluorescence scores of the daughter sequences.

- We moved the example of P1-GFP to Figure S8 because when we tested the specific mutation which leads to gaining the -10 box, fluorescence did not change.

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from reporter constructs harboring the point mutations predicted by our computational analyses.

- Cartoons of RNA polymerase have been removed.

• Figure 4

- The tandem-motif has been removed from the figure.

- Cartoons of RNA polymerase have been removed.

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure 5

- This is a new figure analyzing the role of H-NS in promoter evolution and emergence.

• Figure S4

- Panel B now shows the wild-type parent scores and their standard deviations from the sort-seq experiment.

• Figure S5

- Panels with -10 and -35 box counts moved to Figure 1.

- The panel comparing Pnew to hotspot counts was removed.

- Correlations between different k-mers and Pnew are added to panels C-H.

• Figure S8

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure S9

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure S10

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure S11

- Added DNA sequences and PWM scores.

• Figure S12

- A new figure with further insights about H-NS.

• Figure S13

- A new figure regarding the UP-element analysis.

• Figure S14

- Added Panel D to show how we created mutant reporter constructs for validation.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Liu et al. present CROWN-seq, a technique that simultaneously identifies transcription-start nucleotides and quantifies N6,2'-O-dimethyladenosine (m6Am) stoichiometry. This method is derived from ReCappable-seq and GLORI, a chemical deamination approach that differentiates A and N6-methylated A. Using ReCappable-seq and CROWN-seq, the authors found that genes frequently utilize multiple transcription start sites, and isoforms beginning with an Am are almost always N6-methylated. These findings are consistently observed across nine cell lines. Unlike prior reports that associated m6Am with mRNA stability and expression, the authors suggest here that m6Am may increase transcription when combined with specific promoter sequences and initiation mechanisms. Additionally, they report intriguing insights on m6Am in snRNA and snoRNA and its regulation by FTO. Overall, the manuscript presents a strong body of work that will significantly advance m6Am research.

Strengths:

The technology development part of the work is exceptionally strong, with thoughtful controls and well-supported conclusions.

We appreciate the reviewer for the very positive assessment of the study. We have addressed the concerns below.

Weaknesses:

Given the high stoichiometry of m6Am, further association with upstream and downstream sequences (or promoter sequences) does not appear to yield strong signals. As such, transcription initiation regulation by m6Am, suggested by the current work, warrants further investigation.

We thank the reviewer for the insightful comments. We have softened the language related to m6Am and transcription regulation. We totally agree with the reviewer that future investigation is required to determine the molecular mechanism behind m6Am and transcription regulation.

Reviewer #2 (Public review):

Summary:

In the manuscript "Decoding m6Am by simultaneous transcription-start mapping and methylation quantification" Liu and co-workers describe the development and application of CROWN-Seq, a new specialized library preparation and sequencing technique designed to detect the presence of cap-adjacent N6,2'-O-dimethyladenosine (m6Am) with single nucleotide resolution. Such a technique was a key need in the field since prior attempts to get accurate positional or quantitative measurements of m6Am positioning yielded starkly different results and failed to generate a consistent set of targets. As noted in the strengths section below the authors have developed a robust assay that moves the field forward.

Furthermore, their results show that most mRNAs whose transcription start nucleotide (TSN) is an 'A' are in fact m6Am (85%+ for most cell lines). They also show that snRNAs and snoRNAs have a substantially lower prevalence of m6Am TSNs.

Strengths:

Critically, the authors spent substantial time and effort to validate and benchmark the new technique with spike-in standards during development, cross-comparison with prior techniques, and validation of the technique's performance using a genetic PCIF1 knockout. Finally, they assayed nine different cell lines to cross-validate their results. The outcome of their work (a reliable and accurate method to catalog cap-adjacent m6Am) is a particularly notable achievement and is a needed advance for the field.

Weaknesses:

No major concerns were identified by this reviewer.

We thank the reviewer for the positive assessment of the method and dataset. We have addressed the concerns below.

Mid-level Concerns:

(1) In Lines 625 and 626, the authors state that “our data suggest that mRNAs initate (mis-spelled by authors) with either Gm, Cm, Um, or m6Am.” This reviewer took those words to mean that for A-initiated mRNAs, m6Am was the ‘default’ TSN. This contradicts their later premise that promoter sequences play a role in whether m6Am is deposited.

We thank the reviewer for the comment. We have changed this sentence into “Instead, our data suggest that mRNAs initiate with either Gm, Cm, Um, or Am, where Am are mostly m6Am modified.” The revised sentence separates the processes of transcription initiation and m6Am deposition, which will not confuse the reader.

(2) Further, the following paragraph (lines 633-641) uses fairly definitive language that is unsupported by their data. For example in lines 637 and 638 they state “We found that these differences are often due to the specific TSS motif.” Simply, using ‘due to’ implies a causative relationship between the promoter sequences and m6Am has been demonstrated. The authors do not show causation, rather they demonstrate a correlation between the promoter sequences and an m6Am TSN. Finally, despite claiming a causal relationship, the authors do not put forth any conceptual framework or possible mechanism to explain the link between the promoter sequences and transcripts initiating with an m6Am.

(3) The authors need to soften the language concerning these data and their interpretation to reflect the correlative nature of the data presented to link m6Am and transcription initiation.

For (2) and (3). We have softened the language in the revised manuscript. Specifically, for lines 633-641 in the original manuscript, we have changed “are often due to” into “are often related to” in the revised manuscript, which claims a correlation rather than a causation.

Reviewer #3 (Public review):

Summary:

m6Am is an abundant mRNA modification present on the TSN. Unlike the structurally similar and abundant internal mRNA modification m6A, m6Am’s function has been controversial. One way to resolve controversies surrounding mRNA modification functions has been to develop new ways to better profile said mRNA modification. Here, Liu et al. developed a new method (based on GLORI-seq for m6A-sequencing), for antibody-independent sequencing of m6Am (CROWN-seq). Using appropriate spike-in controls and knockout cell lines, Liu et al. clearly demonstrated CROWN-seq’s precision and quantitative accuracy for profiling transcriptome-wide m6Am. Subsequently, the authors used CROWN-seq to greatly expand the number of known m6Am sites in various cell lines and also determine m6Am stoichiometry to generally be high for most genes. CROWN-seq identified gene promoter motifs that correlate best with high stoichiometry m6Am sites, thereby identifying new determinants of m6Am stoichiometry. CROWN-seq also helped reveal that m6Am does not regulate mRNA stability or translation (as opposed to past reported functions). Rather, m6Am stoichiometry correlates well with transcription levels. Finally, Liu et al. reaffirmed that FTO mainly demethylates m6Am, not of mRNA but of snRNAs and snoRNAs.

Strengths:

This is a well-written manuscript that describes and validates a new m6Am-sequencing method: CROWN-seq as the first m6Am-sequencing method that can both quantify m6Am stoichiometry and profile m6Am at single-base resolution. These advantages facilitated Liu et al. to uncover new potential findings related to m6Am regulation and function. I am confident that CROWN-seq will likely be the gold standard for m6Am-sequencing henceforth.

Weaknesses:

Though the authors have uncovered a potentially new function for m6Am, they need to be clear that without identifying a mechanism, their data might only be demonstrating a correlation between the presence of m6Am and transcriptional regulation rather than causality.

We thank the reviewer for the very positive assessment of the CROWN-seq method. We have softened the language which is related to the correlation between m6Am and transcription regulation.

Author response:

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

Reviewer #1 (Public review):

Summary:

In this work, Qiu and colleagues examined the effects of preovulatory (i.e., proestrous or late follicular phase) levels of circulating estradiol on multiple calcium and potassium channel conductances in arcuate nucleus kisspeptin neurons. Although these cells are strongly linked to a role as the "GnRH pulse generator," the goal here was to examine the physiological properties of these cells in a hormonal milieu mimicking late proestrus, the time of the preovulatory GnRH-LH surge. Computational modeling is used to manipulate multiple conductances simultaneously and support a role for certain calcium channels in facilitating a switch in firing mode from tonic to bursting. CRISPR knockdown of the TRPC5 channel reduced overall excitability, but this was only examined in cells from ovariectomized mice without estradiol treatment.

Comments to address most recent author response:

The concern regarding the CRISPR experiments being confined to OVX mice is that the results can only suggest that CRISPR-mediated knockdown of TRPC5 can, at best, phenocopy the OVX+E condition. A reciprocal experiment in the opposite direction (for example, that returning TRPC5 to OVX levels in OVX+E mice prevents the changes in firing activity and pattern typical of the OVX+E2 condition) would strengthen the indication that E2-sensitive changes in TRPC5 expression and function are critically important to surge function. Acknowledging this as a limitation of the studies would help to better contextualize the value of the CRISPR experiments to an understanding of surge mechanisms when done only in OVX conditions.

We have noted in the manuscript that “It would be of interest in future experiments to do the reciprocal experiment to see if overexpressing Trpc5 channels in Kiss1ARH neurons from OVX + E2 females restores the RMP and  “rescues” the synchronization phenotype.”

The nature of the confusion regarding the consideration of OVX+E2 conditions in the computational model primarily arises from the methods description in the supplemental file: "The effect of E2 on ionic currents is modelled as a change in the maximum conductance parameter. For currents IM,IT, ICa and ITRPC5 this change is inferred from the qPCR data assuming that the conductance is directly proportional to the mRNA expression." If these were instead based on the whole-cell recordings as the authors now indicate in their response, then this description needs to be edited and clarified accordingly. Furthermore, the section states, "For ISK, IBK, Ileak, the OVX and OVX+E2 conductances are obtained from current-voltage relationships recorded from Kiss1ARH neurons in the absence/presence of iberiotoxin (BK blocker) and apamin (SK blocker). All other currents were assumed to be unaffected by E2." This section thus does not directly indicate that the recordings in the stated figures were used in the model, and moreover suggests that currents besides ISK, IBK, and Ileak were not different in OVX+E2 conditions.

The prior evidence stated for correlation of mRNA and channel conductance is not explicitly cited in the manuscript. It is well known that post-translational modifications, physiological modulation of individual channel biophysical properties, and many other factors can influence the end output of a membrane conductance. Therefore, the authors should, at minimum, provide a literature citation supporting the assumption used here.

We have re-written the paragraph on “Modelling the effects of E2” in the Supplemental Information (now Appendix 1)  to clarify the that the modeling was based on a combination of electrophysiological recordings and the qPCR data presented in this and previous publications. The statement that “all other currents were assumed to be unaffected by E2” was a misstatement and has been deleted. As per the reviewer’s request, we have listed seven publications that document the correlation between the mRNA expression and channel conductance for the various channels. We thank the reviewer for the suggestion.

Reviewer #2 (Public review):

Summary:

Kisspeptin neurons of the arcuate nucleus (ARC) are thought to be responsible for the pulsatile GnRH secretory pattern and to mediate feedback regulation of GnRH secretion by estradiol (E2). Evidence in the literature, including the work of the authors, indicates that ARC kisspeptin coordinate their activity through reciprocal synaptic interactions and the release of glutamate and of neuropeptide neurokinin B (NKB), which they co-express. The authors show here that E2 regulates the expression of genes encoding different voltage-dependent calcium channels, calcium-dependent potassium channels and canonical transient receptor potential (TRPC5) channels and of the corresponding ionic currents in ARC kisspeptin neurons. Using computer simulations of the electrical activity of ARC kisspeptin neurons, the authors also provide evidence of what these changes translate into in terms of these cells' firing patterns. The experiments reveal that E2 upregulates various voltage-gated calcium currents as well as 2 subtypes of calcium-dependent potassium currents, while decreasing TRPC5 expression (an ion channel downstream of NKB receptor activation), the slow excitatory synaptic potentials (slow EPSP) elicited in ARC kisspeptin neurons by NKB release and expression of the G protein-associated inward-rectifying potassium channel (GIRK). Based on these results, and on those of computer simulations, the authors propose that E2 promotes a functional transition of ARC kisspeptin neurons from neuropeptide-mediated sustained firing that supports coordinated activity for pulsatile GnRH secretion to a less intense burst-like firing pattern that could favor glutamate release from ARC kisspeptin. The authors suggest that the latter might be important for the generation of the preovulatory surge in females.

Strengths:

The authors combined multiple approaches in vitro and in silico to gain insights into the impact of E2 on the electrical activity of ARC kisspeptin neurons. These include patch-clamp electrophysiology combined with selective optogenetic stimulation of ARC kisspeptin neurons, reverse transcriptase quantitative PCR, pharmacology and CRISPR-Cas9-mediated knockdown of the Trpc5 gene. The addition of computer simulations for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.

The authors add interesting information on the complement of ionic currents in ARC kisspeptin neurons and on their regulation by E2 to what was already known in the literature. Pharmacological and electrophysiological experiments appear of the highest standards and robust statistical analyses are provided throughout. The impact of E2 replacement on calcium and potassium currents is compelling. Likewise, the results of Trpc5 gene knockdown do provide good evidence that the TRPC5 channel plays a key role in mediating the NKB-mediated slow EPSP. Surprisingly, this also revealed an unsuspected role for this channel in regulating the membrane potential and excitability of ARC kisspeptin neurons.

Weaknesses:

The manuscript also has weaknesses that obscure some of the conclusions drawn by the authors.

One is that the authors compare here two conditions, OVX versus OVX replaced with high E2, that may not reflect the physiological conditions under which the proposed transition between neuropeptide-dependent sustained firing and less intense burst firing might take place (i.e. the diestrous [low E2] and proestrous [high E2] stages of the estrous cycle). This is an important caveat to keep in mind when interpreting the authors' findings. Indeed, that E2 alters certain ionic currents when added back to OVX females, does not mean that the magnitude of all of these ionic currents will vary during the estrous cycle.

We do know that the slow EPSP, which is generated by TRPC5 channels, tracks beautifully with the steroid state of female mice.  Using our E2 treatment paradigm that generates a LH surge in OVX females (left panel in Author response image 1), there is no difference in the amplitude of the slow EPSP in proestrous versus OVX + E2 females (right panel in Author response image 1).    

Author response image 1.

In addition, although the computational modeling indicates a role of the various E2-modulated conductances in causing a transition in ARC kisspeptin neuron firing pattern, their role is not directly tested in physiological recordings, weakening the link between these changes and the shift in firing patterns.

In future experiments we will test directly the physiological contribution of the other E2-modulated conductances in causing the transition in the firing pattern of arcuate Kiss1 neurons using CRISPR/SaCas9 technology as we have documented for the TRPC5 channel (e.g., Figures 11 and 12).

Overall, the manuscript provides interesting information about the effects of E2 on specific ionic currents in ARC kisspeptin neurons and some insights into the functional impact of these changes. However, some of the conclusions of the work, with regard, in particular, to the role of these changes in ion channels and to their implications for the LH surge, are not fully supported by the findings.

---------

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this work, Qiu and colleagues examined the effects of preovulatory (i.e., proestrous or late follicular phase) levels of circulating estradiol on multiple calcium and potassium channel conductances in arcuate nucleus kisspeptin neurons. Although these cells are strongly linked to a role as the "GnRH pulse generator," the goal here was to examine the physiological properties of these cells in a hormonal milieu mimicking late proestrus, the time of the preovulatory GnRH-LH surge. Computational modeling is used to manipulate multiple conductances simultaneously and support a role for certain calcium channels in facilitating a switch in firing mode from tonic to bursting. CRISPR knockdown of the TRPC5 channel reduced overall excitability, but this was only examined in cells from ovariectomized mice without estradiol treatment. The manuscript has been substantially improved from the initial version by the addition of new experiments and clarification of important figures. Importantly, the overlap of data with previous reports from the same group has been corrected.

Strengths:

(1) Examination of multiple types of calcium and potassium currents, both through electrophysiology and molecular biology.

(2) Focus on arcuate kisspeptin neurons during the surge is relatively conceptually novel as the anteroventral periventricular nucleus (AVPV) kisspeptin neurons have received much more attention as the "surge generator" population.

(3) The modeling studies allow for direct examination of manipulation of single and multiple conductances, whereas the electrophysiology studies necessarily require examination of each current in isolation. Construction of an arcuate kisspeptin neuron model promises to be of value to the reproductive neuroendocrinology field.

Weaknesses:

A remaining weakness in this revised version of the manuscript is that the relevance of the CRISPR experiments is still rather tenuous given that the goal is to understand what happens in the estrogen-treatment condition, and these experiments were performed only in OVX mice. Similar concerns reflect that the computational model examining the effect of E2 infers multiple conductances based on qPCR data and an assumption that the conductances are directionally proportional to the level of gene expression, and then tunes these to the current recordings obtained from OVX mice, without a direct confirmation in OVX+E2 conditions that the model parameters accurately reflect the properties of these currents in the presence of estrogen.

We are still puzzled by Reviewer’s concerns about doing the CRISPRing of Trpc5 in the OVX+E2 females.  The Trpc5 channel expression is significantly reduced with the E2 treatment (Figure 10E) which we know translates into a minimal slow EPSP (Figure 2, Qiu eLife 2016) and is essentially equivalent to the slow EPSP amplitude in the Trpc5 mutagenesis in the ovariectomized females (Figure 12).  TRPC5 channel conductance is already at “rock bottom.”  The modeling informs us that such a low TRPC5 conductance will not support a long lasting slow EPSP and sustained firing (Figure 13A).

Also, we respectively point out that we have published a score of papers over the past 20 years showing that the channel conductance does correlate with the mRNA expression (e.g., Qiu et al., eLife 2018).  Secondly, the model does take into consideration the OVX + E2 conditions (Figure 13B,C) which is based on the extensive whole-cell recordings presented in Figures 4,5,6,7,8 and 9.

Reviewer #2 (Public Review):

Summary:

Kisspeptin neurons of the arcuate nucleus (ARC) are thought to be responsible for the pulsatile GnRH secretory pattern and to mediate feedback regulation of GnRH secretion by estradiol (E2). Evidence in the literature, including the work of the authors, indicates that ARC kisspeptin coordinate their activity through reciprocal synaptic interactions and the release of glutamate and of neuropeptide neurokinin B (NKB), which they co-express. The authors show here that E2 regulates the expression of genes encoding different voltage-dependent calcium channels, calcium-dependent potassium channels and canonical transient receptor potential (TRPC5) channels and of the corresponding ionic currents in ARC kisspeptin neurons. Using computer simulations of the electrical activity of ARC kisspeptin neurons, the authors also provide evidence of what these changes translate into in terms of these cells' firing patterns. The experiments reveal that E2 upregulates various voltage-gated calcium currents as well as 2 subtypes of calcium-dependent potassium currents while decreasing TRPC5 expression (an ion channel downstream of NKB receptor activation), the slow excitatory synaptic potentials (slow EPSP) elicited in ARC kisspeptin neurons by NKB release and expression of the G protein-associated inward-rectifying potassium channel (GIRK). Based on these results, and on those of computer simulations, the authors propose that E2 promotes a functional transition of ARC kisspeptin neurons from neuropeptide-mediated sustained firing that supports coordinated activity for pulsatile GnRH secretion to a less intense burst-like firing pattern that could favor glutamate release from ARC kisspeptin. The authors suggest that the latter might be important for the generation of the preovulatory surge in females.

Strengths:

The authors combined multiple approaches in vitro and in silico to gain insights into the impact of E2 on the electrical activity of ARC kisspeptin neurons. These include patch-clamp electrophysiology combined with selective optogenetic stimulation of ARC kisspeptin neurons, reverse transcriptase quantitative PCR, pharmacology and CRISPR-Cas9-mediated knockdown of the Trpc5 gene. The addition of computer simulations for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.

The authors add interesting information on the complement of ionic currents in ARC kisspeptin neurons and on their regulation by E2 to what was already known in the literature. Pharmacological and electrophysiological experiments appear of the highest standards and robust statistical analyses are provided throughout. The impact of E2 replacement on calcium and potassium currents is compelling. Likewise, the results of Trpc5 gene knockdown do provide good evidence that the TRPC5 channel plays a key role in mediating the NKB-mediated slow EPSP. Surprisingly, this also revealed an unsuspected role for this channel in regulating the membrane potential and excitability of ARC kisspeptin neurons.

Weaknesses:

The manuscript also has weaknesses that obscure some of the conclusions drawn by the authors.

One is that the authors compare here two conditions, OVX versus OVX replaced with high E2, that may not reflect the physiological conditions under which the proposed transition between neuropeptide-dependent sustained firing and less intense burst firing might take place (i.e. the diestrous [low E2] and proestrous [high E2] stages of the estrous cycle). This is an important caveat to keep in mind when interpreting the authors' findings. Indeed, that E2 alters certain ionic currents when added back to OVX females, does not mean that the magnitude of all of these ionic currents will vary during the estrous cycle.

Unfortunately, mice are a poor reproductive model since female mice do not have a clear follicular (estradiol-driven) phase distinctive from the luteal (progesterone-driven) phase.  Had we utilized a “proestrous” female, we could not with certainty distinguish between the effects of estradiol versus progesterone on the expression of the calcium and potassium channels that were the focus of this study.  Therefore, using our physiological model we can state with confidence that “estradiol elicits distinct firing patterns in arcuate nucleus kisspeptin neurons….”

Overall, the manuscript provides interesting information about the effects of E2 on specific ionic currents in ARC kisspeptin neurons and some insights into the functional impact of these changes. However, some of the conclusions of the work, with regard, in particular, to the role of these changes in ion channels and their implications for the LH surge, are not fully supported by the findings.

As we pointed out in the Discussion, the O’Byrne lab has clearly shown the relevance of Kiss1ARH neuronal burst firing and the release of glutamate to its effects on the LH surge:

“Rather, we postulate that glutamate neurotransmission is more important for excitation of Kiss1AVPV/PeN neurons and facilitating the GnRH (LH) surge with high circulating levels of E2 when peptide neurotransmitters are at a nadir and glutamate levels are high in female Kiss1ARH neurons. Indeed, low frequency (5 Hz) optogenetic stimulation of Kiss1ARH neurons, which only releases glutamate in E2-treated, ovariectomized females (Qiu J. et al., 2016), generates a surge-like increase in LH release during periods of optical stimulation (Lin et al., 2021; Voliotis et al., 2021).  In a subsequent study optical stimulation of Kiss1ARH neuron terminals in the AVPV at 20 Hz, a frequency commonly used for terminal stimulation in vivo, generated a similar surge of LH (Shen et al., 2022).  Additionally, intra-AVPV infusion of glutamate antagonists, AP5+CNQX, completely blocked the LH surge induced by Kiss1ARH terminal photostimulation in the AVPV (Shen et al., 2022).”

Recommendations for the authors:

Reviewer #2 (Recommendations for The Authors):

The reviewer noted the following in the revised manuscript:

- page 6, the authors may consider adding that presynaptic effects of blocking calcium channels on the slow EPSP cannot be fully ruled out. Indeed, the added experiments do indicate that some of the effects can be explained by impaired regulation of TRPC5 channels by calcium influx through calcium channels; however, the senktide-induced current is not fully blocked by the broad-spectrum calcium channel inhibitor cadmium, suggesting that the effect of blocking these channels on the slow EPSP may involve other mechanisms, such as presynaptic effects.

Optogenetic stimulation of all Kiss1ARH neurons induces the release of NKB at “physiological” concentrations, which in turn generates a slow EPSP in the recorded Kiss1ARH neuron. Blocking voltage-gated calcium channels can inhibit the NKB release from presynaptic  Kiss1ARH neurons, thereby reducing the amplitude of the slow EPSP. However, in whole-cell recordings of synaptically isolated Kiss1ARH neurons,  senktide directly induces a large inward current (Figure 3F), which is generated by the opening of TRPC5 channels (Qiu et al. J. Neurosci 2021). Voltage-gated calcium channels are coupled to the activation of TRPC5 channels (Blair, Kaczmarek and Clapham, J. Gen Physiol 2009), so by blocking voltage-gated calcium channels, cadmium effectively abrogates the facilitating effects of these channels on TRPC5 channel activation and significantly reduces but does not abolish the inward (excitatory) current (Figures 3F-H). We have clarified in the Results (page 6) that the Kiss1ARH neurons were synaptically isolated as depicted in Figures 3F,G.

- page 8, bottom, the mean value given for the apamin-sensitive current amplitude in E2 treated females does not match that plotted on the I/V graph in Figure 7F.

Thank you for pointing out this typographical error, which we have corrected.

Author response:

Reviewer 1 (Public Review)

(1) The proposed design is not sufficient to answer the research question. The rationale of the study proposed in the introduction is that auditory stimulation may explain the analgesic effects of RPMS. To answer this question, the authors should have used a factorial design using 4 groups (active RPMS + sound; active RPMS + no sound; sham RPMS + sound; sham RPMS + no sound). Using this design, it would have been possible to determine if the sound, the afferent stimulation, or both are necessary to produce analgesia. Rather, they tested two types of RPMS (iTBS, cTBS) without real rationale, one electrical stimulation and a placebo.

We will clarify that the study design employed was originally designed to determine whether iTBS or cTBS would be more effective to reduce pain. We included TENS as a positive control, and sham as a negative control. We were indeed surprised by the findings, and present them herein. Future RCTs should be performed to reproduce these findings.

(2) There are multiple ways that the current design could have introduced biases. The study was not randomized but pseudo-randomised. What does that mean? Was their allocation concealment? Was the assessor and data analyst blinded to group allocation? Did an intention to treat analyses were performed? Did the participants were adequately blinded (was it measured)?

This study was not designed as an RCT, but rather as experimental study. The study was pseudo-randomized to ensure that the groups had equal allocation and distribution of sexes.

The groups were blinded to the other stimulations (they were not informed of the various arms of the study, through different consent forms).

It was not possible to blind the experimenter as the iTBS and cTBS protocols are very different: iTBS has multiple bursts separated by brief intervals, whereas cTBS is continuous). The data were masked for analysis, and only unblinded at the final stage. We will update the manuscript to reflect these changes.

(3) The TENS parameters used were not optimal and are not those commonly used in clinical practice. This could have explained the lack of TENS effects. The lack of TENS effects has not been discussed and it is concerning. If TENS had been effective (as expected), the story about the auditory effects would not have been presented as the primary mechanisms underlying the current results.

We acknowledge that this is a limitation of the study. A future study should address this. However, we will not remove the arm for transparency.

(4) No primary outcome has been identified. It is important to mention that the interpretation of results is based on the presence of only one statistically significant result. Pain intensity and pain unpleasantness are not affected. This was not properly addressed in the Discussion. What does that mean that secondary hyperalgesia is affected but not pain?

We reiterate that this study was not designed as an RCT, but rather an experimental study with The primary outcomes measures that capture change in  were measures of pain sensitivity (pain intensity NRS, pain unpleasantness NRS, and secondary hyperalgesia). We will clarify this in the revised manuscript.

We will now include discussion of the effects being solely on secondary hyperalgesia, and not on pain intensity and unpleasantness.

(5a) The use of secondary hyperalgesia variable is concerning. How is it possible to measure secondary hyperalgesia if there is no lesioned tissue?

Secondary hyperalgesia refers to hyperalgesia assessed in an area adjacent to or remote of the site of stimulation. In general, it is not required to lesion a tissue to activate the nociceptive system or to induce pain. We have cited other studies that have employed secondary hyperalgesia as a pain outcome measure without inducing a lesion.

Hyperalgesia reflects increased pain on suprathreshold stimulation. Then, one measures the subjective response to a painful (i.e. suprathreshold) stimulation, then applies a conditioning stimulation (e.g. heat), and measures the subjective response to the same original stimulus. If the response after conditioning is higher than the baseline measure, hyperalgesia has been induced. Secondary hyperalgesia just refers to hyperalgesia assessed in an area adjacent to or remote of the site of stimulation. In general, it is not required to lesion a tissue to activate the nociceptive system or to induce pain.

(5b) If heat creates secondary hyperalgesia without lesion, what does that mean physiologically?

Secondary hyperalgesia is normally interpreted as a perceptual correlate of central sensitization.

(5c) Is it a valid and reliable "pain" variable?

Yes and yes. A noxious heat stimulus can reliably elicit secondary hyperalgesia (see section 3.2 from Quesada et al. 2021). We also cite several studies that have used secondary hyperalgesia as an outcome measure of central sensitization in pain.

(6) The follow-up study has been designed to cover the RPMS sound using pink noise. However, the pink noise was also present during the PHP measurement. How can we determine whether the absence of change is due to the pink noise during the RPMS or the presence of pink noise during PHP? I don't think this is possible to discriminate.

We will add a third study that performs the control analysis with the sound of the rPMS masked, but no pink noise otherwise. The study will be performed in two groups: one with pink noise, and one without pink noise.

Appraisal

(7) Despite all these potential issues, authors interpret their data with high confidence and with several overstatements in the Title, Abstract, and Discussion. The results do not support their conclusions. The fact that auditory stimulation may produce an analgesic effect is a hypothesis, but the current study cannot ascertain it.

We believe that the chief concern with the interpretation lies with concerns with the second study. The proposed third experiment will address these concerns.

Reviewer 2 (Public Review):

(1) My biggest concern in this paper is that the stimulation protocols are not applied after pain was induced in the subjects, but before. This is not bad in itself, but as the paper presents the stimulations as potential "treatments" it generates a severe mismatch between the objective, context (introduction), and impact (discussion) presented for the experiments, and how they are actually designed. This adds to the fact that healthy volunteers are used here to generate a study with low translational capability, that aims to be translational and provide an indication for clinics (maybe this is why the reduction in pain intensity caused by PMS when applied in patients, reported in references [29, 35 and 39], is not observed here).

We will reframe these as prophylaxis, rather than treatment. This study was an experimental study originally designed to determine which stimulation parameters (cTBS or iTBS) would be better suited to modulate pain. We performed the study in healthy individuals undergoing acute pain, akin to a person undergoing painful procedure, which could lead to central sensitization and pain persistence (e.g., post-surgical pain). However, before testing this in individuals undergoing actual procedures, it is essential to determine efficacy in people before translation.

Khan et al [29] is a case study with neuropathic pain, whereas our study uses a nociceptive pain model. Lim et al [35] employed 10 sessions of rPMS stimulation in patients with acute low back pain. Similar to our study, the change in VAS driven by rPMS was no different than the sham stimulation. We notice that there is no reference 39, and will correct this.

(2) TENS treatment duration is simply too short (90s) to be considered a therapeutic TENS intervention. I get that this duration was chosen to match the one of PMS, but TENS is never applied like this in the clinics, in which the duration varies from 10 minutes to an hour (or more). This specific study comparing different durations recommends 40 minutes for knee osteoarthritis pain relief (PMID: 12691335). Under these conditions, this stimulation is more similar to a sham TENS than to a real TENS treatment: I would suggest interpreting it as such. As the paper is right now, it could give the impression that PMS could produce clinical effects not observed in TENS, but while the PMS application resembles a clinical one, the TENS application does not (due to its extremely short duration). As an example, giving paracetamol at a dose 10 times below its effective dose is a placebo, not a paracetamol treatment.

We acknowledge that this is a limitation, and will address this in the Discussion of the revised manuscript.

(3) This study measured pain, not central sensitization. Specifically, the effects refer to the area of secondary hyperalgesia. The IASP definition for central sensitization is "Increased responsiveness of nociceptive neurons in the central nervous system to their normal or subthreshold afferent input." (PMID: 32694387). No neuronal results are reported in this article. Therefore, central sensitization is not measured here, and we do not know if it is reduced by sound. This frontally clashes with the title of the article and with many interpretations of the results. For a deep review on this topic, I recommend PMID: 39278607 and the short article PMID: 30416715.

It is widely accepted that central sensitization is the neurophysiological basis of secondary hyperalgesia (see PMID: 11313449; PMID: 10581220).

The reviewer is conflating secondary hyperalgesia due to central sensitization and chronic pain. Whether chronic pain is driven or maintained by central sensitization is not the goal of our study. However, there is ample evidence that nociceptive drive can induce plasticity in the CNS, which alters pain sensitivity, and that these changes facilitate pain.

(4a) There is no mention of blinding/masking/concealing in this manuscript. Was the therapist blind to whether they applied one protocol, another, or a placebo? Were the evaluators blind, as this can heavily influence their measurements? And the volunteers? Was allocation concealed? Was this blinding measured afterwards? Blinding is, together with randomization, the most important methodological feature for those interventional studies. For example, not introducing blinding and concealing directly makes a study lose 4 out of 10 points in the PEDro scale, failing to fulfill criteria 3, 5, 6, and 7 (https://pedro.org.au/english/resources/pedro-scale/).

This study was not designed as an RCT, but rather as experimental study. The study was pseudo-randomized to ensure that the groups had equal allocation and distribution of sexes.

The groups were blinded to the other stimulations (they were not informed of the various arms of the study, through different consent forms). However, blinding was not measured afterwards (again, this was not meant to be an RCT).

It was not possible to blind the experimenter as the iTBS and cTBS protocols are very different: iTBS has multiple bursts separated by brief intervals, whereas cTBS is continuous). The data were masked for analysis, and only unblinded at the final stage. We will update the manuscript to reflect these changes.

(4b) Continuing with methodological considerations, the dropout percentage is high (18% for the first and 25% for the second study), both above the 15% cutoff for criterion 8 of the PEDro, losing another point.

In the study, only 2 withdrew after feeling the heat, 2 were lost to follow up, and 2 had incomplete data. That totals 6/123 in Study 1. In study 2, none of the participants that met inclusion/exclusion criteria, and who were ‘allocated’ to the study were included (0% dropout/data loss).

We are unsure how to address this point, as we had clear inclusion/exclusion criteria, and these could only be measured after consenting. As this is an experimental study performed on healthy individuals in a university setting, we are not able to collect any study related data prior to consent.

We openly reported individuals who did not meet the criteria, and thus were excluded. These criteria are a combination of what is required to collect good quality data, and what we are ethically permitted to do. We understand that in an interventional trial where >15% drop out due to intolerance, or adverse events would indeed be concerning.

(5) Data reporting and statistical treatment can be improved, as only differences are reported and regression to the mean is not accounted for in this study. Moreover, baseline levels for the dependent variables (control session) are not accessible for evaluation and they are not compared statistically, making it impossible to know if the groups were similar at baseline. This will imply failing criterion 3 of the PEDro, for a total of 2/10 points.

This only concerns study 1, as study 2 is a within subject study design. Study 1 provides the raw data in Figure 4. We will provide the raw data for each of the primary outcome measures in a supplemental table in the revision.

Author response:

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

Reviewer #1 (Public review):

Summary:

Park et al. conducted various analyses attempting to elucidate the biological significance of SARS-CoV-2 mutations. However, the study lacks a clear objective. The specific goals of the analyses in each subsection are unclear, as is how the results from these subsections are interconnected. Compiling results from unrelated analyses into a single paper can be confusing for readers. Clarifying the objective and narrowing down the topics would make the paper's purpose clearer.

The logic of the study is also unclear. For instance, the authors developed an evaluation score, APESS, for analyzing viral sequences. Although they state that the APESS score correlates with viral infectivity, there is no explanation in the results section about why this is the case.

The structure of the paper should be reconsidered.

Thank you for your feedback. We have heeded the input that the study lacks a clear objective and made sure that the overall goal of the study is reflected in the Abstract, Results, and Discussion.

We have made sure that the specific goals in each subsection are clearer in the Results section that better explain the goals of those sections and elaborated on how the components of our study connect to each other. We have addressed these in more detail in the ‘Recommendations for the authors’ section.

Thank you for the feedback on APESS, our evaluation model. APESS was created based on virus properties that we discovered of SARS-CoV-2 in our study. When applying our evaluation model, high APESS scores indicated high infectivity. APESS is calculated from a comprehensive evaluation of SARS-CoV-2 at the nucleotide, amino acid, and protein structure levels.

The detailed explanations and exact calculations of APESS are detailed in the Materials and Methods section in line 571 but we should have been more detailed in the Results section as well. We have made sure to properly indicate this in the Results section in line 284.

And overall, we have made edits to the manuscript that accurately explain our research by amending terms, restructuring arguments, and providing more clarity for the interconnectivity of the research.

Reviewer #2 (Public review):

Summary:

The authors have developed a machine learning tool AIVE to predict the infectivity of SARS-CoV-2 variants and also a scoring metric to measure infectivity. A large number of virus sequences were used with a very detailed analysis that incorporates hydrophobic, hydrophilic, acid, and alkaline characteristics. The protein structures were also considered to measure infectivity and search for core mutations. The study especially focused on the S protein of SARS-CoV-2. The contents of this study would be of interest to many researchers related to this area and the web service would be helpful to easily analyze such data without in-depth bioinformatics expertise.

Strengths:

- Analysis of large-scale data.

- Experimental validation on a partial set of searched mutations.

- A user-friendly web-based analysis platform that is made public.

Weaknesses:

- Complexity of the research.

Thank you for your kind feedback. Our study explored a wide range of topics including biochemical properties, machine learning, and viral infectivity.

In presenting our research, we recognize that our comprehensive analysis may have slightly obscured the specific aims and overall objective of the study. We investigated properties in the viral sequences of SARS-CoV-2 and examined big data, clinical data, and expression data to elucidate their effect on viral infectivity. We then used evaluation modeling and in silico and in vitro validation.

We have clarified the aims of our research and improved upon the flow of the manuscript by adding sentences that outline the goals of our research in the appropriate sub sections of the Results and Discussion sections.

Reviewer #1 (Recommendations for the authors):

The abstract should clearly state the backgrounds, objectives, strategies, and findings of this study in an orderly manner.

Thank you for your feedback. We have restructured the Abstract to better reflect the goals and methods of our study. We start the Abstract by introducing the background of the study ‘An unprecedented amount of SARS-CoV-2 data has been accumulated compared with previous infectious diseases, enabling insights into its evolutionary process and more thorough analyses.’ in line 48. Then we more clearly stated the overall objectives of our research in line 50 as ‘This study investigates SARS-CoV-2 features as it evolves to evaluate its infectivity.’ Then, we clearly defined our specific discoveries in the virus, the purpose of our evaluation model, and how we validated our findings.

In the Introduction, the message of each paragraph is unclear. Please clearly state the objectives of the study and what was done to achieve these objectives.

Thank you for the feedback. We have updated the Introduction section to more clearly state the objectives of the study.

To increase clarity, we have moved ‘Furthermore, hydrophobic properties in the amino acid sequence affect protein folding. Coronavirus hydrophobicity has significant effects on amino acid properties and protein folding.’ to line 127.

In line 130, we rephrased the first sentence of the paragraph to ‘For these prior approaches to virus analysis and prediction, expertise with the relevant fields is required for a full understanding.’ to better establish the link between the background information and aims of the study. Then in line 134, we added ‘elucidate properties about the virus’ to clarify the aims of the study.

In line 141, we have improved the clarity of the sentence to better present the scope and objectives of the study.

The relationship between the sections in the Results is unclear. Clarify why each section is necessary and how they are interconnected.

We investigated properties in the viral sequences of SARS-CoV-2 that highlighted amino acid substitutions or changes in polarity (Figure 1). In VOCs, we noted trends or absences of amino acid substitutions at specific positions (Figure 2). We examined epidemiological and clinical data to determine the infectivity, severity, and symptomaticity of lineages. Looking at expression data and binding affinity further illuminated the effect of amino acid substitutions (Figure 3). We created APESS, an evaluation modeling, that is comprehensively calculated from the nucleotide, amino acid, and protein structure levels of the virus. Evaluation of lineages revealed that higher APESS scores were associated with higher infectivity (Figure 4). We used in silico and in vitro validation to reinforce our findings then used machine learning to make predictions on future developments (Figure 5). We created candidate sequences for evaluation and utilized machine learning in predictions (Figure 6).

We have added explanations to each section in Results that elucidate the objective of each section and how they connect with each other in the wider study.

In line 157, we have added ‘We examined the amino acid sequences of SARS-CoV-2 to make discoveries about biochemical properties.’ to clearly outline the objective of the subsection.

In line 207, we have improved the phrasing of the sentence.

In line 278, we stressed that ‘We developed APESS, an evaluation model to analyze viral sequences based on the nucleotide, amino acid, and protein structure properties.’ to properly define the purpose and background of APESS.

Please define abbreviations when they first appear.

We have added the full terms for the stated abbreviations in the relevant sections of the manuscript.

In line 107, we have added the proper abbreviation for Our World in Data (OWID).

In lines 143, 175, and 489 we have added the full term for Variants of Concern (VOCs).

In line 160, we have added the full term for Receptor Binding Motif (RBM).

Reviewer #2 (Recommendations for the authors):

(1) pg 9, line 51, full name of RBM should be declared.

We have added the full name of Receptor Binding Motif (RBM) to the appropriate section in the Abstract.

(2) How are the Variants of Concern (VOCs) defined?

Thank you for the comment and we apologize for the confusion. Variants of Concern as defined by the World Health Organization are specified in the Materials and Methods section. We have also added the full name for Variants of Concern (VOCs) when they are first mentioned in the Introduction and Results sections.

(3) pg 17, line 297. The purpose of using AI/ML to predict amino acid substitutions at specific locations is not clear. The VOCs and related mutation loci were already searched, so the AA substitution prediction step seems a little repetitive. Is it to create customized sequences? Also, if prediction (or probability) was made, some performance evaluation would be helpful.

Thank you for this feedback. The purpose of utilizing machine learning to make predictions about amino acid substitutions is to assess the possibility of amino acid substitutions occurring at specific locations. These potential amino acid substitutions were evaluated by APESS to have high scores, linking them to high infectivity. As the feedback suggests, amino acid substitutions in VOCs are researched but our prediction sought to ascertain the likelihood of amino acid substitutions that our evaluation model associated with infectivity. In the Results section in line 330, we assessed the probability of amino acid substitutions N460K and Q493R that the study found to be significant. The datasets that we utilized for these predictions are detailed in the Materials and Methods section in line 677.

The models we trained with machine learning predicted the probability of mutations based on samples in each group and their performance was evaluated by comparing the presence of mutations in the clades they diverged from. We have added the following sentences to line 330: “We used Accuracy, Precision, Recall, and F1 score to evaluate performance. All models showed high performance scores above 0.95 in Precision, Recall, and F1 score. For accuracy, XGBoost, scored above 0.89, exhibiting relatively high performance while LightGBM scored above 0.78.”

(4) pg 17, line 289. The objective of creating candidate lineages is not clear and would be helpful for the readers if its purpose is elaborated on. Since there are enough SARS-CoV-2 sequences, wouldn't it be more realistic and accurate to use those real sequences instead of creating them? Furthermore, the candidate lineages should be defined but they were missing in this section. This part made it a little difficult to follow the overall paper's logic.

The manuscript should have been clearer on what ‘candidate lineages’ signified, we apologize for the confusion. In line 314, we included the following sentences for clarity: ‘We introduced amino acid substitutions at specific locations in the SARS-CoV-2 backbone for the wildtype and VOCs. The amino acid substitutions were lysine (K), arginine (R), asparagine (N), serine (S), tyrosine (Y), and glycine (G). We then evaluated the infectivity of these candidate lineages with our evaluation model APESS.’

The purpose of creating candidate lineages in our study was to assess the effect of specific amino acid substitutions on the virus’ infectivity. The amino acid substitutions we evaluated were lysine (K), arginine (R), asparagine (N), serine (S), tyrosine (Y), and glycine (G). We determined that examining the introduction of specific amino acid substitutions to SARS-CoV-2 sequences would highlight the significance they had on infectivity. We have revised the paragraph in line 314 of the Results section to convey what we were doing.

(5) This study covers very detailed contents regarding lineages, mutations, and their effect on infectivity. It would be more readable if subsections could be added per group of investigation, especially in the results and discussion section.

In the Results section, we have emphasized the objective of each subsection and how they connect with one another for the overall goals of our study.

In line 157, we have added ‘We examined the amino acid sequences of SARS-CoV-2 to make discoveries about biochemical properties.’ to clearly outline the objective of the subsection.

In line 207, we have improved the phrasing of the sentence.

In line 278, we stressed that ‘We developed APESS, an evaluation model to analyze viral sequences based on the nucleotide, amino acid, and protein structure properties.’ to properly define the purpose and background of APESS.

We have made edits to the Discussion section to more clearly indicate subsections.

In line 389, we have added ‘In our investigation of various viruses’ to clearly indicate the background on other viruses.

In line 409, we added the sentence ‘We made discoveries on specific amino acid substitutions at positions.’ to indicate the subsection talking about N437R, N460K, and D467 mutations.

In line 471, we added the sentence ‘We created AIVE to feature our findings and analyses on an online platform.’ And modified the following sentence to better explain AIVE.

(6) pg 26, line 557. The criteria for the SCPSi scores were set to 0.9 and 0.1 by the proportion of the Omicron and Delta variants. How do other criteria affect the performance of the method?

Thank you for the question and check point. We used 0.9/0.1 for our initial criteria in our SCPS calculation. To determine how that affected performance, we have used 0.8/0.2 and 0.7/0.3 as the criteria.

After calculating APESS with different SCPS weights (0.9/0.1, 0.8/0/2, 0.7/0.3), we used a Gaussian Mixture Model (GMM) to compare how the groups were divided based on APESS. All three groups with different SCPS weights were determined to accurately reflect data patterns when they had four components.

When comparing parameter values, the group that used the original weights of 0.9 and 0.1 for SCPS showed the lowest values for variance and standard error across all four components. This indicates that each component was stable and clearly distinguishable from one another.

The group where the weights were adjusted to 0.7 and 0.3 for SCPS showed significantly higher variance and a large error for the G2 component. The distribution of each component was more widespread, signifying that the stability and reliability was lower.

The group where the weights were adjusted to 0.8 and 0.2 for SCPS was positioned between the two previous groups for finer data classification and reliability. However, the group notably lacked reliability when it came to the SE values for the G4 component.

Thus, the original model with 0.9 and 0.1 weight is the most reliable.

When the Gaussian Density for each group was plotted, the group with 0.9/0.1 SCPS weights showed the highest peak near 2 (G1), with a value of approximately 2. For the group with SCPS 0.8/0.2 weights, the highest peak appeared near 4.2 (G3), showing a high value around 14. For the group with SCPS 0.7/0.3 weights, the highest peak appeared near 3.7 (G3) showing a value around 5. The group with 0.9/0.1 SCPS weights exhibited a more uniform Gaussian distribution compared to the other two.

Author response image 1.

Superposition of Gaussian Densities for SCPS weight 0.9/0.1

Author response table 1.

Statistical values of the Superposition of Gaussian Densities for SCPS weight 0.9/0.1

Author response image 2.

Superposition of Gaussian Densities for SCPS weight 0.8/0.2

Author response table 2.

Statistical values of the Superposition of Gaussian Densities for SCPS weight 0.8/0.2

Author response image 3.

Superposition of Gaussian Densities for SCPS weight 0.7/0.3

Author response table 3.

Statistical values of the Superposition of Gaussian Densities for SCPS weight 0.7/0.3

(7) Overall, the approach is very detailed and realistic. Just curious if this approach would be also applicable to other viruses such as influenza.

We appreciate the insightful comments from the reviewer, and this is a direction we hope to take our research in the future. Our study focused on SARS-CoV-2 and the properties we discovered from the virus’ spike protein interacting with the host’s ACE2 receptor. In our investigation of other coronaviruses such as MERS-CoV, SARS-CoV-1 possesses a different structure and properties than these viruses as we have illustrated in Supplementary Figure 24. We had provided explanations about our investigation of other viruses in the Discussion section. In line 389, we have added ‘In our investigation of various viruses’ to better signpost this section.

Author response:

In this initial response to the public review, we outline our plan to address the major concerns raised. Below, we provide a general categorization of the suggestions and our corresponding responses

Weakness #1: Statistical Concerns - using the number of seizures (rather than the number of animals) may identify small effects that could be insignificant. Effect size should be taken into consideration.

Reviewer 1:

“While the data generally supports the authors' conclusions, a weakness of this manuscript lies in their analytical approach where EEG feature-space comparisons used the number of spontaneous or evoked seizures as their replicates as opposed to the number of IHK mice; these large data sets tend to identify relatively small effects of uncertain biological significance as being highly statistically significant.”

Reviewer 2:

“In several sections of the paper, the authors argue that two different groups are similar on the basis that no statistical difference was found between the two groups (i.e., p > 0.05); however, the failure to find a statistically significant difference, particularly with relatively small sample sizes, is not rigorous evidence that the two groups are actually similar - they are just "not significantly different.”

Reviewer 3:

“(3) The utility of increasing the number of seizures for enhancing statistical power is limited unless the sample size under evaluation is the number of seizures. However, the standard practice is for the sample size to be the number of mice.”

Reviewer 3:

“(1) Evaluation of seizure similarity using the SVM modeling and clustering is not sufficiently explained to show if there are meaningful differences between induced and spontaneous seizures. SVM modeling did not include analysis to assess the overfitting of each classifier since mice were modeled individually for classification.”

We understand the reviewers’ concerns. In this work, we used linear mixed effect model to address two levels of variability –between animals and within animals. The interactive linear mixed effect model shows that most (~90%) of the variability in our data comes from within animals (Residual), the random effect that the model accounts for, rather than between animals. Since variability between animals are low, the model identifies common changes in seizure propagation across animals, while accounting for the variability in seizures within each animal. Therefore, the results we find are of changes that happen across animals, not of individual seizures. We will make text edits to enhance understanding of the linear mixed effect model.

To address the point raised about similarity, we will explain how the SVM classifier was trained. The purpose of the SVM is not to identify meaningful differences between induced and spontaneous seizures. Rather, it is to classify EEG sections as “seizures” or non-seizures, demonstrating the gross similarity between induced and spontaneous seizures despite minor differences. We will make text clarifications for the SVM model.

Weakness #2: Clinical and biological significance is unclear.

Reviewer 1:

“Furthermore, the clinical relevance of similarly small differences in EEG feature space measurements between seizure-naïve and epileptic mice is also uncertain.”

Reviewer 2:

“While the paper may be relevant for the ETSP and contract research organizations (CROs), the paper was not written to attract the interest of biological scientists, even those in this specific area of epilepsy research. It may be of low interest to other neuroscientists… The key issue the authors aim to address is the 30-40% of patients with DRE, but the real problem with DRE patients is not that these people have seizures with no effect of the ASDs; rather, although ASD may reduce seizure burden, these patients continue to have some remaining seizures even after high doses of ASDs, which often leads to adverse effects from the particular ASDs… It remains unclear that the optogenetically induced seizures in this model are better than similarly induced seizures in a naïve animal, and there is no evidence that the model will be useful for finding new ASDs to treat DRE.”

Reviewer 3:

“(6) Human epilepsy is extensively heterogeneous in both etiology and individual phenotype, and it may be hard to generalize the approach.”

Reviewer 2:

“The authors state that this approach should be used to test for and discover new ASDs for DRE, and also used for various open/closed loop protocols with deep-brain stimulation; however, the paper does not actually discuss rigorously or critically the background literature on other published studies in these areas or how this approach will improve future research for a broader audience than the ETSP and CROs. Thus, it is not clear whether the utility will apply more widely and how extensive a readership will be attracted to this work.”

We appreciate the reviewer’s concerns. We will revise the manuscript to better emphasize the potential significance of our approach. The on-demand seizure model can be applied to address biologically and clinically relevant questions beyond its utility in drug screening. For example, crossing the Thy1-ChR2 mouse line with genetic epilepsy models, such as Scn1a mutants, could reveal how optogenetic stimulation differentially induces seizures in mutant versus non-mutant mice, providing insights into seizure generation and propagation in Dravet Syndrome. Due to the cellular specificity of optogenetics, we also envision this approach being used to study circuit-specific mechanisms of seizure generation and propagation. Regarding drug-resistant epilepsy (DRE) and anti-seizure drug (ASD) screening, we agree with the reviewer that probing new classes of ASDs for DRE represents the critical goal. However, we believe a full exploration of additional ASD classes and/or modeling DRE lies outside the scope of this manuscript.

Weakness #3: Definition of Seizure is unclear

Reviewer 2:

“Although the figures provide excellent examples of individual electrographic seizures and compare induced seizures in epileptic and naïve animals, it is unclear which criteria were used to identify an actual seizure induced by the optogenetic stimulus, versus a hippocampal paroxysmal discharge (HPD), an "afterdischarge", an "electrophysiological epileptiform event" (EEE, Ref #36, D'Ambrosio et al., 2010 Epilepsy Currents), or a so-called "spike-wave-discharge" (SWD). Were HPDs or these other non-seizure events ever induced using stimulation in animals with IH-KA? A critical issue is that these other electrical events are not actual seizures, and it is unclear whether they were included in the column showing data on "electrographic afterdischarges" in Figure 5 for the studies on ASDs”

Reviewer 3:

“(2) The difference between seizures and epileptiform discharges or trains of spikes (which are not seizures) is not made clear.”

Reviewer 2:

“The differences between the optogenetically evoked seizures in IH-KA vs naïve mice are interpreted to be due to the "epileptogenesis" that had occurred, but the lesion from the KA-induced injury would be expected to cause differences in the electrically and behaviorally recorded seizures - even if epileptogenesis had not occurred. This is not adequately addressed.”

Thank you for pointing out the unclear definition of the seizures analyzed. We agree and will revise the text to clarify this issue. In this manuscript, we focused on tonic-clonic seizures. We analyzed animal behavior during evoked events, and a high percentage of induced electrographic events were accompanied by behavioral seizures with a Racine scale of three or above. Regarding epileptogenesis, our model is based on the IHK model, in which spontaneous tonic-clonic seizures occur a few to several days after KA injection. These mice are, by definition, epileptogenic. We will further clarify this methodology in the text.

Weakness #4: Similarity/Difference with Kindling Not Clear

Reviewer 2:

“The authors did not test whether an apparent "kindling" effect, apparently seen in naïve controls, also occurred in animals micro-injected with kainic acid (KA). This effect could cause model instability that might result in variability in response to ASDs. It is not clear whether the number of optogenetically induced seizures in epileptic animals would affect the response to drugs. It is also unclear how much of an improvement the animal model in the present work is over other similar models of TLE, where electrically triggered seizures could simply be applied to one of them.”

Reviewer 3:

“(5) It is unlikely that long-term adaptation to CA1-stimulated seizure induction is absent in these mice. A duration of evaluation longer than 16 days is warranted in light of the downward slope at days 13-16 for induced seizures in Figure 4C.”

We appreciate the reviewer’s comments regarding the “kindling effect” as well as its similarity to the kindling model. We will carefully assess the data and address this in the revised manuscript. In electrical kindling, the activated cellular population is non-specific, including both excitatory and inhibitory neurons. In our model, we specifically activate predominantly excitatory neurons (Thy1-positive neurons), which we observed to participate in convulsant-induced seizures (as demonstrated in Thy1-GCaMP experiments). We consider this specificity an improvement over the kindling model, making our approach more biologically relevant.

Weakness #5: Time needed to generate model is significant. Unclear if animals were pre-selected

Reviewer 1:

“Finally, the multiple surgeries and long timetable to generate these mice may limit the value compared to existing models in drug-testing paradigms.

Reviewer 2:

“The authors offer little mention of other research using animal models of TLE to screen ASDs, of which there are many published studies - many of them with other strengths and/or weaknesses. For example, although Grabenstatter and Dudek (2019, Epilepsia) used a version of the systemic KA model to obtain dose-response data on the effects of carbamazepine on spontaneous seizures, that work required use of KA-treated rats selected to have very high rates of spontaneous seizures, which requires careful and tedious selection of animals. The ETSP has published studies with an intra-amygdala kainic acid (IA-KA) model (West et al., 2022, Exp Neurol), where the authors claim that they can use spontaneous seizures to identify ASDs for DRE; however, their lack of a drug effect of carbamazepine may have been a false negative secondary to low seizure rates. The approach described in this paper may help with confounds caused by low or variable seizure rates. These types of issues should be discussed, along with others.”

We appreciate the reviewer’s insights. In an existing model investigating spontaneous tonic-clonic seizures (such as the intra-amygdala kainate injection model), the time investment is back-loaded, requiring two to three weeks per condition while counting spontaneous seizures, which may occur only once a day. In contrast, our model requires a front-loaded time investment. Once the animals are set up, we can test multiple drugs within a few weeks, providing significant time savings. Additionally, we did not pre-screen animals in our study. Existing models often pre-select mice with high rates of spontaneous seizures, whereas in our model, seizures can be induced even in animals with few spontaneous seizures. We believe that bypassing the need for pre-screening is a key advantage of our induced seizure model.

Reviewer 3:

“(7) No mention or assessment of mouse sex as a biological variable.”

Thank you for pointing this out. Both female and male animals were included in this study: Epileptic cohort: 7 males, 3 females; Naïve cohort: 3 males, 4 females

Author response:

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

Reviewer #1 (Public Review):

Summary:

Wilson's Disease (WD) is an inherited rare pathological condition due to a mutation in ATP7B that alters mitochondrial structure and dysfunction. Additionally, WD results in dysregulated copper metabolism in patients. These metabolic abnormalities affect the functions of the liver and can result in cholecystitis. Understanding the immune component and its contribution to WD and cholecystitis has been challenging. In this work, the authors have performed single-cell RNA sequencing of mesenchymal tissue from three WD patients and three liver hemangioma patients.

Strengths:

The authors describe the transcriptomic alterations in myeloid and lymphoid compartments.

Weaknesses:

In brief, this manuscript lacks a clear focus, and the writing needs vast improvement. Figures lack details (or are misrepresented), the results section only catalogs observations, and the discussion needs to focus on their findings' mechanistic and functional relevance. The major weakness of this manuscript is that the authors do not provide a mechanistic link between the absence of ATP7B and NK cells' impaired/altered functions. While the work is of high clinical relevance, there are various areas that could be improved.

In this study, we reported for the first time that ATP7B mutation and the resulting metabolic abnormalities in hepatocytes cause functional alteration of immune cells in WD patients. We dissected the transcriptional profiles of liver mesenchymal cells and delineated the functional differences of main immune cells in WD patients through scRNA-seq. The NK cell exhaustion and its clinical significance were further demonstrated.

The mechanism study is of our concern. Given that the ATP7B mutation is hepatocyte-specific, its effect on immune cells is most probably through intercellular communication rather than through the direct action of ATP7B protein. How ATP7B mutation disturbs the metabolic homeostasis in hepatocyte, how metabolic pathways regulate the release of signal substances, and how signal substances act on the NK cells need to be explained. These contents, together with this manuscript, are beyond the scope of a single article, so we put the novelty in this manuscript.

We sincerely appreciate the comments. We have improved the manuscript based on your valuable suggestions. The mechanism study is our subsequent research topic. We are actively promoting it and have found that ATP7B mutation rewires a certain metabolism pathway in hepatocyte, and that a critical metabolite functions as the mediator causing NK cell exhaustion.

Reviewer #2 (Public Review):

Summary:

Wilson's disease is a rare genetic disorder caused by mutations in the ATP7B gene. Previous studies have documented that ATP7B mutations can disrupt copper metabolism, affecting brain and liver function. In this paper, the authors performed a retrospective clinical study and found that Wilson's disease has a high incidence of cholecystitis. Single-cell RNA-seq analysis revealed changes in the immune microenvironment, including the activation of immune responses and the exhaustion of natural killer cells.

Strengths:

A key finding of this study is that the predominant ATP7B gene mutation in the Chinese population is the 2333G>T (p. R778L) mutation. The authors reported associations between Wilson's disease and cholecystitis, as well as the exhaustion of natural killer cells.

Weaknesses:

The underlying mechanisms linking ATP7B mutations to cholecystitis and natural killer cell exhaustion remain unclear. Specifically, it is not yet determined whether copper metabolism alterations directly cause cholecystitis and natural killer cell exhaustion, or if these effects are secondary to liver dysfunction.

In this study, we reported for the first time that ATP7B mutation and the resulting metabolic abnormalities in hepatocytes cause functional alteration of immune cells in WD patients. We dissected the transcriptional profiles of liver mesenchymal cells and delineated the functional differences of main immune cells in WD patients through scRNA-seq, focusing on the NK cell exhaustion and its clinical significance.

The mechanism study is of our concern. Given that the ATP7B mutation is hepatocyte-specific, its effect on immune cells is most probably through intercellular communication, so we prioritize the studying of this aspect. How ATP7B mutation disturbs the metabolic homeostasis in hepatocyte, how metabolic pathways regulate the release of signal substances, and how signal substances act on the NK cells need to be explained. These contents, together with this manuscript, are beyond the scope of a single article, so we put the novelty in this manuscript.

We sincerely appreciate the comments. The mechanism study is the topic of our follow-up study. We are actively promoting the research and we have found that ATP7B mutation rewires a certain metabolism pathway in hepatocyte, and that a critical metabolite functions as the mediator causing NK cell exhaustion.

Reviewer #1 (Recommendations For The Authors):

Major:

(1) Abstract. A major portion of this manuscript focuses on non-NK cells. Data that describes NK cell exhaustion is only minimal. Therefore, the authors should modify the abstract.

Thank you for your valuable suggestion. We have supplemented the description of functional changes in other immune cells, and have modified the abstract (line 31-35).

(2) Introduction. There are three paragraphs. The first paragraph discusses cholecystitis. However, there are too many repetitions, and the information is unclear. In the second part, the authors discuss NK cells and their exhaustion. The authors do not establish a clear rationale or logic linking NK cells to WD or cholecystitis. In the last paragraph, the authors describe their findings. Their correlation between NK cell exhaustion and the poor healing process of cholecystitis has no direct experimental proof.

Thank you for your comments. We have deleted the repetitions and rephrased some sentences (line 72-74). Briefly, in the first paragraph, we proposed the significant prognostic value of immune cell dysfunction for cholecystitis. In the second paragraph, we introduced NK cell exhaustion and its potential to predict prognosis of certain diseases. In the third paragraph, we introduced that the liver is a central organ involved in metabolism and immunity, holding a large number of NK cells. Liver pathologies commonly impact the development and outcome of inflammation-associated diseases such as cholecystitis. WD was selected as a research model. In the last paragraph, we introduced our findings from clinical study, scRNA-seq, clinical samples, and bioinformatics analysis, and concluded at the end.

(3) Results. Overall, the results section lacks clarity and a clear focus. Figure legends need to be significantly detailed. The authors make too many broad statements without any support. The authors also make too many overstatements.

Thank you for your valuable suggestion. We have improved the inaccurate statements and made detailed refinement of figure legends. All the changes are marked in the manuscript, and related responses are described below.

Figure 1: No information is provided about the functional impairment of ATP7B protein due to the mutation found in the cohort of Chinese patients. What does 'immune abnormalities' (line 127) mean? What is the relevance of showing liver fibrosis and copper accumulation in the eye in Figure 1c and d, respectively? Total cholesterol concentrations are still within the range in the plasma of WD patients, but the authors call it higher. ECAR has not changed in WD patients, but the authors claim it has (line 117).

(1) All these gene mutations in WD disable the protein function and cause the same outcome. (2) We have deleted the inappropriate statement. (3) In clinical observation, we found that WD not only causes copper accumulation in hepatocytes, but also leads to a variety of diseases, including liver fibrosis, Kayser-Fleischer Ring, and lower risk of hyperglycemia. We showed these together with the data of cholecystitis incidence. We think these might suggest the significance of intercellular communication between hepatocytes and other cells in microenvironment. (4) We have deleted the inappropriate statement (line 108-110, 112-113).

Figure 2: Did the authors use the liver mesenchymal tissue or mesenchymal cells? Figure 2 states that they used mesenchymal cells, different from liver mesenchymal tissue. Numbers within Figure 2b UMAP are not visible. Were the initial T and NK cells annotated as indicated in Figure S2 (CD3D, CD#E, CD3G)? If so, that does not include NK cells.

(1) The liver mesenchymal cells were used for scRNA-seq. (2) It is possible that the image resolution was reduced due to the compression of files by the submission system during merging process. We confirm that the image resolution of all figures meets publishing requirements, and that all characters on the figures are visible. You can download figure files to view details. (3) It was our negligence that the incomplete cell markers were shown in Figure S2. We have updated the markers (CD3D, CD3E, NKG7), references (Ref #53, #55, and #56), and related figures (Figure 2e, and Figure S2c).

Figure 3: The authors should change 'Case' to 'WD patients' both in the text and figures. DEGs in Figure 3C indicate a transcriptomic alteration in the B cell compartment, which the authors do not delineate. Also, the rationale and explanation for the CellChat analyses are minimal. Concluding that a change occurred within the TME with minimal data and explanations is unfair.

Thank you for your comments. (1) We apologize for the confusion caused by the use of nomenclatures and abbreviations in the text and figures. In all scRNA-seq data analysis, presentation, and description, we used specific terms (CASE and CON) to refer to the group of WD patients and controls, as well as their cell population. We have now unified the use of nomenclature in full text and defined them when first appeared (line 126-127), avoiding using lowercase form to prevent confusion. (2) We have now compared the expression of key genes of B cell between the two group in the next section “The dysfunction of main immune cells in WD patients” (line 230-235, Figure 4e, Figure S4e). (3) We have described the results of cellular communication in more detail (line 188-194). (4) We have modified the conclusion and all the related statement in full text (line 29-31, 82-84, 149, 194-195).

Figure 4: This section deals with multiple cell types with minimal explanations. This section discusses various cell types, but it lacks focus. In particular, the T cell section should be separated and elaborated more in detail.

(1) In this section, we intended to show the comparison in function of main immune cells that account for a considerable proportion, instead of just showing differently expressed genes that provide minimal information. The evaluation of functional signature, based on the integration of multiple gene expression, allows a direct understanding of the final outcome owing to transcriptional changes. (2) Given that the main functions of T cells did not change significantly and there were more significant changes in innate immunity, the T cell section is relatively short and unsuitable as a separated part.

Figure 5: What are the distinct subsets of NK cells authors have found in the WD patients and controls? How do these subsets differ between the two groups in numbers and their transcriptomes? The presentation and labeling of Figure 5 and Supplementary Figure 5 need to be vastly improved. The pseudotime presentation in Figure 5b should be presented separately for the patients and the controls. Are the changes in gene expression presented in Figure 5a due to the change in the subset compositions? Figure 5c immuno-staining is not at all visible. A clear explanation should be given for the differences between Figure 5c and Figure 5e, where NKG2A expressions are shown. A better explanation for Figure 5d is required. Did the authors use all the antibodies with the same fluorochrome? If so, what color is that? Can the authors include the individual samples in the bar diagram in Figure 5e? Again, the data in Figure 5 is insufficient to conclude that NK cells are exhausted in WD patients. While the role of changes in the expression of T-BET and EOMES can be related to dysfunction and cellular exhaustion of NK cells, the statement made by the authors needs to be toned down as they do not test with independent experiments.

(1) The subsets of NK cell were clustered by gene expression profile and labeled by the characteristically expressed gene, using certain algorithm in the routine procedure. They cannot be distinguished in clinical samples by one or several genes or other sorting methods. Thus, we were not able to analyze these subsets in clinical samples. (2) We have supplemented the comparison of numbers and transcriptomes of three NK subtypes between the two groups (line 268-273). (3) We have checked the figures and confirmed that all characters on the figures are visible. (4) We have separately presented the plot in Figure S5d. (5) We compared the expression level of genes presented in Figure 5a between the two groups in three NK subtypes and supplemented this part (line 264-268). The results were very consistent across the three subtypes, suggesting that the results in total NK population were contributed by all three subtypes and not affected by a single composition. (6) KLRC1 is also known as NKG2A. We are sorry for not making a clear explanation, and now we use KLRC1 only in all text to avoid confusion. We have made a more clear and detailed description for Figure 5c, 5d, and 5e (now labeled as Figure 5b, 5c, and 5d), and have included the fluorochrome in Figure 5d (now labeled as Figure 5c) and the individual value in Figure 5e (now labeled as Figure 5d) (line 293-299). (7) In this section, we found the upregulated expression of inhibitory receptors, downregulated expression of effector molecules, and the impaired NK cell-mediated cytotoxicity in NK cell of WD patients from scRNA-seq. Then we validated the findings in clinical liver section samples and clinical blood samples by mIHC and flow cytometry, respectively. According to the recent articles, exhausted NK cells are characterized by decreased production of effector cytokines (e.g., IFNγ), as well as by impaired cytolytic activity, and downregulate expression of certain activating receptors and upregulate expression of inhibitory receptors (e.g., 10.3389/fimmu.2017.00760, 10.1038/s41590-018-0132-0, 10.1038/s41467-019-09212-y, 10.1080/2162402X.2016.1264562). Therefore, we concluded NK cell exhaustion in WD patients. (8) In the part about transcription factors, we kept the description of objective data and deleted the statement of the contribution of transcription factors to NK exhaustion.

Figure 6: Data presented in Figure 6 and the conclusion made in this manuscript are predictive. There is no direct testing of ATP7B in NK cells to show the functions of this gene. Extension of this to patient survival is purely speculative. As long as authors state these facts clearly in their text, it can be acceptable. However, they do not extend their conclusions to similar liver diseases.

ATP7B mutation is hepatocyte-specific, and it does not occur in any immune cells. The function of ATP7B in NK cell was not studied. We found the NK exhaustion and poor prognosis of cholecystitis in WD patients. Given that there were researches demonstrating that NK exhaustion is correlated with poor liver cancer prognosis, we hypothesized that NK exhaustion contributes to the poor prognosis of cholecystitis. Bioinformatics studies confirmed our hypothesis and supported the extension of this result to other inflammatory diseases. We had no experimental data, but this result was reliable in bioinformatics method.

(4) Discussion: While the authors analyzed multiple cell types, the discussion is primarily focused on NK cells. There is no clear link between copper utilization, NK cell function, and exhaustion that the authors articulate.

Thank you for your comments. The focus of our study is NK cell exhaustion, which is experimentally proven, so we discussed this aspect. We prioritize the effect of intercellular communication and metabolic alteration on the NK cell exhaustion in our follow-up study. Excess copper is released into the circulation in some circumstances in WD patients, but generally they receive long-term de-coppering therapy to maintain intracellular copper at a non-lethal level. Thus, we do not tend to consider copper as a critical factor in this study. In original manuscript, we mentioned the cuproptosis and its potential as a novel target. It is likely to lead to ambiguity and misunderstanding, so we deleted this part to put our point of view clearly.

(5) Supplementary Figures: The presentation and labeling of these figures need to be changed.

Thank you for your suggestions. We have modified the figures and confirmed that all characters on the figures are visible.

Reviewer #2 (Recommendations For The Authors):

It is better to test whether ATP7B mutation can directly affect immune functions.

Thank you for your suggestions. Given that the ATP7B mutation is hepatocyte-specific, its effect on immune cells is most probably through intercellular communication. Thus, we prioritize the effect of intercellular communication on the NK cell exhaustion and we are actively promoting the research.

Author response:

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

Public reviews:

Reviewer 1

We would like to express our gratitude to Reviewer 1 for providing a thorough summary of our work and highlighting its strengths. With regards to the weaknesses, we are committed to improve the manuscript by performing the necessary changes. First, we will specify the exact p-value in all cases.

Regarding the discussion section, we acknowledge the feedback regarding its potential confusion. In line with the reviewer's suggestion, we will reduce the literature review and highlight our findings.

Finally, for the preprint we did not include cofounders such as HIV infection and ethnicity as our study population did not exhibit viral infections and comprised only Hispanic individuals. We will make a more thorough description of the population of study and address these characteristics explicitly in both the methods section and the initial part of the results.

Reviewer 2

We appreciate and thank reviewer 2 for the commentaries. Although it is true that several papers have described the role of microbiome in COVID-19 severity, we firmly believe that our current work stands out. There is not much information related to this association in Mediterranean countries, especially in the south of Spain. In addition, most of the studies only describe microbiota composition in stool or nasopharyngeal samples separately, without investigating any potential relationships between them as we do.

(1) We agree with the reviewer idea of a limited sample size. We faced the challenge of collecting the samples during the peak of COVID-19 pandemia. Thus, doctors and nurses were overwhelmed and not always available for carrying out patient recruitment following the inclusion criteria. Despite these constraints, we ensured that all included samples met our specified inclusion criteria and were from subjects with confirmed symptomatology.

In addition, our main goal was to identify whether severity of the disease could be assessed through microbiota composition. Therefore we did not include a healthy group. Despite not having a large N, our results should be reproducible as they are supported by statistical analysis.

(2) We thank reviewer commentary, and since our original sentence may have lacked clarity, we intend to modify it to ensure it conveys the intended meaning more effectively.

Nonetheless, we remain confident in the significance of our findings. Not only have we found correlation between microbiota and COVID severity, but we have also described how specific bacteria from each condition is associated with key biochemical parameters of clinical COVID infection.

(3) We appreciate the feedback provided by the reviewer. In this case, we have performed 16S analysis due to its cost-effectiveness compared to metagenomic approaches. Furthermore, 16S analysis has undergone refinements that ensure comprehensive coverage and depth, along with standardized analysis protocols. Unlike 16S, metagenomic approaches lack software tools such as QIIME that facilitate standardization of analysis and, thus, reduce reproducibility of results.

(4) We sincerely appreciate this insightful suggestion. simply listing associations between both microbiomes and COVID-19 severity could not be enough, we intend to discuss how microbiota composition may be linked to the mechanisms underlying COVID-19 pathogenesis in our discussion.

(5) We are grateful for the constructive criticism and intend to rewrite our abstract to enhance clarity. Additionally, we will thoroughly review all figures and their descriptions to ensure accuracy and comprehensibility.

Reviewer 3

We acknowledge the annotations made by reviewer 3 and are committed to addressing all identified weaknesses to enhance the quality of our work. Our idea is to modify the methods section and figures to make them easier to understand.

Specifically, in the case of Figure 1, we recognize an error in the description of the Bray-Curtis test. We appreciate the commentary and we will make the necessary changes. Moreover, there is another observation related to Figure 1 description. We are going to modify it in order to gain accuracy.

For figure 2 we are planning to add a supplementary table showing the abundance of detected genus. Nevermind, we will also update the manuscript text to provide clarification on how we obtained this result.

Regarding the clarification about "1% abundance," we want to emphasize that we are referring to relative abundance, where 1 represents 100%. To avoid confusion, we will explicitly state this in both the methods section and figure descriptions. Besides, it is true that the statistical test employed for the analysis is not mentioned in the figure description and we recognize that the image may be difficult to interpret. Therefore, we will modify the text and a supplementary table displaying the abundance and p values is going to be added.

Furthermore, we agree with the reviewer's suggestion to investigate whether the bacteria identified as potential biomarkers for each condition are specific to their respective severity index or if there is a threshold. Thus, we will reanalyze the data and include a supplementary table with the abundance of each biomarker for each condition. We will also place greater emphasis on these results in our discussion.

Finally, in response to the reviewer's suggestion, we are going to go through the nasopharyngeal-fecal axis part in the discussion. It is well described that COVID-19 induces a dysbiosis in both microbiomes. Consequently, we understand that the ratio we have described could be an interesting tool for assessing COVID severity development as it considers alterations in both environments. However, we acknowledge that there may be room for improvement in clarifying the significance of this intriguing finding and its implications.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This manuscript from Schwintek and coworkers describes a system in which gas flow across a small channel (10^-4-10^-3 m scale) enables the accumulation of reactants and convective flow. The authors go on to show that this can be used to perform PCR as a model of prebiotic replication.

Strengths:

The manuscript nicely extends the authors' prior work in thermophoresis and convection to gas flows. The demonstration of nucleic acid replication is an exciting one, and an enzyme-catalyzed proof-of-concept is a great first step towards a novel geochemical scenario for prebiotic replication reactions and other prebiotic chemistry.

The manuscript nicely combines theory and experiment, which generally agree well with one another, and it convincingly shows that accumulation can be achieved with gas flows and that it can also be utilized in the same system for what one hopes is a precursor to a model prebiotic reaction. This continues efforts from Braun and Mast over the last 10-15 years extending a phenomenon that was appreciated by physicists and perhaps underappreciated in prebiotic chemistry to increasingly chemically relevant systems and, here, a pilot experiment with a simple biochemical system as a prebiotic model.

I think this is exciting work and will be of broad interest to the prebiotic chemistry community.

Weaknesses:

The manuscript states: "The micro scale gas-water evaporation interface consisted of a 1.5 mm wide and 250 µm thick channel that carried an upward pure water flow of 4 nl/s ≈ 10 µm/s perpendicular to an air flow of about 250 ml/min ≈ 10 m/s." This was a bit confusing on first read because Figure 2 appears to show a larger channel - based on the scale bar, it appears to be about 2 mm across on the short axis and 5 mm across on the long axis. From reading the methods, one understands the thickness is associated with the Teflon, but the 1.5 mm dimension is still a bit confusing (and what is the dimension in the long axis?) It is a little hard to tell which portion (perhaps all?) of the image is the channel. This is because discontinuities are present on the left and right sides of the experimental panels (consistent with the image showing material beyond the channel), but not the simulated panels. Based on the authors' description of the apparatus (sapphire/CNC machined Teflon/sapphire) it sounds like the geometry is well-known to them. Clarifying what is going on here (and perhaps supplying the source images for the machined Teflon) would be helpful.

We understand. We will update the figures to better show dimensions of the experimental chamber. We will also add a more complete Figure in the supplementary information. Part of the complexity of the chamber however stems from the fact that the same chamber design has also been used to create defined temperature gradients which are not necessary and thus the chamber is much more complex than necessary.

We added the scheme of the whole PTFE Chip to Figure 2 in the top left corner, indicating the ROI shown in the fluorescence micrographs. Additionally, the channel walls are now clearly indicated by white dotted lines. The dimensions of the setup are now shown clearer, by showing the total width of the channel as well as its height until the gas flux channel, as well as its depth. Changed caption of the figure accordingly and it now reads: “[…] The PTFE chip cutout in the top left corner shows the ROI used for the micrographs. The color scale is equal for both simulation and experiment and Channel dimensions are 4 x 1.5 x 0.25 mm as indicated. Dotted lines visualize the location of the channel walls. […]“

The data shown in Figure 2d nicely shows nonrandom residuals (for experimental values vs. simulated) that are most pronounced at t~12 m and t~40-60m. It seems like this is (1) because some symmetry-breaking occurs that isn't accounted for by the model, and perhaps (2) because of the fact that these data are n=1. I think discussing what's going on with (1) would greatly improve the paper, and performing additional replicates to address (2) would be very informative and enhance the paper. Perhaps the negative and positive residuals would change sign in some, but not all, additional replicates?

To address this, we will show two more replicates of the experiment and include them in Figure 2.

We are seeing two effects when we compare fluorescence measurements of the experiments.

Firstly, degassing of water causes the formation of air-bubbles, which are then transported upwards to the interface, disrupting fluorescence measurements. This, however, mostly occurs in experiments with elevated temperatures for PCR reactions, such as displayed in Figure 4.

Secondly, due to the high surface tension of water, the interface is quite flexible. As the inflow and evaporation work to balance each other, the shape of the interface adjusts, leading to alterations in the circular flow fields below.

Thus the conditions, while overall being in steady state, show some fluctuations. The strong dependence on interface shape is also seen in the simulation. However, modeling a dynamic interface shape is not so easy to accomplish, so we had to stick to one geometry setting. Again here, the added movies of two more experiments should clarify this issue.

We performed three more replicates of the experiment and included the averaged data points together with their respective standard deviation as error bars in Figure 2d. Additionally, the videos of each individual repeat are now added to the supplementary files for the reader to better understand where the strong fluctuations around half an hour come from. The Figure caption was adjusted to “ […] The maximum relative concentration of DNA increased within an hour to ~30 X the initial concentration, with the trend following the simulation. Error bars are the standard deviation from four independent measurements. […].

The main text was also changed to better explain how the fluctuations impact the measurements: […] Water continuously evaporated at the interface, but nucleic acids remained in the aqueous phase accumulating near the interface. They could only escape downward either by diffusion or by the vortex induced by the gas flowing across the interface, pushing the molecules back deeper into the bulk (See the flow lines in Fig2(b) taken from the simulation).  As the gas flow continuously removed excess vapor, the evaporation rate remained constant. Thus, except for fluctuations, a stable interface shape should be expected. However, due to the high surface tension of water, the interface is very flexible. As the inflow and evaporation work to balance each other, the shape of the interface adjusts, likely in response to small fluctuations in gas pressure and spatial variations in water surface tension. This is leading to alterations in the circular flow fields below (Supplementary Movie 2).

As these fluctuations are difficult to simulate, we decided to stick with one interface shape, matching evaporation and inflow speeds. The evaporation rate at the interface was therefore set to be proportional to the vapor concentration gradient and varied spatially along the interface between 5 and 10.5 µm/s (See Suppl. Fig. VI.1(d)). Using the known diffusion coefficient of 95 µm²/s for the 63mer[9]}, the simulation closely matched the experimental results. In both cases, DNA accumulated in regions with circular flow patterns driven by the gas flux (Fig.2(b), right panel).

5 minutes after starting the experiment, the maximum DNA accumulation was 3-fold, while after one hour of evaporation, around 30-fold accumulation was observed. Due to molecules residing in very shallow volumes when directly at the interface, the fluorescence signal can vary drastically compared to measurements deeper in the bulk. This can be seen in the fluctuations between independent measurements (See Supplementary Movies 2b,2b,2c), especially around 0.5~h shown in Figure 2(d). The simulated maximum accumulation followed the experimental results and starts saturating after about one hour (Fig.2(d)). […]”

The authors will most likely be familiar with the work of Victor Ugaz and colleagues, in which they demonstrated Rayleigh-Bénard-driven PCR in convection cells (10.1126/science.298.5594.793, 10.1002/anie.200700306). Not including some discussion of this work is an unfortunate oversight, and addressing it would significantly improve the manuscript and provide some valuable context to readers. Something of particular interest would be their observation that wide circular cells gave chaotic temperature profiles relative to narrow ones and that these improved PCR amplification (10.1002/anie.201004217). I think contextualizing the results shown here in light of this paper would be helpful.

Thanks for pointing this out and reminding us. We apologize. We agree that the chaotic trajectories within Rayleigh-Bénard convection cells lead to temperature oscillations similar to the salt variations in our gas-flux system. Although the convection-driven PCR in Rayleigh-Bénard is not isothermal like our system, it provides a useful point of comparison and context for understanding environments that can support full replication cycles. We will add a section comparing approaches and giving some comparison into the history of convective PCR and how these relate to the new isothermal implementation.

We added a main text paragraph after the last paragraph in section “Strand Separation Dynamics”: “[…]Rayleigh-Bénard convection cells generate similar patterns to those seen in Fig. 3(c) The oscillations in salt concentration resemble the temperature fluctuations observed in convection-based PCR reactions from earlier studies [32,33], which showed that chaotic temperature variations, compared to periodic ones, enhanced the efficiency of the PCR reaction.[…]

Again, it appears n=1 is shown for Figure 4a-c - the source of the title claim of the paper - and showing some replicates and perhaps discussing them in the context of prior work would enhance the manuscript.

We appreciate the reviewer for bringing this to our attention. We will now include the two additional repeats for the data shown in Figure 4c, while the repeats of the PAGE measurements are already displayed in Supplementary Fig. IX.2. Initially, we chose not to show the repeats in Figure 4c due to the dynamic and variable nature of the system. These variations are primarily caused by differences at the water-air interface, attributed to the high surface tension of water. Additionally, the stochastic formation of air bubbles in the inflow—despite our best efforts to avoid them—led to fluctuations in the fluorescence measurements across experiments. These bubbles cause a significant drop in fluorescence in a region of interest (ROI) until the area is refilled with the sample.

Unlike our RNA-focused experiments, PCR requires high temperatures and degassing a PCR master mix effectively is challenging in this context. While we believe our chamber design is sufficiently gas-tight to prevent air from diffusing in, the high surface-to-volume ratio in microfluidics makes degassing highly effective, particularly at elevated temperatures. We anticipate that switching to RNA experiments at lower temperatures will mitigate this issue, which is also relevant in a prebiotic context.

The reviewer’s comments are valid and prompt us to fully display these aspects of the system. We will now include these repeats in Figure 4c to give readers a deeper understanding of the experiment's dynamics. Additionally, we will provide videos of all three repeats, allowing readers to better grasp the nature of the fluctuations in SYBR Green fluorescence depicted in Figure 4c.

The data from the triplicates are now added to Figure 4c, showing how air bubbles, forming through degassing at the high temperatures required for Taq polymerase, disrupt the measurement, as they momentarily dry off the channel and stop the reaction until the channel fills again. Figure caption has been adapted and now reads: “[…] Dotted lines show the data from independent repeats. Air bubbles formed through degassing can momentarily disrupt the reaction. […]”

We additionally changed the main text to explain the reader the experimental difficulties: “[…] In other repetitions of the reaction, this increase was sometimes even observed earlier, around the one-hour mark (dotted lines). However, air bubbles nucleated by degassing events rise and temporarily dry out the channel, interrupting the reaction until the liquid refills the channel (Supplementary Movies 4,4b,4c\&5). Despite our best efforts, we were unable to fully prevent this, especially given the high temperatures required for Taq polymerase activity. In an identical setting when the gas- and water flux were switched off, no fluorescence increase was found (See Fig. 4(c) red lines). Fluorescence variations are additionally caused by fluctuations in the position of the gas-water interface, as discussed earlier. […]”

I think some caution is warranted in interpreting the PCR results because a primer-dimer would be of essentially the same length as the product. It appears as though the experiment has worked as described, but it's very difficult to be certain of this given this limitation. Doing the PCR with a significantly longer amplicon would be ideal, or alternately discussing this possible limitation would be helpful to the readers in managing expectations.

This is a good point and should be discussed more in the manuscript. Our gel electrophoresis is capable of distinguishing between replicate and primer dimers. We know this since we were optimizing the primers and template sequences to minimize primer dimers, making it distinguishable from the desired 61mer product. That said, all of the experiments performed without a template strand added did not show any band in the vicinity of the product band after 4h of reaction, in contrast to the experiments with template, presenting a strong argument against the presence of primer dimers.

We added a main text section explaining this to the reader: “[…]Suppl. Fig. IX.2 shows all independent repeats of the corresponding experiments. No product was detected in any of these cases, ruling out reaction limitations such as primer dimer formation. Primer dimers would form even in the absence of a template strand and would be identifiable through gel electrophoresis. As Taq polymerase requires a significant overlap between the two dimers to bind, this would result in a shorter product compared to the 61mer used here.  […]”

Reviewer #2 (Public review):

Schwintek et al. investigated whether a geological setting of a rock pore with water inflow on one end and gas passing over the opening of the pore on the other end could create a non-equilibrium system that sustains nucleic acid reactions under mild conditions. The evaporation of water as the gas passes over it concentrates the solutes at the boundary of evaporation, while the gas flux induces momentum transfer that creates currents in the water that push the concentrated molecules back into the bulk solution. This leads to the creation of steady-state regions of differential salt and macromolecule concentrations that can be used to manipulate nucleic acids. First, the authors showed that fluorescent bead behavior in this system closely matched their fluid dynamic simulations. With that validation in hand, the authors next showed that fluorescently labeled DNA behaved according to their theory as well. Using these insights, the authors performed a FRET experiment that clearly demonstrated the hybridization of two DNA strands as they passed through the high Mg++ concentration zone, and, conversely, the dissociation of the strands as they passed through the low Mg++ concentration zone. This isothermal hybridization and dissociation of DNA strands allowed the authors to perform an isothermal DNA amplification using a DNA polymerase enzyme. Crucially, the isothermal DNA amplification required the presence of the gas flux and could not be recapitulated using a system that was at equilibrium. These experiments advance our understanding of the geological settings that could support nucleic acid reactions that were key to the origin of life.

The presented data compellingly supports the conclusions made by the authors. To increase the relevance of the work for the origin of life field, the following experiments are suggested:

(1) While the central premise of this work is that RNA degradation presents a risk for strand separation strategies relying on elevated temperatures, all of the work is performed using DNA as the nucleic acid model. I understand the convenience of using DNA, especially in the latter replication experiment, but I think that at least the FRET experiments could be performed using RNA instead of DNA.

We understand the request only partially. The modification brought about by the two dye molecules in the FRET probe to be able to probe salt concentrations by melting is of course much larger than the change of the backbone from RNA to DNA. This was the reason why we rather used the much more stable DNA construct which is also manufactured at a lower cost and in much higher purity also with the modifications. But we think the melting temperature characteristics of RNA and DNA in this range is enough known that we can use DNA instead of RNA for probing the salt concentration in our flow cycling.

Only at extreme conditions of pH and salt, RNA degradation through transesterification, especially under alkaline conditions is at least several orders of magnitude faster than spontaneous degradative mechanisms acting upon DNA [Li, Y., & Breaker, R. R. (1999). Kinetics of RNA degradation by specific base catalysis of transesterification involving the 2 ‘-hydroxyl group. Journal of the American Chemical Society, 121(23), 5364-5372.]. The work presented in this article is however focussed on hybridization dynamics of nucleic acids. Here, RNA and DNA share similar properties regarding the formation of double strands and their respective melting temperatures. While RNA has been shown to form more stable duplex structures exhibiting higher melting temperatures compared to DNA [Dimitrov, R. A., & Zuker, M. (2004). Prediction of hybridization and melting for double-stranded nucleic acids. Biophysical Journal, 87(1), 215-226.], the general impact of changes in salt, temperature and pH [Mariani, A., Bonfio, C., Johnson, C. M., & Sutherland, J. D. (2018). pH-Driven RNA strand separation under prebiotically plausible conditions. Biochemistry, 57(45), 6382-6386.] on respective melting temperatures follows the same trend for both nucleic acid types. Also the diffusive properties of RNA and DNA are very similar [Baaske, P., Weinert, F. M., Duhr, S., Lemke, K. H., Russell, M. J., & Braun, D. (2007). Extreme accumulation of nucleotides in simulated hydrothermal pore systems. Proceedings of the National Academy of Sciences, 104(22), 9346-9351.].

Since this work is a proof of principle for the discussed environment being able to host nucleic acid replication, we aimed to avoid second order effects such as degradation by hydrolysis by using DNA as a proxy polymer. This enabled us to focus on the physical effects of the environment on local salt and nucleic acid concentration. The experiments performed with FRET are used to visualize local salt concentration changes and their impact on the melting temperature of dissolved nucleic acids.  While performing these experiments with RNA would without doubt cover a broader application within the field of origin of life, we aimed at a step-by-step / proof of principle approach, especially since the environmental phenomena studied here have not been previously investigated in the OOL context. Incorporating RNA-related complexity into this system should however be addressed in future studies. This will likely require modifications to the experimental boundary conditions, such as adjusting pH, temperature, and salt concentration, to account for the greater duplex stability of RNA. For instance, lowering the pH would reduce the RNA melting temperature [Ianeselli, A., Atienza, M., Kudella, P. W., Gerland, U., Mast, C. B., & Braun, D. (2022). Water cycles in a Hadean CO2 atmosphere drive the evolution of long DNA. Nature Physics, 18(5), 579-585.].

(2) Additionally, showing that RNA does not degrade under the conditions employed by the authors (I am particularly worried about the high Mg++ zones created by the flux) would further strengthen the already very strong and compelling work.

Based on literature values for hydrolysis rates of RNA [Li, Y., & Breaker, R. R. (1999). Kinetics of RNA degradation by specific base catalysis of transesterification involving the 2 ‘-hydroxyl group. Journal of the American Chemical Society, 121(23), 5364-5372.], we estimate RNA to have a half-life of multiple months under the deployed conditions in the FRET experiment (High concentration zones contain <1mM of Mg2+). Additionally, dsRNA is multiple orders of magnitude more stable than ssRNA with regards to degradation through hydrolysis [Zhang, K., Hodge, J., Chatterjee, A., Moon, T. S., & Parker, K. M. (2021). Duplex structure of double-stranded RNA provides stability against hydrolysis relative to single-stranded RNA. Environmental Science & Technology, 55(12), 8045-8053.], improving RNA stability especially in zones of high FRET signal. Furthermore, at the neutral pH deployed in this work, RNA does not readily degrade. In previous work from our lab [Salditt, A., Karr, L., Salibi, E., Le Vay, K., Braun, D., & Mutschler, H. (2023). Ribozyme-mediated RNA synthesis and replication in a model Hadean microenvironment. Nature Communications, 14(1), 1495.], we showed that the lifetime of RNA under conditions reaching 40mM Mg2+ at the air-water interface at 45°C was sufficient to support ribozymatically mediated ligation reactions in experiments lasting multiple hours.

With that in mind, gaining insight into the median Mg2+ concentration across multiple averaged nucleic acid trajectories in our system (see Fig. 3c&d) and numerically convoluting this with hydrolysis dynamics from literature would be highly valuable. We anticipate that longer residence times in trajectories distant from the interface will improve RNA stability compared to a system with uniformly high Mg2+ concentrations.

Added a new Supplementary section for this. We used the trace from Figure 3(c) and calculated the hydrolysis rate for each timestep by using literature values from RNA [Li, Y., & Breaker, R. R. (1999). Kinetics of RNA degradation by specific base catalysis of transesterification involving the 2 ‘-hydroxyl group. Journal of the American Chemical Society, 121(23), 5364-5372.]. We conclude that the conditions deployed for the experiment are not harsh on RNA, with hydrolysis rates in the E-6 1/min regime. The figure below (also now in the supplementary information) shows the hydrolysis of RNA deployed under the conditions of the experiment in Figure 3. RNA is not expected to hydrolyze under these conditions and timescales, in which a replication reaction would occur. With a half life of around 83 days, even a prebiotically plausible – very slow – replication reaction would not be constrained by hydrolysis boundary conditions in this scenario.

Referenced to this section in the supplementary information in the maintext: […] In the experimental conditions used here, RNA would also not readily degrade, even if the strand enters the high salt regimes (See Suppl. Sec. IX). Using literature values for hydrolysis rates under the deployed conditions, we estimate dissolved RNA to have a half life of around 83 days. […]

(3) Finally, I am curious whether the authors have considered designing a simulation or experiment that uses the imidazole- or 2′,3′-cyclic phosphate-activated ribonucleotides. For instance, a fully paired RNA duplex and a fluorescently-labeled primer could be incubated in the presence of activated ribonucleotides +/- flux and subsequently analyzed by gel electrophoresis to determine how much primer extension has occurred. The reason for this suggestion is that, due to the slow kinetics of chemical primer extension, the reannealing of the fully complementary strands as they pass through the high Mg++ zone, which is required for primer extension, may outcompete the primer extension reaction. In the case of the DNA polymerase, the enzymatic catalysis likely outcompetes the reannealing, but this may not recapitulate the uncatalyzed chemical reaction.

This is certainly on our to-do list for future experiments in this setting. Our current focus is on templated ligation rather than templated polymerization and we are working hard to implement RNA-only enzyme-free ligation chain reaction, based on more optimized parameters for the templated ligation from 2’3’-cyclic phosphate activation that was just published [High-Fidelity RNA Copying via 2′,3′-Cyclic Phosphate Ligation, Adriana C. Serrão, Sreekar Wunnava, Avinash V. Dass, Lennard Ufer, Philipp Schwintek, Christof B. Mast, and Dieter Braun, JACS doi.org/10.1021/jacs.3c10813 (2024)]. But we first would try this at an air-water interface which was shown to work with RNA in a temperature gradient [Ribozyme-mediated RNA synthesis and replication in a model Hadean microenvironment, Annalena Salditt, Leonie Karr, Elia Salibi, Kristian Le Vay, Dieter Braun & Hannes Mutschler, Nature Communications doi.org/10.1038/s41467-023-37206-4 (2023)] before making the jump to the isothermal setting we describe here. So we can understand the question, but it was good practice also in the past to first get to know the setting with PCR, then jump to RNA.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Could the authors comment on the likelihood of the geological environments where the water inflow velocity equals the evaporation velocity?

This is an important point to mention in the manuscript, thank you for pointing that out. To produce a defined experiment, we were pushing the water out with a syringe pump, but regulated in a way that the evaporation was matching our flow rate. We imagine that a real system will self-regulate the inflow of the water column on the one hand side by a more complex geometry of the gas flow, matching the evaporation with the reflow of water automatically. The interface would either recede or move closer to the gas flux, depending on whether the inflow exceeds or falls short of the evaporation rate. As the interface moves closer, evaporation speeds up, while moving away slows it down. This dynamic process stabilizes the system, with surface tension ultimately fixing the interface in place.

We have seen a bit of this dynamic already in the experiments, could however so far not yet find a good geometry within our 2-dimensional constant thickness geometry to make it work for a longer time. Very likely having a 3-dimensional reservoir of water with less frictional forces would be able to do this, but this would require a full redesign of a multi-thickness microfluidics. The more we think about it, the more we envisage to make the next implementation of the experiment with a real porous volcanic rock inside a humidity chamber that simulates a full 6h prebiotic day. But then we would lose the whole reproducibility of the experiment, but likely gain a way that recondensation of water by dew in a cold morning is refilling the water reservoirs in the rocks again. Sorry that I am regressing towards experiments in the future.

We added a paragraph after the second paragraph in Results and Discussion.

It now reads: […] For a real early Earth environment we envision a system that self-regulates the water column's inflow by automatically balancing evaporation with capillary flows. The interface adjusts its position relative to the gas flux, moving closer if the inflow is less than the evaporation rate, or receding if it exceeds it. When the interface nears the gas flux, evaporation accelerates, while moving it away slows evaporation. This dynamic process stabilizes the system, with surface tension ultimately fixing the interface's position. […]

(2) Could the authors speculate on using gases other than ambient air to provide the flux and possibly even chemical energy? For example, using carbonyl sulfide or vaporized methyl isocyanide could drive amino acid and nucleotide activation, respectively, at the gas-water interface.

This is an interesting prospect for future work with this system. We thought also about introducing ammonia for pH control and possible reactions. We were amazed in the past that having CO2 instead of air had a profound impact on the replication and the strand separation [Water cycles in a Hadean CO2 atmosphere drive the evolution of long DNA, Alan Ianeselli, Miguel Atienza, Patrick Kudella, Ulrich Gerland, Christof Mast & Dieter Braun, Nature Physics doi.org/10.1038/s41567-022-01516-z (2022)]. So going more in this direction absolutely makes sense and as it acts mostly on the length-selectively accumulated molecules at the interface, only the selected molecules will be affected, which adds to the selection pressure of early evolutionary scenarios.

Of course, in the manuscript, we use ambient air as a proxy for any gas, focusing primarily on the energy introduced through momentum transfer and evaporation. We speculate that soluble gasses could establish chemical gradients, such as pH or redox potential, from the bulk solution to the interface, similar to the Mg2+ accumulation shown in Figure 3c. The nature of these gradients would depend on each gas's solubility and diffusivity. We have already observed such effects in thermal gradients [Keil, L. M., Möller, F. M., Kieß, M., Kudella, P. W., & Mast, C. B. (2017). Proton gradients and pH oscillations emerge from heat flow at the microscale. Nature communications, 8(1), 1897.] and finding similar behavior in an isothermal environment would be a significant discovery.

Added a paragraph in the Conclusion to showcase this: [… ] Furthermore we expect that other gases, such as CO2, could establish chemical gradients in this environment. Such gradients have been observed in thermal gradients before [23] and finding similar behaviour in an isothermal environment would be a significant discovery.[…]

(3) Line 162: Instead of "risk," I suggest using "rate".

Thanks for pointing this out! Will be changed.

Fixed.

(4) Using FRET of a DNA duplex as an indicator of salt concentration is a decent proxy, but a more direct measurement of salt concentration would provide further merit to the explicit statement that it is the salt concentration that is changing in the system and not another hidden parameter.

Directly observing salt concentration using microscopy is a difficult task. While there are dyes that change their fluorescence depending on the local Na+ or Mg2+ concentration, they are not operating differentially, i.e. by making a ratio between two color channels. Only then we are not running into artifacts from the dye molecules being accumulated by the non-equilibrium settings. We were able to do this for pH in the past, but did not find comparable optical salt sensors. This is the reason we ended up with a FRET pair, with the advantage that we actually probe the strand separation that we are interested in anyhow. Using such a dye in future work would however without a doubt enhance the understanding of not only this system, but also our thermal gradient environments.

(5) Figure 3a: Could the authors add information on "Dried DNA" to the caption? I am assuming this is the DNA that dried off on the sides of the vessel but cannot be sure.

Thanks to the reviewer for pointing this out. This is correct and we will describe this better in the revised manuscript.

Added a sentence in the caption to address this: […] Fluctuations in interface position can dry and redissolve DNA repeatedly (see “Dried DNA” in right panel). […]

(6) Figure 4b and c: How reproducible is this data? Have the authors performed this reaction multiple independent times? If so, this data should be added to the manuscript.

The data from the gel electrophoresis was performed in triplicates and is shown in full in supplementary information. The data in c is hard to reproduce, as the interface is not static and thus ROI measurements are difficult to perform as an average of repeats. Including the data from the independent repeats will however give the reader insight into some of the experimental difficulties, such as air bubbles, which form from degassing as the liquid heats up, that travel upwards to the interface, disrupting the ongoing fluorescence measurements.

This was also pointed out by reviewer 1 and addressed there.

(7) Line 256: "shielding from harmful UV" statement only applies to RNA oligomers as UV light may actually be beneficial for earlier steps during ribonucleoside synthesis. I suggest rephrasing to "shielding nucleic acid oligomers from UV damage.".

Will be adjusted as mentioned.

Fixed.

(8) The final paragraph in the Results and Discussion section would flow better if placed in the Conclusion section.

This is a good point and we will merge results and discussion closer together.

Fixed.

(9) Line 262, "...of early Life" is slightly overstating the conclusions of the study. I suggest rephrasing to "...of nucleic acids that could have supported early life."

This is a fair comment. We thank the reviewer for his detailed analysis of the manuscript!

Changed the phrase to: […]In this work we investigated a prebiotically plausible and abundant geological environment to support the replication of nucleic acids. […]

(10) In references, some of the journal names are in sentence case while others are in title case (see references 23 and 26 for example).

Thanks - this will be fixed.

Fixed.

Author response:

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

Reviewer #1 (Public Review):

This study provides compelling evidence that RAR, rather than its obligate dimerization partner RXR, is functionally limiting for chromatin binding. This manuscript provides a paradigm for how to dissect the complicated regulatory networks formed by dimerizing transcription factor families.

Dahal and colleagues use advanced SMT techniques to revisit the role of RXR in DNA-binding of the type-2 nuclear receptor (T2NR) RAR. The dominant consensus model for regulated DNA binding of T2NRs posits that they compete for a limited pool of RXR to form an obligate T2NR-RXR dimer. Using advanced SMT and proximity-assisted photoactivation technologies, Dahal et al. now test the effect of manipulating the endogenous pool size of RAR and RXR on heterodimerization and DNA-binding in live U2OS cells. Surprisingly, it turns out that RAR, rather than RXR, is functionally limiting for heterodimerization and chromatin binding. By inference, the relative pool size of various T2NRs expressed in a given cell, rather than RXR, is likely to determine chromatin binding and transcriptional output.

The conclusions of this study are well supported by the experimental results and provide unexpected novel insights into the functioning of the clinically important class of T2NR TFs. Moreover, the presented results show how the use of novel technologies can put long-standing theories on how transcription factors work upside down. This manuscript provides a paradigm for how to further dissect the complicated regulatory networks formed by T2NRs or other dimerizing TFs. I found this to be a complete story that does not require additional experimental work. However, I do have some suggestions for the authors to consider.

Reviewer #1 (Recommendations For The Authors):

(1) Does the increased chromatin binding measured when the RAR levels are increased reflect a higher occupancy of a similar set of loci, or are additional loci bound? The authors could discuss this issue in the context of the published literature. Obviously, this could be addressed experimentally by ChIP-seq or a similar analysis, but this would extend beyond the main topic of this manuscript.

We attempted to explore this experimentally using ChIP-seq with multiple RAR- and RXR-specific antibodies. Unfortunately, our results were inconclusive, as the antibody enrichment relative to the IgG control was insufficient for reliable interpretation. Specifically, our ChIP-seq enrichment levels were only around 1.5fold, while the accepted standard for meaningful ChIP enrichment is typically at least 2-fold. Due to these technical limitations, we decided to defer these experiments for now.

However, we agree with the reviewer that understanding whether the increased chromatin binding of RAR reflects higher occupancy at the same set of loci or binding to additional loci is a key question. In similar experiments involving the transcription factor TFEB (Esbin et al., 2024, Genes Dev, doi: 10.1101/gad.351633.124) where an increase in the SMT bound fraction occurred, both scenarios—higher occupancy at known loci and binding to additional loci in ChIP-seq was observed. So, addressing this intriguing possibility in future studies focused on RAR and RXR would be interesting.

(2) The results presented suggest convincingly that endogenous RXR is normally in excess to its binding partners (in U2OS cells). This point could be strengthened further by reducing RXR levels, e.g., by knocking out 1 allele or the use of shRNAs (although the latter method might be too hard to control). Overexpression of another T2NR might also help determine the buffer capacity of RXR.

We appreciate the reviewers’ acknowledgment that our results convincingly demonstrate that endogenous RXR is typically in excess relative to its binding partners in U2OS cells. We agree that this conclusion could be further reinforced by experiments such as overexpression of another T2NR to test RXR's buffering capacity. We are actively pursuing follow-up experiments involving overexpression of additional T2NRs to address this question in more detail. These studies are ongoing, and we plan to explore the buffer capacity of RXR more extensively in a future manuscript.

(3) The ~10% difference in fbound of RAR and RXR (in Figs 1 and 2), while they should be 1:1 dimers, is explained by invoking the expression of RXR isoforms. Can the authors be more specific concerning the nature of these isoforms?

We have provided detailed information about different T2NRs expressed in U2OS cells according to the Expression Atlas and the Human Protein Atlas Database in Supplementary Table S1. Table S1 specifically shows that both isoforms of RXRα and RXRβ are expressed in U2OS cells. Additionally, the caption of Table S1 explicitly notes the presence of isoform RXRβ in U2OS cells. In the main text, we reference Table S1 when discussing the 10% difference in fbound between RARα and RXRα, and we have now suggested that the expression of RXRβ likely accounts for the observed discrepancy.

Reviewer #2 (Public Review):

Summary:

In the manuscript "Surprising Features of Nuclear Receptor Interaction Networks Revealed by Live Cell Single Molecule Imaging", Dahal et al combine fast single molecule tracking (SMT) with proximity-assisted photoactivation (PAPA) to study the interaction between RARa and RXRa. The prevalent model in the nuclear receptor field suggests that type II nuclear receptors compete for a limiting pool of their partner RXRa. Contrary to this, the authors find that over-expression of RARa but not RXRa increases the fraction of RXRa molecules bound to chromatin, which leads them to conclude that the limiting factor is the abundance of RARa and not RXRa. The authors also perform experiments with a known RARa agonist, all trans retinoic acid (atRA) which has little effect on the bound fraction. Using PAPA, they show that chromatin binding increases upon dimerization of RARa and RXRa.

Strengths:

In my view, the biggest strength of this study is the use of endogenously tagged RARa and RXRa cell lines. As the authors point out, most previous studies used either in vitro assays or over-expression. I commend the authors on the generation of single-cell clones of knock-in RARa-Halo and Halo-RXRa. The authors then carefully measure the abundance of each protein using FACS, which is very helpful when comparing across conditions. The manuscript is generally well written and figures are easy to follow. The consistent color-scheme used throughout the manuscript is very helpful.

Weaknesses:

(1) Agonist treatment:

The authors test the effect of all trans retinoic acid (atRA) on the bound fraction of RARa and RXRa and find that "These results are consistent with the classic model in which dimerization and chromatin binding of T2NRs are ligand independent." However, all the agonist treatments are done in media containing FBS. FBS is not chemically defined and has been found to have between 10 and 50 nM atRA (see references in PMID 32359651 for example). The addition of 1 nM or 100 nM atRA is unlikely to result in a strong effect since the medium already contains comparable or higher levels of agonist. To test their hypothesis of ligand-independent dimerization, the authors should deplete the media of atRA by growing the cells in a medium containing charcoal-stripped FBS for at least 24 hours before adding agonist.

We acknowledge the reviewer's concern regarding the presence of atRA in FBS and agree that it may introduce baseline levels of agonist. However, in our experiments, both the 1 nM and 100 nM atRA treatments resulted in observable changes in RAR expression levels (Figure S3C). Additionally, the luciferase assays demonstrated that 100 nM atRA significantly increased retinoic acid-responsive promoter activity (Figure S1C). Given these clear responses to atRA, we believe the observed lack of effect on the chromatin-bound fraction cannot be attributed to the presence of comparable or higher levels of atRA in the FBS, as the reviewer suggests. Moreover, since our results align with the established literature and do not impact the core findings of our study, we decided not to pursue the suggested experiments with charcoal-stripped FBS in this manuscript.  

(2) Photobleaching and its effect on bound fraction measurements:

The authors discard the first 500 to 1000 frames due to the high localization density in the initial frames. This will preferentially discard bound molecules that will bleach in the initial frames of the movie and lead to an over-estimation of the unbound fraction.

For experiments with over-expression of RAR-Halo and Halo-RXR, the authors state that the cells were pre-bleached and that these frames were used to calculate the mean intensity of the nuclei. When pre-bleaching, bound molecules will preferentially bleach before the diffusing population. This will again lead to an over-representation of the unbound fraction since this is the population that will remain relatively unaffected by the pre-bleaching. Indeed, the bound fraction for over-expressed RARa and RXRa is significantly lower than that for the corresponding knock in lines. To confirm whether this is a biological result, I suggest that the authors either reduce the amount of dye they use so that this pre-bleaching is not necessary or use the direct reactivation strategy they use for their PAPA experiments to eliminate the pre-bleaching step.

As for the measurement of the nuclear intensity, since the authors have access to multiple HaloTag dyes, they can saturate the HaloTagged proteins with a high concentration of JF646 or JFX650 to measure the mean intensity of the protein while still using the PA-JFX549 for SMT. Together, these will eliminate the need to prebleach or discard any frames.

The Janelia Fluor dyes used in our experiments are known for their high photostability (Grimm et al., 2021, JACS Au, doi: 10.1021/jacsau.1c00006). During the initial 80 ms imaging to calculate the mean nuclear intensity, the laser power was kept at very low intensity (~3%) for a brief duration (~10 seconds), in contrast to the high-intensity (~100%) used during the tracking experiments, which span around 3 minutes. This low-power illumination does not induce significant photobleaching but merely puts the dyes in a temporary dark state. Therefore, this pre-bleaching step closely resembles the direct reactivation strategy employed in our PAPA experiments.

To further address the reviewer's concern, we performed a frame cut-off analysis for our SMT movies of endogenous RARα-Halo and over-expressed RARα-Halo (Figure S9B). The analysis shows no significant change in the bound fraction of either endogenous or over-expressed RARα-Halo when discarding the initial 1000 frames. Based on these results, we conclude that the pre-bleaching does not lead to an overestimation of the unbound fraction, and that our experimental approach is robust.

(3) Heterogeneous expression of the SNAP fusion proteins:

The cell lines expressing SNAP tagged transgenes shown in Fig S6 have very heterogeneous expression of the SNAP proteins. While the bulk measurements done by Western blotting are useful, while doing single-cell experiments (especially with small numbers - ~20 - of cells), it is important to control for expression levels. Since these transgenic stable lines were not FACS sorted, it would be helpful for the reader to know the spread in the distribution of mean intensities of the SNAP proteins for the cells that the SMT data are presented for. This step is crucial while claiming the absence of an effect upon over-expression and can easily be done with a SNAPTag ligand such as SF650 using the procedure outlined for the over-expressed HaloTag proteins.

We agree with the reviewer that there is heterogeneity in SNAP protein expression across the transgenic lines. In response to the reviewer’s suggestion, we performed the proposed experiment to assess the distribution of mean intensities for two key experimental conditions: Halo-RXRα with overexpressed RARα-SNAP and HaloRXRα with overexpressed RARαRR-SNAP. These results again confirm that the increase in chromatin-bound fraction of Halo-RXRα is observed only in the presence of RARα capable of heterodimerizing with RXRα, supporting our main conclusion (Figure S9).

For these experiments, we followed the same labelling procedure described in the methods section for tracking endogenous Halo-tagged proteins alongside transgenic SNAP proteins. As shown in Figure S9, for ~ 70 cell nuclei, the distribution of mean intensities is similar for both conditions, with the bound fraction of Halo-RXRα significantly increasing in the presence of RARα-SNAP compared to RARαRR-SNAP. This analysis underscores that the observed effects are indeed due to the functional differences between the two RARα variants rather than variability in expression levels.

(4) Definition of bound molecules:

The authors state that molecules with a diffusion coefficient less than 0.15 um2/s are considered bound and those between 1-15 um2/s are considered unbound. Clarification is needed on how this threshold was determined. In previous publications using saSPT, the authors have used a cutoff of 0.1 um2/s (for example, PMID 36066004, 36322456). Do the results rely on a specific cutoff? A diffusion coefficient by itself is only a useful measure of normal diffusion. Bound molecules are unlikely to be undergoing Brownian motion, but the state array method implemented here does not seem to account for non-normal diffusive modes. How valid is this assumption here?

We acknowledge the inconsistency in the diffusion coefficient thresholds for defining the chromatin-bound fraction used across our group’s publications. The choice of threshold or cutoff (0.1 µm²/s vs 0.15 µm²/s) is largely arbitrary and does not significantly impact the results. To validate this, we tested the effect of different cutoffs on fbound (%) for endogenously expressed Halo-tagged RARα and RXRα (Figure S10). As shown in Figure S10, there was no substantial difference in fbound (%) calculated using a 0.1 µm²/s versus 0.15 µm²/s cutoff (e.g., RARα clone c156: 47±1% vs 49±1%; RXRα clone D6: 34±1% vs 35±1%). 

Since we have consistently applied the 0.15 µm²/s cutoff throughout this manuscript across all experimental conditions, the comparative analysis of fbound (%) remains valid. While we agree that a Brownian diffusion model may not fully capture the motion of bound molecules, our state array model accounts for localization error, which likely incorporates some of the chromatin motion features. Moreover, the distinction between bound (<0.15 µm²/s) and unbound (1-15 µm²/s) populations is sufficiently large that using a normal diffusion model is reasonable for our analysis.

(5) Movies:

Since this is an imaging manuscript, I request the authors to provide representative movies for all the presented conditions. This is an essential component for a reader to evaluate the data and for them to benchmark their own images if they are to try to reproduce these findings.

We have now included representative movies for all the SMT experimental conditions presented in the manuscript. Please see data availability section of the manuscript.

(6) Definition of an ROI:

The authors state that "ROI of random size but with maximum possible area was selected to fit into the interior of the nuclei" while imaging. However, the readout speed of the Andor iXon Ultra 897 depends on the size of the defined ROI. If the ROI was variable for every movie, how do the authors ensure the same sampling rate?

We used the frame transfer mode on the Andor iXon Ultra 897 camera for our acquisitions, which allows for fast frame rate measurements without altering the exposure time between frames. Additionally, we verified the metadata of all our movies to ensure a consistent frame interval of 7.4 ms across all conditions. This confirms that the sampling rate was maintained uniformly, despite the variability in ROI size. 

Reviewer #2 (Recommendations For The Authors):

(1) 'Hoechst' is mis-spelled.

We have now corrected this typo in the manuscript.

(2) Cos7 appears in several places throughout the text. I assume this is a typo. If so, please correct it. If not, please explain if some experiments were done in Cos7 cells and kindly provide a justification for that.

The use of Cos7 cells is intentional and not a typo. Cos7 cells have been previously utilized in studies investigating the interaction between T2NRs (Kliewer et al., 1992, Nature, doi: 10.1038/355446a0). In our study, due to technical issues with antibodies for coIP in U2OS cells, we initially used Cos7 cells for control experiments to verify that Halo-tagging of RARα and RXRα did not disrupt their interaction, by transiently expressing the constructs in Cos7 cells. Following these control experiments, we confirmed the direct interaction of endogenously expressed RAR and RXR in U2OS cells with their respective binding partners using the SMT-PAPA assay. Since these results confirmed that Halo-tagging did not interfere with RAR-RXR interactions, we chose not to repeat the coIP experiments in U2OS cells.

Reviewer #3 (Public Review):

Summary:

This study aims to investigate the stoichiometric effect between core factors and partners forming the heterodimeric transcription factor network in living cells at endogenous expression levels. Using state-of-the-art single-molecule analysis techniques, the authors tracked individual RARα and RXRα molecules labeled by HALO-tag knock-in. They discovered an asymmetric response to the overexpression of counter-partners. Specifically, the fact that an increase in RARα did not lead to an increase in RXRα chromatin binding is incompatible with the previous competitive core model. Furthermore, by using a technique that visualizes only molecules proximal to partners, they directly linked transcription factor heterodimerization to chromatin binding.

Strengths:

The carefully designed experiments, from knock-in cell constructions to singlemolecule imaging analysis, strengthen the evidence of the stoichiometric perturbation response of endogenous proteins. The novel finding that RXR, previously thought to be a target of competition among partners, is in excess provides new insight into key factors in dimerization network regulation. By combining the cutting-edge single-molecule imaging analysis with the technique for detecting interactions developed by the authors' group, they have directly illustrated the relationship between the physical interactions of dimeric transcription factors and chromatin binding. This has enabled interaction analysis in live cells that was challenging in single-molecule imaging, proving it is a powerful tool for studying endogenous proteins.

Weaknesses:

As the authors have mentioned, they have not investigated the effects of other T2NRs or RXR isoforms. These invisible factors leave room for interpretation regarding the origin of chromatin binding of endogenous proteins (Recommendations 4). In the PAPA experiments, overexpressed factors are visualized, but changes in chromatin binding of endogenous proteins due to interactions with the overexpressed proteins have not been investigated. This might be tested by reversing the fluorescent ligands for the Sender and Receiver. Additionally, the PAPA experiments are likely to be strengthened by control experiments (Recommendations 5).

We agree that this would be an interesting experiment. However, there are three technical challenges that complicate its implementation: First, as demonstrated in our original PAPA paper, dark state formation is less efficient when dyes are conjugated to Halo compared to SNAPf, making the reverse configuration less optimal. Second, SNAPf-tagged proteins have slower labeling kinetics than Halotagged proteins, often resulting in under-labeling of SNAPf. Third, our SNAPf transgenes were integrated polyclonally. Since background PAPA scales with the concentration of the sender-labeled protein, variable concentrations of the senderlabeled SNAPf proteins would introduce significant variability, complicating the interpretation of the background PAPA signal. Due to these concerns, we believe that performing reciprocal measurements with reversed fluorescent ligands may not yield reliable results. 

Reviewer #3 (Recommendations For The Authors):

(1) The term "Surprising features" in the title is ambiguous and may force readers to search for what it specifically refers to. Including a word that evokes specific features might be helpful.

Our findings contradict previous work, which suggested that chromatin binding of T2NRs is regulated by competition for a limited pool of RXR. In contrast, we found that RAR expression can limit RXR chromatin binding, but not the other way around, which challenges the existing model. This unexpected result is what we refer to as a "surprising feature" in our title, and we believe it accurately reflects the novel insights our study provides. We also think that this is clearly conveyed in our manuscript abstract, supporting the use of "Surprising features" in the title. 

(2) p.3, line 11 - The threshold of 0.15 μm2s-1 seems to be a crucial value directly linked to the value of fbound. What is the rationale for choosing this specific value? If consistent conclusions can be obtained using threshold values that are similar but different, it would strengthen the robustness of the results.

Please refer to our response to Reviewer #2’s Public Review point 4. The threshold choice is arbitrary and doesn’t affect the overall conclusions. To test this, we compared fbound (%) values calculated using both 0.1 μm²s-1 and 0.15 μm²s-1 cutoffs. For example, with endogenously expressed Halo-tagged RARα (clone c156), we observed fbound values of 47±1% vs 49±1%, and for RXRα (clone D6), 34±1% vs 35±1%, respectively (Figure S10). Since we have consistently applied the 0.15 μm²s-1 cutoff across all experimental conditions in this manuscript, the comparisons of fbound (%) between different conditions are robust and valid.

(3) p.4, line 13 - "the fbound of endogenous RARα-Halo (47{plus minus}1%) was largely unchanged upon expression of SNAP (47{plus minus}1%)" part of the sentence is not surprising. It would make more sense if it were expressed as "the fbound of endogenous RARα-Halo (47{plus minus}1%) was largely unchanged upon expression of RXRα-SNAP (49{plus minus}1%), consistent with the control SNAP (47{plus minus}1%).".

We understand how the original phrasing may be confusing to the readers and have restructured the sentence as suggested by the reviewer for clarity.

(4) p.6, line 26 - The discussion that "most chromatin binding of endogenous RXRα in U2OS cells depends on heterodimerization partners other than RARα" seems to contradict the top right figure in Figure 4. If that's the case, the binding partner for the bound red molecule might be yellow rather than blue. Given a decrease in the number of RARα molecules with an unchanged binding ratio, the total number of binding molecules has decreased. Could it be interpreted that the potential reduction in RXRα chromatin binding, accompanying the decrease in binding RARα, is compensated for by other partners?

We agree with the reviewer that both the yellow and blue molecules in Figure 4 represent T2NRs that can heterodimerize with RXR. For simplicity, we chose to omit the depiction of RXR dimerization with other T2NRs (represented in yellow) in Figure 4. We have now included a note in the figure caption to clarify this. We plan to follow up on the buffer capacity of RXR with other T2NRs in a separate manuscript and will discuss this aspect in more detail once we have data from those experiments.

(5) Fig. 3 - I expected that DR localizations always appear more frequently than PAPA localizations by the difference in the number of distal molecules. Why does the linear line for SNAP-RXRα in Fig. 3 B have a slope exceeding 1? Also, although the sublinearity is attributed to binding saturation, is there any possibility that this sublinearity originates from the PAPA system like the saturation of PAPA reactivation? Control samples like Halo-SNAPf-3xNLS might address these concerns.

The number of DR and PAPA localizations depends on the arbitrarily chosen intensity and duration of green and violet light pulses. For any given protein pair, different experimental settings can result in PAPA localizations being greater than, less than, or equal to the number of DR localizations. Therefore, the informative metric is not the absolute number of DR and PAPA localizations, but rather how the ratio of PAPA to DR localizations changes between different conditions—such as between interacting pairs and non-interacting controls.

Regarding the sublinearity, we agree that it is essential to consider whether the observed sublinearity might stem from saturation of the PAPA signal. We know of two ways in which this could occur:

First, PAPA can be saturated as the duration of the green light pulse increases and dark-state complexes are depleted. However, this cannot explain the nonlinearity that we observe, because the duration of the green light pulse is constant, and thus the probability that a given complex is reactivated by PAPA is also constant. Likewise, holding the violet pulse duration constant yields a constant probability that a given molecule is reactivated by DR. PAPA localizations are expected to scale linearly with the number of complexes, while DR localizations are expected to scale linearly with the total number of molecules. Sublinear scaling of PAPA localizations with DR localizations thus implies that the number of complexes scales sublinearly with the total concentration of the protein.

Second, saturation could occur if PAPA localizations are undercounted compared to DR localizations. While this is a valid concern, we consider it unlikely in this case because 1) our localization density is below the level at which our tracking algorithm typically undercounts localizations, and 2) we observe sublinearity for RXR → RAR PAPA even though the number of PAPA localizations is lower than the DR localizations; undercounting due to excessive localization density would be expected to introduce the opposite bias in this case.

(6) Fig. 4 - The differences between A, B, and C on the right side of the model are subtle, making it difficult to discern where to see. Emphasizing the difference in molecule numbers or grouping free molecules at the top might help clarify these distinctions.

We appreciate the reviewer’s feedback. In response, we have revised Figure 4 by grouping the free molecules on the top right side for panels A, B and C, as suggested.

(7) While the main results are obtained through single-molecule imaging, no singlemolecule fluorescence images or trajectory plots are provided. Even just for representative conditions, these could serve as a guide for readers trying to reproduce the experiments with different custom-build microscope setups. Also, considering data availability, depositing the source data might be necessary, at least for the diffusion spectra.

We have now included representative movies for all the presented SMT conditions as source data. Please see data availability section of the manuscript.

(8) Tick lines are not visible on many of the graph axes. 

We have revised the figures to ensure that the tick lines are now clearly visible on all graph axes.

(9) Inconsistencies in the formatting are present in the methods, such as "hrs" vs. "hours", spacing between numbers and units, and "MgCl2". "u" should be "μ" and "x" should be "×". 

We have corrected the formatting errors.

(10) Table S4, rows 16 and 17 - Are "RAR"s typos for "RXR"s? 

We have corrected this in the manuscript.

(11) p.10~12 - Are three "Hoestch"s typos for "Hoechst"s? 

This is now corrected in the manuscript.

(12) p.11, line 17 - According to the referenced paper, the abbreviation should be "HILO" in all capital letters, not "HiLO". 

This is now corrected in the manuscript.

(13) "%" on p.3, line 18, and "." on p.6, line 27 are missing. 

This missing “%”  and “.” are now added.

Author response:

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

Reviewer #1 (Public review):

Summary:

The manuscript by Yao S. and colleagues aims to monitor the potential autosomal regulatory role of the master regulator of X chromosome inactivation, the Xist long non-coding RNA. It has recently become apparent that in the human system, Xist RNA can not only spread in cis on the future inactive X chromosome but also reach some autosomal regions where it recruits transcriptional repression and Polycomb marking. Previous work has also reported that Xist RNA can show a diffused signal in some biological contexts in FISH experiments.

In this study, the authors investigate whether Xist represses autosomal loci in differentiating female mouse embryonic stem cells (ESCs) and somatic mouse embryonic fibroblasts (MEFs). They perform a time course of ESC differentiation followed by Capture Hybridization of Associated RNA Targets (CHART) on both female and male ESCs, as well as pulldowns with sense oligos for Xist. The authors also examine transcriptional activity through RNA-seq and integrate this data with prior ChIP-seq experiments. Additional experiments were conducted in MEFs and Xist-ΔB repeat mutants, the latter fails to recruit Polycomb repressors.

Based on this experimental design, the authors make several bold claims:

(1) Xist binds to about a hundred specific autosomal regions.

(2) This binding is specific to promoter regions rather than broad spreading.

(3) Xist autosomal signal is inversely correlated with PRC1/2 marks but positively correlated with transcription.

(4) Xist targeting results in the attenuation of transcription at autosomal regions.

(5) The B-repeat region is important for autosomal Xist binding and gene repression.

(6) Xist binding to autosomal regions also occurs in somatic cells but does not lead to gene repression.

Together, these claims suggest that Xist might play a role in modulating the expression of autosomal genes in specific developmental and cellular contexts in mice.

Strengths:

This paper deals with an interesting hypothesis that Xist ncRNA can also function at autosomal loci.

Weaknesses: The claims reported in this paper are largely unsubstantiated by the data, with multiple misinterpretations, lacking controls, and inadequate statistics. Fundamental flaws in the experimental design/analysis preclude the validity of the findings. Major concerns are listed below: (1) The entire paper is based on the CHART observation that Xist is specifically targeted to autosomal promoters. Overall, the data analysis is flawed and does not support such conclusions. Importantly the sense WT and the 0h controls are not used, nor are the biological replicates. 

We respectfully disagree with Rev1 but nevertheless thank the reviewer for making some suggestions that helped to strengthen our manuscript.  We have provided new experiments and analyses in the revised manuscript. Please see responses below.

Rev1 seems to have missed or misunderstood some key experiments. In fact, the sense WT and 0h controls were shown. Furthermore, we included at least two biological replicates for each experiment.

We used both male ES cells (which do not express Xist) and sense probes as key negative controls, as outlined in Figure S1. Crucially, we only analyzed peaks that were reproducible between biological replicates. The Xist CHART peaks in differentiating female ES cells were significantly enriched above the “background” defined by the sense probe and male controls. Specifically, in comparison to undifferentiated female ES cells (day 0) where both X chromosomes are active and Xist is not induced, Xist CHART robustly pulled down the X chromosome during cell differentiation (day 4, day 7, and day 14). In contrast, male ES cells showed no significant pull-down of the X chromosome, and the sense group also exhibited markedly reduced binding (new Figure S1B). Furthermore, Principal Component Analysis (PCA) of CHART-seq reads (day 4 as an example) include Xist, sense, and input in WT and ΔRepB female, further confirmed that the sense probe CHART was clearly distinguishable from Xist CHART signals. Please see revised Figure S1C. Together, these findings underscore the specificity and robustness of our CHART results.

Data is typically visualized without quantification, and when quantified, control loci/gene sets are erroneously selected. Firstly, CHART validation on the X in FigS1 is misleading and not based on any quantifications (e.g., see the scale on Kdm6a (0-190) compared to Cdkl5 (0-40)). If scaled appropriately, there is Xist signal on the escapee. 

Rev1 may have misread the presented data. In the example raised by Rev1, Fig. S1 is inherently quantitative: e.g., a ratio is a number in Fig. S1A (now Fig. S1B) and all gene tracks in Fig. 1B-E are shown with scales. We showed X-linked genes in Fig. S1 (now Fig. S2) as a control to demonstrate that the CHART worked and that Xist accumulated over time from day 0 to day 14. Our new Figure 1B demonstrates the Xist accumulation in graph format. 

Our paper focuses on Xist autosomal binding sites. Thus, the X-linked examples were placed in the supplement. Escapee genes do in fact accumulate Xist at their promoter regions and this finding is consistent with data published by Simon et al. (2013, Nature). It was therefore not desirable in this paper to reanalyze X-linked genes, including escapees. Nevertheless, to address the reviewer’s concerns, we present new data in new Figure S3A. Here we analyzed the density of Xist binding across X-linked genes, including both active and inactive genes, as well as escapee genes. From this quantitative analysis, it should be clear that escapees do bind Xist. However, from the metagene plots in Figure S3B, we confirm the previous conclusion that escapees bind Xist at high levels just upstream of the promoter and that there is a depletion of Xist in the escapee gene body, consistent with a barrier preventing Xist from moving into the active gene. 

All X-linked loci should have been quantified and classified based on escape status; sense control should also be quantified, and biological replicates should be shown separately. 

Please see above response.

Additionally, in the revised manuscript, we have examined the Irreproducible Discovery Rate (IDR) to validate the reproducibility of peaks between the two replicates in the revised version, and we included a representative example from female WT ES cells at day 4 (revised Figure S4A). The results showed a strong correlation between the replicates, with an IDR threshold of 0.05 (red point > 0.05). As described in the Methods section, to ensure reliable and robust peak identification, we performed peak calling (MACS2) separately on each replicate, and then used bedtools intersect to identify peaks that overlapped between the two replicates. This stringent process, including strict q-value settings in MACS2, ensures the reliability and reproducibility of the peaks presented in this study.

Secondly, and most importantly, Figure 1 does not convincingly show specific Xist autosomal binding. Panel A quantification is on extremely variable y-scales and actually shows that Xist is recruited globally to nearly all autosomal genes, likely indicating an unspecific signal. Again, the sense and 0h controls should have been quantified along with biological replicates. 

Figure 1 shows heatmaps and corresponding metagenes for d0, d4, d7, and d14 female ES cells. Two biological replicates are analyzed. In our revised manuscript, we have used Pearson and Spearman correlation coefficients to measure the strength and direction of a relationship between two biological replicates and shown that the two replicates have high reproducibility (new Figure S1A). On d0, the Xist coverage on autosomes and X chromosome is low, but there is a clear increase on d4, d7, and d14, particularly at the TSS of autosomal genes, as shown by the metagene plots on in Figure 1A-B and the CHART density maps in new Figure 1E-F. We also show relative depletion of Xist signals in the male and sense negative controls.

Upon inspecting genome browser tracks of all regions reported in the manuscript (Rbm14, Srp9, Brf1, Cand2, Thra, Kmt2c, Kmt2e, Stau2, and Bcl7b), the signal is unspecific on all sites with the possible exception of Kmt2e. On all other loci, there is either a strong signal in the 0h ESC controls or more signal in some of the sense controls. This implies that peak calling is picking up false positive regions. How many peaks would have been picked up if the sense or the 0h controls were used for peak calling? It is likely that there would be a lot since there are also possible "peaks" (e.g., Fzd9) in control tracks. 

The analysis cannot be performed by visual inspection. A statistical analysis must be performed to call signal above noise. This is why we performed peak-calling on two biological replicates and identified overlapping peaks using bedtools intersect to improve reliability. Significant peaks are noted as black bars under each track. As mentioned above, for our analysis, we focused on the top 100 peaks based on peak scores to ensure robustness. Xist has significantly higher signal compared to the sense probe in the Xist-autosomal peak regions (revised Figure 1E-F). Additionally, we conducted peak calling on undifferentiated ES cells (d0) and detected a significantly higher number of peaks (~600) compared to the differentiated states (d4 or d7) (~100).

Single-cell sequencing studies have shown that about 2% of undifferentiated mESCs express detectable Xist (Pacini et al., Nat Commun, 2021). The Xist peaks in “day 0” cells may be due to the differentiating population.

Further inspection of the data was not possible as the authors did not provide access to the raw fastq files. When inspecting results from past published experiments {Engreitz, 2013 #1839} reported regions were not bound by Xist. 

On the contrary, we deposited the raw data files to GEO prior to the submission of the paper and included the reviewer link to access them. As of August 24, 2024, GEO publicly released these files, allowing for full inspection of the data. 

Regarding the Engreitz publication, it is not recommended to compare our current study to their analysis for the crucial reason that the Engreitz study was not conducted under physiological conditions. The authors overexpressed the Xist gene in male ES cells. Because Xist RNA can silence genes in male cells as well, this ectopic overexpression normally leads to cell death — thus forcing examination of effects in a narrow time window before Xist can fully spread and act across the genome. Comparing our experiments (endogenous Xist expression in female ES cells) to the ectopic overexpression in male ES cells of Engreitz et al. should therefore not be undertaken.

Thirdly, contrary to the authors' claim, deleting the B repeat does not lead to a loss of autosomal signal. Indeed, comparing Fig1A and Fig2B side by side clearly shows no difference in the autosomal signal, likely because the autosomal signal is CHART background. Properly quantifying the signal with separate replicates as well as the sense and 0h controls is vital. Overall current data together with published results indicate that CHART peak calling on autosomes is due to technical noise or artefacts.

In our revised manuscript, we have included the quantitative results as mentioned above in the main and supplementary figure (new Figure 1E-F, Figure 2E-F, and S3A). The data clearly show an enrichment in the Xist CHART samples in differentiating female ES cells.

We believe the reviewer may be comparing the original Figure 1A and Figure 2A (not Figure 2B). As mentioned above, the analysis cannot be performed by visual inspection. Please see new Figure 2E and 2F. From these data, it should be clear that deleting RepB causes a decrease in Xist targeting to autosomal loci.

(2) The RNA-seq analysis is also flawed and precludes strong statements. Firstly, the analysis frequently lacks statistical analysis (Fig3B, FigS2B-C) and is often based on visualizations (Fig 3D-G) without quantifications. Day 4 B-repeat deletion does not lead to a significant change in the expression of genes close to Xist signal (Fig3H, d14 does not fully show). 

Please see new revised Figure 3B and Figures S2B-C (now revised as Figures S6A and S6B). 

Secondly, for all transcriptional analysis, it is important to show autosomal non-target genes, which is not always done. 

In the revised manuscript, we included non-target genes for each analysis (new Figure 4E-F, 5D and 5F, 7C and 7E, S7F, S8).

Indeed, both males and B repeat deletion will lead to transcriptional changes on autosomes as a secondary effect from different X inactivation status. The control set, if used, is inappropriate as it compares one randomly selected set of ~100 genes. This introduces sampling error and compares different classes of genes. Since Xist signal targets more active genes, it is important to always compare autosomal target genes to all other autosomal genes with similar basal expression patterns.

Please see new Figure S8. We included 100 randomly selected non-target sites on autosomes for this comparative analysis. For consistency, we applied the same flanking regions (10 kb) in the analysis of both target and non-target genes. We believe that this selection method for nontargets is appropriate for two reasons: first, it allows us to control for Xist binding and non-binding; second, it ensures a similar number of genes in both groups, providing a robust foundation for statistical analysis. 

(3) The ChIP-seq analysis also has some problems. The authors claim that there is no positive correlation between genes close to Xist autosomal binding (10kb) compared to those 50kb away (Fig 3C, S2D); however, this analysis is based entirely on metagene visualization. Signal within the Xist binding sites should be quantified (not genes close by) and compared to other types of genomic loci and promoters. Focusing on the 50kb group only as controls is misleading.

We believe the reviewer may have misunderstood our conclusions. As stated in the paper, we observed lower coverage of the histone marks H3K27me3 and H2AK119ub, associated with PRC2 and PRC1, respectively. Our conclusions regarding PRC1/2 support the RNA-seq results, indicating that Xist tends to bind to actively expressed genes. In other words, these genes exhibit lower levels of PRC-mediated silencing signals. This observation underscores the relationship between Xist binding and gene activity, highlighting that Xist preferentially associates with regions that are less subject to silencing by polycomb repressive complexes.

Secondly, the authors only look at PRC mark signal upon differentiation; what about the 0h timepoint, i.e., is there pre-marking? 

Day 0 is not an appropriate timepoint for this analysis because Xist is not yet induced. There is also a small fraction of cells (<5%) that spontaneously differentiate and start to undergo XCI. Because of these reasons, the day 0 timepoint is considered somewhat heterogeneous and it would be difficult to make conclusions regarding Xist peaks in these samples.

Most worryingly, the data analysis is not consistent between figures (see Fig3C vs 5H-I). In Fig5, the group of Xist targets was chosen as those within 100kb of Xist binding, which would encompass all the control regions from Fig3C. In this analysis, the authors report that there is Xist-dependent H3K27me3 deposition, and in fact, here the Xist autosomal targets have more of it than the controls. Overall, all of this analysis is misleading, and clear conclusions cannot be made.

We believe that the reviewer may have also misunderstood the analysis in Figure 5. Figure 5 shows the effect of the Xist inhibitor, X1, on H3K27me3 and gene expression. X1 blocks reduces PRC2 targeting and gene silencing — consistent with X1’s effect on RepA as published in Aguilar et al. 2022. 

All in all, because the fundamental observation is not robust (see point 1), all subsequent analyses are also affected. There are also multiple other inconsistencies within the analysis; however, they have not been included here for brevity.

We again respectfully disagree with Rev1 but thank the reviewer for making suggestions that helped to strengthen our manuscript.  We believe that the revised manuscript with new analyses is improved in part because of the reviewer’s critical comments.

Reviewer #2 (Public review):

Summary:

To follow-up on recent reports of Xist-autosome interaction the authors examine female (and male transgenic) mESCs and MEFs by CHARTseq. Upon finding that only 10% of reads map to X, they sought to identify reproducible alternative sites of Xist-binding, and identify ~100 autosomal Xistbinding sites and show a transient impact on expression.

Strengths:

The authors address a topical and interesting question with a series of models including developmental timepoints and utilize unbiased approaches (CHARTseq, RNAseq). For the CHARTseq they have controls of both sense probes and male cells; and indeed do detect considerable background with their controls. The use of deletions emphasizes that intact functional Xist is involved. The use of 'metagene' plots provides a visual summation of genic impact.

Reviewer 2 has made some excellent suggestions. We have revised the manuscript accordingly and are grateful to the reviewer for the recommendations.

Weaknesses:

Overall, the result presentation has many 'sample' gene presentations (in contrast to the stronger 'metagene' summation of all genes). The manuscript often relies on discussion of prior X chromosomal studies, while the data generated would allow assessment of the X within this study to confirm concordance with prior results using the current methodology/cell lines. 

Many of the 'follow-up' analyses are in fact reprocessing and comparison of published datasets. The figure legends are limited, and sample size and/or source of control is not always clear. While similar numbers of autosomal Xist-binding sites were often observed, the presented data did not clarify how many were consistent across time-points/cell types. While there were multiple time points/lines assessed, only 2 replicates were generally done.

We apologize for the deficiencies in the legend.  The revised manuscript has corrected them.

We generated many new datasets with deep sequencing, with at least two biological replicates for each. Such experiments are extremely expensive by nature. Thus, two biological replicates are typically considered acceptable.

Additionally, we performed reanalysis of published datasets to test whether — in the hands of other investigators — cell lines expressing Xist also supported autosomal targeting. Figure 4 is a case in point. Here we examined Tg1 and Tg2, which respond to doxycycline to overexpress Xist from an ectopic site. Transcriptomic analysis showed significant downregulation of autosomal Xist targets, as exemplified by Rbm14 and Bcl7b (new Figure 4C, S9B). In contrast, non-targets of Xist such as Stau1 did not demonstrate significant changes in gene expression (new Figure 4E and 4G). Looking across all autosomal target genes, we observed a significant decrease in mean expression in the Xist overexpressing cell lines (new Figure 4D). The fact that the autosomal changes were also observed in datasets generated by other investigators greatly strengthen our conclusions. 

Aim achievement:

The authors do identify autosomal sites with enrichment of chromatin marks and evidence of silencing. More details regarding sample size and controls (both treatment, and most importantly choice of 'non-targets' - discussed in comments to authors) are required to determine if the results support the conclusions.

Specific scenarios for which I am concerned about the strength of evidence underlying the conclusion:

I found the conclusion "Thus, RepB is required not only for Xist to localize to the X- chromosome but also for its localization to the ~100 autosomal genes " (p5) in constrast to the statement 2 lines prior: "A similar number of Xist peaks across autosomes in ΔRepB cells was observed and the autosomal targets remained similar". Some quantitative statistics would assist in determining impact, both on autosomes and also X; perhaps similar to the quintile analysis done for expression.

We have added the Xist coverage panel for day 4 and 7 in the identified Xist-autosomal peak regions (new Figure 1E-F, Figure 2E-F), as mentioned above. The results clearly demonstrate that the deletion of RepB decreases Xist binding to autosomes. Also, we showed that ΔRepB increased X-linked genes expression in our revised Figure 3D. 

It is stated that there is a significant suppression of X-linked genes with the autosomal transgenes; however, only an example is shown in Figure 4B. To support this statement, a full X chromosomal geneset should be shown in panels F and G, which should also list the number of replicates. 

Please see new Figure 4B.

As these are hybrid cells, perhaps allelic suppression could be monitored? Is Med14 usually subject to X inactivation in the Ctrl cells, and is the expression reduced from both X chromosomes or preferentially the active (or inactive) X chromosome?

If Rev2 is referring to Figure 4, the dataset used in Figure 4 comes from another research group and was previously published (Loda, A. et al. Nat Commun, 2017).

If Rev2 is referring to our ES cells, they are N2 cell lines.  The X chromosomes are fully hybridized (Cas/Mus), but the autosomes are not fully hybridized (Ogawa et al., Science, 2008). Med14 is subject to XCI and is expressed from the Xa, silenced on the Xi. 

The expression change for autosomes after transgene induction is barely significant; and it was not clear what was used as the Ctrl? This is a critical comparator as doxycycline alone can change expression patterns.

We agree that there was a modest change in expression after transgene induction, but it is a significant change. Again, the dataset is from a published study where the authors generated doxycycline-responsive Xist transgenes (see above). The control in this case is Dox-treated wildtype cells. We now clarify these points.

In the discussion there is the statement. "Genetic analysis coupled to transcriptomic analysis showed that Xist down-regulates the target autosomal genes without silencing them. This effect leads to clear sex difference - where female cells express the ~100 or so autosomal genes at a lower level than male cells (Figure 7H)." This sweeping statement fails to include that in MEFs there is no significant expression difference, in transgenics only borderline significance, and at d14 no significant expression difference. The down-regulation overall seems to be transient during development while targeting is ongoing?

Indeed, the Xist effects on autosomes seem to occur during cell differentiation in ES cells. While there is no apparent effect in MEFs, we cannot exclude effects on other somatic cells. Regardless of whether the effects are in early development or throughout life, the sex differences may have life-long effects in mammals. The study conducted in human cells by the Plath lab also concluded that the differences primarily affect stem cells.

Finally, I would have liked to see discussion of the consistency of the identified genes to support the conclusion that the autosomal sites are not merely the results of Xist diffusion.

We address this in the third paragraph of the Discussion. Our main argument is that if autosomal binding were caused by diffusion, then RepB deletion or X1 treatment would have led to increased binding at autosomal sites, as Xist would bind less to the X chromosome. However, as demonstrated in our study, both treatments resulted in reduced Xist binding on both the X chromosome and autosomes. This finding suggests that the binding is specific and reliant on Xist's RepA and RepB domains, rather than being a passive diffusion process.

To examine overlap between the conditions (days of differentiation and WT/RepB cells), we generated Venn Diagrams as now shown in Figure S4E.

The impact of Xist on autosomes is important for consideration of impact of changes in Xist expression with disease (notably cancers). Knowing the targets (if consistent) would enable assessment of such impact.

We thank Rev2 for the very helpful review and for the forward-looking experiments. Indeed, the physiological changes brought on by autosomal targeting will be of future interest.

Reviewer #3 (Public review):

Summary:

Yao et al use CHART to identify chromatin associated with Xist in female mouse ESCs, and, as control, male ESCs at various timepoints of differentiation. Besides binding of Xist to X chromosome regions they found significant binding to autosomes, concentrating mostly on promoter regions of around 100 autosomal genes, as elucidated by MACS. The authors went on to show that the RepB repeat is mostly responsible for these autosomal interactions using a female ESC line in which RepB is deleted. Evidence is provided that Xist interacts with active autosomal genes containing lower coverage of repressive marks H3K27me3 and H2AK119ub and that RepB dependent Xist binding leads to dampening of expression, but not silencing of autosomal genes. These results were confirmed by overexpression studies using transgenic ESCs with doxycycline-inducible Xist as well as via a small molecule inhibitor of Xist (X1), inducing/inhibiting the dampening of autosomal genes, respectively. Finally, using MEFs and Xist mutants RepB or RepE the authors provide evidence that Xist is bound to autosomal genes in cells after the XCI process but appears not to affect gene expression. The data presented appear generally clear and consistent and indicate some differences between human and mouse autosomal regulation by Xist. Thus, these results are timely and should be published.

We thank Rev3 for the positive remarks and great suggestions.  We have amended the manuscript per below. 

Strengths:

Regulation of autosomal gene expression by Xist is a "big deal" as misregulation of this lncRNA causes developmental defects and human disease. Moreover, this finding may explain sexspecific developmental differences between the sexes. The results in this manuscript identify specific mouse autosomal genes bound by Xist and decipher critical Xist regions that mediate this binding and gene dampening. The methods used in this study are appropriate, and the overall data presented appear convincing and are consistent, indicating some differences between human and mouse autosomal regulation by Xist.

Weaknesses:

(1) The figure legends and/or descriptions of data are often very short lacking detail, and this unnecessarily impedes the reading of the manuscript, in particular the figures would benefit not only from more detailed descriptions/explanations of what has been done but also what is shown. 

We have included more detailed descriptions in the figure legends and throughout the manuscript.

This will facilitate the reading and overall comprehension by the reader. One out of many examples: In Fig S1B in the CHART data at d4 and d7 there is not only signal in female WT Xist antisense but also in female sense control. For a reader that is not an expert in XCI it would be helpful to point out in the legend that this signal corresponds to the lncRNA Tsix (I suppose), that is transcribed on the other strand.

We thank the reviewer for this excellent point.  We have amended the Results section accordingly.

(2) Different scales are used in the lower panels of Figures 1A and 2A, which makes it difficult to directly compare signals between the different differentiation stages.

We have included a figure combining all timepoints — d0, d4, d7, and d14 WT female Xist CHART signals  — on the X chromosome and autosomes to support our thesis. Please see new Figure 1B.

(3) In this study some of the findings on mouse cells contrast previously published results in human ESCs: 1) Xist binding occurs preferentially to promoters in mice, not in human. 2) Binding of Xist is mostly detected in polycomb-depleted regions in mice but there is a positive correlation between Xist RNA and PRC2 marks in human ESCs. These differences are surprising but may be very interesting and relevant. While I am aware that this might be a difficult task, it would be helpful to experimentally address this issue in order to distinguish whether species specific and/or methodological differences between the studies are responsible for these differences.

Indeed, our findings in mouse cells contrast with those observed in humans. As discussed in the manuscript, this discrepancy may be attributed to factors such as cell type, differentiation methods, and the Xist pull-down technique employed (our CHART method utilizes a 20 nt oligo library, whereas RAP uses long oligos). We agree that future work should investigate the underlying causes of these differences between mouse and human systems.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

For Figure 2: labelling ∆B on the panel A timeline (e.g. d0-∆B) would make the results clearer for the audience. Panel B makes most sense beside panel E of Figure 1, so combine here and skip in Figure 1?

We have modified Figure 2A and thank Rev2 for this suggestion. As for the embedded tables: since we performed peak calling for WT and ∆B separately, we believe that showing both the peak numbers and their corresponding peak patterns provides a clearer representation of the data.

I agree that at day 7 there appears to be a difference in X; but by day 14 this looks much more minimal - is it just time-shifted rather than altered? Perhaps this could be discussed. Autosomal binding sites show no change in number.

Day 7 exhibits the strongest Xist binding on the X chromosome, consistent with the de novo establishment phase of XCI when Xist is expressed at the highest levels (300 copies/cell during de novo XCI versus ~100 copies/cell during maintenance [Sunwoo et al., 2015 as cited]. Per our RNA-seq analysis here, we also observed highest Xist expression on day 7 and reduced levels on day 14 (Fig. S5A). This expression difference explains the reduced Xist CHART levels on day 14 compared to day 7. 

While the X has previously been examined, it would seem beneficial to conduct the same expression analyses (Figure 3) for the X (perhaps supplemental), as the authors have the data 'in hand'. I feel comparison to X in the main figure for panels A and B would fit, while a similar analysis for the X for panel C could be supplemental, presumably supporting the published data to which this data is currently compared. 

This is a good suggestion. Please find the new data in Figures 2E-F and 3D, which demonstrate that the RepB deletion inhibits Xist binding on the X chromosome, resulting in increased X-linked gene expression, as previously mentioned. Since Xist binds across the X chromosome, we did not perform peak calling as we did for the autosomes. Therefore, applying a similar analysis as in Figures 3A-B may not be appropriate in this case.

Such a direct comparison to X-data from the same study would be important. For panel H: How many replicates (2)? This should be in the legend. What is the change in median expression? Again, a supplemental figure showing impact on X-linked targets would be useful. Do male and female ESCs show an expression difference prior to differentiation (ie d0)? The data underlying this Figure should be in one of the supplementary tables, showing the full statistical tests and average change. The supplementary tables 8-12 list the WT target genes, not expression differences with the deletion. Again, given that the difference appears transient, might the ∆B cells be altered in rate of differentiation?

Panel H (revised Figure 3G) includes two replicates, and this has been added to the legends. We have provided a supplementary figure demonstrating that RepB increases the expression levels of X-linked genes on days 4, 7, and 14 (revised Figure 3D). Male and female ESCs show differences in the expression of X-linked genes, as both X chromosomes are active in females at this stage prior to differentiation (revised Figure S5C). 

A supplementary table with statistical tests and average change information has been included in our revised version (Table S11).

On the other hand, these Xist-autosomal target genes displayed no significant differences between WT male, female, or ∆B female cells on day 0 — prior to onset of XCI and Xist expression. Please see new Figure 3H. 

As for whether ∆B cells are altered in their rate of differentiation, the analysis by Colognori et al. 2019 indicates that ∆B cells differentiate similarly to WT cells. (In Figure 6 of Colognori et al. 2019, autosomal genes expressed similarly in WT and ∆B cells, whereas XCI is affected only in ∆B cells)

We have also modified the legends for our supplementary tables.

Why were the transgene lines examined upon neuronal differentiation rather than the same approach as in Figures 1-3? I would have thought neuronal differentiation might be more similar to d14, where limited changes remain? Could the authors clarify and discuss?

We apologize for the confusion. The Tg lines in Figure 4 came from a previously published study. We performed reanalysis of published datasets because we wanted to test whether — in the hands of other investigators — cell lines expressing Xist also supported autosomal targeting. Here we examined Tg1 and Tg2, which respond to doxycycline to overexpress Xist from an ectopic site. Transcriptomic analysis showed significant downregulation of autosomal Xist targets, as exemplified by Bcl7b and Rbm14 (Figure 4C and S9B). In contrast, non-targets of Xist such as Stau1 did not demonstrate significant changes in gene expression (Figure 4E and 4F). Looking across all autosomal target genes, we observed a significant decrease in mean expression in the Xist overexpressing cell lines (Figure 4D). The fact that the autosomal changes were also observed in datasets generated by other investigators greatly strengthen our conclusions. We have clarified this in the Results section.

Figure 5 - the legend should specify the number of replicates and clarify the blue/green (intuitive, but not specified). Are the 'target' / 'non-target' genes from d4 Chart (but the RNA from d5)? How are 'non-targets' defined - do they match the 'targets' in certain criteria (expression level, chromatin features, GC content)? Do they change per differentiation protocol?

We have modified the legends to clarify that the 'target' and 'non-target' genes are derived from the day 4 CHART-seq data, while the RNA data is from day 5, as that study sequenced day 5 and not day 4. Non-targets were randomly chosen based on (i) the absence of Xist binding and (ii) similar expression levels. Please see revised Figure S8.

It would be helpful to compare Xist expression levels across the various models, and the MEF model could be better described - are they polyploid as often happens?

We have included the Xist expression levels of ES cells and MEF cells in the revised version (revised Figure S5A, 6D). The transformed MEFs are indeed tetraploid, as is typical.

For 6A to be informative, one needs to know % mapping to X in ES timeline, which is in supplemental, so perhaps 6A should also be supplemental?

We have moved 6A to the supplemental figure.

It is odd that ∆B seems to have had more impact in MEFs, and I would like more discussion - but I also think I am missing something: "We observed that Xist signals were more substantially reduced on both the Xi and autosomal regions in ΔRepE MEFs compared to ΔRepB cells", yet in lower panel 6 G it looks like ∆B is LOWER than ∆E? Am I misinterpreting?

We apologize for the confusing writing.  The revised text now reads:  “To investigate, we utilized a deletion of Xist’s Repeat E (∆RepE), which was previously demonstrated to severely abrogate localization of Xist to the Xi 41,42. We reasoned that the severe loss of Xist binding might unmask a transcriptomic difference. As expected, we observed that Xist signals were somewhat more reduced on the Xi in ΔRepE MEFs compared to ΔRepB cells (Figure 6E-6F). Despite this reduction, peak coverages in autosomal target genes did not increase in ΔRepE MEFs (Figure 6E-6F). However, there was an overall decrease in the number of significant autosomal peaks in ∆RepE MEFs relative to WT cells (Figure 6A). Regardless, we observed no significant transcriptomic differences in ∆RepE MEFs relative to WT MEFs (Figure 7A-7E). Additionally, further examination of RNA sequencing data from male and female MEF cells in two published studies 43,44 corroborated that the expression levels of these autosomal Xist targets did not exhibit significant changes (Figure 7F and 7G). Altogether, the analysis in MEFs demonstrates that Xist continues to bind autosomal genes in post-XCI somatic cells. However, autosomal binding of Xist in post-XCI cells does not overtly impact expression of the associated autosomal genes. Nonetheless, we cannot exclude more subtle changes that do not meet the significance cut-off.”

Overall, I would like to see how consistent these autosomal peaks are - I shudder to suggest Venn diagrams, but something to show whether there are day/lineage specific peaks and/or ∆repeat B/E resistant peaks. 

We now present Venn diagrams comparing MEF, ES_d4, and ES_d7, showing approximately 50% overlap between MEF and ES cells (revised Figure S10B). This may be expected, as each timepoint is a different developmental stage of XCI, with expected gene expression differences.

Very minor comments:

It would be easier if the supplemental tables were tabs in 1 file!

We will defer to the editor on how best to format the supplemental tables.

Similar to the text, could gene names be included in the supplemental?

We have provided gene names in the supplemental files.

Figure 3 legend: should 'representing' be representative?

We have modified it.

"Xist patterns identified in human cells" p 5; it is challenging to follow human versus mouse, so specify or ensure correct use of XIST/Xist Indeed, we edited the manuscript accordingly.

Gene names should be italicized.

We have italicized gene names in our manuscript.

Ref. 38 lacks details (...).

We have updated the reference.

Peak-like characters - perhaps characteristics? P8

We have modified this.

Reviewer #3 (Recommendations for the authors):

On page 6, the 6th sentence in the first paragraph needs correction. "Consistent with Xist's behavior on the X chromosome."

We have modified the sentence. Thank you.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The study by Longhurst et al. investigates the mechanisms of chemoresistance and chemosensitivity towards three compounds that inhibit cell cycle progression: camptothecin, colchicine, and palbociclib. Genome-wide genetic screens were conducted using the HAP1 Cas9 cell line, revealing compound-specific and shared pathways of resistance and sensitivity. The researchers then focused on novel mechanisms that confer resistance to palbociclib, identifying PRC2.1. Genetic and pharmacological disruption of PRC2.1 function, but not related PRC2.2, leads to resistance to palbociclib. The researchers then show that disruption of PRC2.1 function (for example, by MTF2 deletion), results in locus-specific changes in H3K27 methylation and increases in D-type cyclin expression. It is suggested that increased expression of D-type cyclins results in palbociclib resistance.

Strengths:

The results of this study are interesting and contribute insights into the molecular mechanisms of CDK4/6 inhibitors. Importantly, while CDK4/6 inhibitors are effective in the clinic, tumour recurrence is very high due to acquired resistance.

Weaknesses:

A key resistance mechanism is Rb loss, so it is important to understand if resistance conferred by PRC2.1 loss is mediated by Rb, and whether restoration of PRC2.1 function in Rb-deplete cells results in renewed palbociclib sensitivity. It is also important to understand the clinical implications of the results presented. The inclusion of these data would significantly improve the paper. However, besides some presentation issues and typos as described below, it is my opinion that the results are robust and of broad interest.

Major questions:

(1) Is the resistance to CDK4/6 inhibition conferred by mutation of MTF2 mediated by Rb?

(2) Are mutations in PRC2.1 found in genetic analyses of tumour samples in patients with acquired resistance?

We thank the reviewer for their editing and experimental suggestions, and have integrated their responses into our re-submitted manuscript.

We also agree that understanding the role of RB1 in mediating palbociclib resistance to the proposed resistance mechanism is of particular interest. However, as there are three RB proteins expressed in human cells, this is a technically difficult question to probe genetically. Despite this technical challenge, we have provided multiple lines of evidence in our resubmitted manuscript that the resistance to palbociclib observed in our PRC2.1-deficent cells is mediated through the canonical CDK4/6-RB1 pathway. First, disruption of RB1 in HAP1 cells results in palbociclib resistance to a level comparable level to PRC2.1 disruption (Fig. 4E). Second, inactivation of SUZ12 or MTF2 increases the number of cells entering S-phase in palbociclib treatment (Fig. 4G) with no increase in basal rates of apoptosis (Fig. S2D), suggesting that any proliferation advantage observed in PRC2.1-defective cells is due to resistance to  palbociclib-induced cell cycle arrest. Third, we show that over expression of CCND1 and CCND2 is sufficient to drive resistance to palbociclib in wild-type HAP1 cells (Fig. S5F).  And finally, increased levels of CCND1 and CCND2 observed in cells lacking PRC2.1 activity results in higher CDK4/6 activity as measured by RB1 phosphorylation, despite palbociclib blockade (Fig. 6F). All these lines of evidence strongly suggest that MTF2-containing PRC2.1 regulates G1 progression in through the canonical CDK4/6RB1 pathway by repressing CCND1 and CCND2 expression. 

Whether or not MTF2 deletion leads to palbociclib resistance in clinical samples is also of a question of particular interest. Currently, we are unaware of any reports that specifically mention MTF2 deletion as leading to palbociclib resistance, and we were unable to find another example in our own cancer database review. However, we have included references to other examples of MTF2 mutation resulting in chemotherapeutic resistance in our discussion. Additionally, although MTF2 is rarely observed to be mutated in cancers (Ngubo et al. 2023), it is highly differentially expressed and investigating decreased MTF2 transcription in palbociclib resistant tumors, though challenging, might prove fruitful.  However, as mechanisms of palbociclib resistance is an area of active investigation, we speculate that future studies might uncover additional examples of MTF2 mediating resistance to this clinically important chemotherapeutic.  

Reviewer #2 (Public Review):

Summary:

Longhurst et al. assessed cell cycle regulators using a chemogenetic CRISPR-Cas9 screen in haploid human cell line HAP1. Besides known cell cycle regulators they identified the PRC2.1 subcomplex to be specifically involved in G1 progression, given that the absence of members of the complex makes the cells resistant to Palbociclib. They further showed that in HAP1 cells the PRC2.1, but not the PRC2.2 complex is important to repress the cyclins CCND1 and CCND2. This can explain the enhanced resistance to Palbociclib, a CDK4/6Inhibitor, after PRC2.1 deletion.

Strengths:

The initial CRISPR screen is very interesting because it uses three distinct chemicals that disturb the cell cycle at various stages. This screen mostly identified known cell cycle regulators, which demonstrates the validity of the approach. The results can be used as a resource for future research.

The most interesting outcome of the experiment is the finding that knockouts of the PRC2.1 complex make the cell resistant to Palbociclib. In a further experiment, the authors focused on MTF2 and JARID2 as the main components of PRC2.1 and PRC2.2, respectively. Via extensive analyses, including genome-wide experiments, they confirmed that MTF2 is particularly important to repress the cyclins CCND1 and CCND2. The absence of MTF2 therefore leads to increased expression of these genes, sufficient to make the cell resistant to palociclib. This result will likely be of wide interest to the community.

Weaknesses:

The main weakness of the manuscript is that the experiments were performed in only one cell line. To draw more general conclusions, it would be essential to confirm some of the results in other cell lines.

In addition, some of the findings, such as the results from the CRISPR screen as well as the stronger impact of the MTF2 KO on H3K27me3 and gene expression (compared to JARID2 KO), are not unexpected, given that similar results were already obtained before by other labs.

We thank the reviewer for their suggestions and we believe that we have addressed their main concern about the generality of the MTF2 regulation of D-type cyclin expression in our resubmitted manuscript. We have now shown through shRNA knockdown that MTF2 represses CCND1 in two additional cell lines, the breast cancer MDA-MB-231 and immortalized monkey COS7 cell line (Fig. 6E). However, it is important to note that MTF2 did not control CCND1 expression in every cell line tested (Fig. 6D), underscoring the context-dependent nature of this regulation. Future studies will illuminate what cell or tumor types in which this regulation is observed.

Additionally, while MTF2 has previously been shown to exert a greater effect on H3K27me3 levels in some circumstances (Loh et al. 2021, Rothberg et al. 2018), a number of notable reports in ES cell lines have concluded that PRC2 localization and H3K27me3 at the majority of genomic sites are dependent on both PRC2.1 and PRC2.2 activity (Healy et al. 2019, Højfeldt et al. 2019, Perino et al. 2020, Oksuz et al. 2018). Therefore, we think it is important to highlight the greater dependence on MTF2 for promoter proximal H3K27me3 levels in our transformed cell line context.  

Reviewer #3 (Public Review):

This study begins with a chemogenetic screen to discover previously unrecognized regulators of the cell cycle. Using a CRISPR-Cas9 library in HAP1 cells and an assay that scores cell fitness, the authors identify genes that sensitize or desensitize cells to the presence of palbociclib, colchicine, and camptothecin. These three drugs inhibit proliferation through different mechanisms, and with each treatment, expected and unexpected pathways were found to affect drug sensitivity. The authors focus the rest of the experiments and analysis on the polycomb complex PRC2, as the deletion of several of its subunits in the screen conferred palbociclib resistance. The authors find that PRC2, specifically a complex dependent on the MTF2 subunit, methylates histone 3 lysine 27 (H3K27) in promoters of genes associated with various processes including cell-cycle control. Further experiments demonstrate that Cyclin D expression increases upon loss of PRC2 subunits, providing a potential mechanism for palbociclib resistance.

The strengths of the paper are the design and execution of the chemogenetic screen, which provides a wealth of potentially useful information. The data convincingly demonstrate in the HAP1 cell line that the MTF2-PRC2 complex sustains the effects of palbociclib (Figure 4), methylates H3K27 in CpG-rich promoters (Figure 5), and represses Cyclin D expression (Figure 6). These results could be of great interest to those studying cell-cycle control, resistance mechanisms to therapeutic cell-cycle inhibitors, and chromatin regulation and gene expression.

There are several weaknesses that limit the overall quality and potential impact of the study. First, none of the results from the colchicine and camptothecin screens (Figures 1 and 2) are experimentally validated, which lessens the rigor of those data and conclusions. Second, all experiments validating and further exploring results from the palbociclib screen are restricted to the Hap1 cell line, so the reproducibility and generality of the results are not established. While it is reasonable to perform the initial screen to generate hypotheses in the Hap1 line, other cancer and non-transformed lines should be used to test further the validity of conclusions from data in Figures 4-6. Third, conclusions drawn from data in Figures 3D and 4D are not fully supported by the experimental design or results. Finally, there have been other similar chemogenetic screens performed with palbociclib, most notably the study described by Chaikovsky et al. (PMID: 33854239). Results here should be compared and contrasted to other similar studies.

We thank the reviewer for their suggestions regarding our manuscript. While the genes recovered as mediating cellular responses to camptothecin and colchicine was never confirmed following our chemogenetic screens, we felt our primary findings were in the area of palbociclib resistance and decided focus our follow-up investigations on genes. We included the results camptothecin and colchicine chemogenetic screens as confirmation of the specificity of PRC2 mutation resulting in resistance to palbociclib (Fig. 4C) and for others in the community to use as a resource for future investigations. We have also clarified our results for Figure 3D and 4D in our revised manuscript, as well as included additional plots of these results (Fig. S1DS1F). And, with our resubmitted manuscript, we believe we have addressed their concern of the generality of our results by demonstrating our primary finding that MTF2 regulates D-type cyclins in additional cell lines other than HAP1. We feel these results indicate that while not “general”, there are additional cellular contexts that our main result holds true. In line with this, and to address how our chemogenetic screens fits into the landscape of previous studies, including Chaikosvsky et al., we have included the following lines to our discussion:  “Additionally, other chemogenetic screens utilizing palbociclib and have not identified that inactivation of PRC2 components as either enhancing or reducing palbociclib-induced proliferation defects, suggesting that PRC2 mutation is neutral in the cell lines studied. These observations not only underscore the context-dependent ramifications of mutation of these PRC2 complex members, but also may help inform the context in which CDK4/6 inhibitors are most efficacious.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) "We found that only thirteen and twenty genes resulted in sensitivity or resistance, respectively, in every conditions tested and were deemed non-specific and excluded from any further analysis (see Table S2)." It's unclear to me why these genes were deemed 'nonspecific'. Are these genes functionally important for the general exclusion of xenobiotic molecules?

By this, we simply meant that these effects were not specific to one condition. Such genes could affect drug half-life or a general stress response, but are less likely to have functions directly tied to the pathway targeted by a drug than are genes whose loss affects only one condition.  

(2) "Given that increased CCND1 levels is sufficient to drive increased CDK4/6 kinase activity, upregulation of these D-type cyclins is likely to be a significant contributor to the palbociclib resistance in MTF2∆ cells." It's unclear to me what is the basis for this statement. This is only true if there is free CDK4/6. If CDK4/6 is already fully occupied by D-type cyclins, then increased CCND1 levels would not be expected to have an effect. 

While we anticipated that increased levels of CCND1 would result in more CDK4/6-Dtype association, we now demonstrate in the new Figure S5F that there is more CCND1 in complex with CDK6 in both SUZ12∆ and MTF2∆ cell lines. Furthermore, we able to show in Figure S5G that overexpression of D-type cyclins results in resistant to palbociclib-induced proliferation defects in HAP1 cells.

(3) The description of the results is very confusing in places, especially regarding "resistance" versus "sensitivity" genes. For example: "CCNE1, CDK6, CDK2, CCND2 and CCND1, all of which are integral to promoting the G1/S phase transition, ranked as the 2nd, 24th, 27th, 29th and 46th most important genes for palbociclib resistance, respectively (Figures 1F and 1G). CCND1 and CCND2 bind either CDK4 or CDK6, the molecular targets of palbociclib, whereas CDK2 and CCNE1 form a related CDK kinase that promotes the G1/S transition.

Similarly, cells with sgRNAs targeting RB1, whose phosphorylation by CDK4/6 is a critical step in G1 progression, displayed substantial resistance to palbociclib." My reading of this paragraph suggests that disruption of the CDK6 locus is associated with palbociclib resistance - surely this is a typo and instead should have been sensitivity? Please explain.

We thank the reviewer for pointing this out and have corrected this typo  

(4) Sensitivity to palbociclib was enhanced in cells expressing sgRNAs targeting H4 acetylation, positive regulators of Pol II transcription, and regulators of the DNA Damage Response pathway (Figures 3A and 3B), although this sensitivity was much weaker than that seen with DNA damaging agents. This observation is consistent with long-term treatment with palbociclib inducing DNA damage, as has been suggested by a number of recent publications 65,66." This is also consistent with recent work on Cdk7 inhibitors (Wilson et al. Mol Cell 2023), as Cdk7 inhibition is expected to affect both CDK1/2/4/6 activities and Pol II transcription.

We thank the reviewer for bringing this observation to our attention and we have added this citation to this passage in our manuscript.

(5) Figure 3D - would it not make sense to plot the data such that palbo concentration is on the x-axis? It is also difficult to interpret since the data are normalized to starting "% proliferation" at the indicated palbo treatment, when it is likely that % proliferation changes significantly with palbo concentration. Indeed, this is the graphing format used for a later figure (Figure 4D). The data with rotenone suggests palbo antagonizes rotenone-mediated reduction in proliferation. But it's unclear to me whether the graph shows the converse - that rotenone treatment modulates palbo-induced cell cycle arrest.

This reviewer is correct about the fact that increasing doses of palbociclib in the absence of oxidative phosphorylation do indeed have an effect on proliferation. However, it is helpful to normalize proliferation values to each initial dose of palbociclib and then compare this to the different oxidative phosphorylation inhibitors treatment combinations. To illustrate that the oxidative phosphorylation inhibitors do indeed antagonize palbociclib-induced proliferation defects, we have now included the data graphed as each oxidative phosphorylation inhibitor vs palbociclib as Supplemental Figures S1D-S1F.

• The highest concentration of GSK126 tested (5µM) does not appear to confer resistance, but perhaps this is due to off-target effects or cytotoxicity?

We agree with the reviewer that at the highest doses of dose of GSK126, low doses of palbociclib do not confer resistance to palbociclib. However, higher doses do appear to have this effect. We have included a statement in our results section to address this reviewer’s observations. 

• Disruption of Emi1 leads to resistance (Figure 1F, FZR1), yet overexpression induces resistance (Mouery et al. bioRxiv 2023). Explain.

We do not understand why EMI1 responds in this way, and therefore we cannot comment on this in the text. 

Typos/stylistic comments:

• Typo "However, the net result of these opposing effects on cell cycle progression, and the contribution of the individual subcomplexes to this regulation, rained unclear."

We thank the reviewer for pointing this out, and we have corrected it.  

• Use of the word "growth" - I think the authors should be more precise. Is "proliferation" meant here?

We thank the reviewer for pointing this out, and we have corrected it.

• n Figure 4G, two of the panels have 8.42%. Is this correct, or may it be a copy/paste error?

This was an error, but is no longer relevant as we have reconducted and reanalyzed this experiment.

Reviewer #2 (Recommendations For The Authors):

Major Points

(1) Some of the conclusions should be confirmed in additional cell lines. I would suggest testing the resistance to Palbociclib in several additional cell lines, where MTF2 and JARID2 are deleted. If the conclusion can be generalized, one would expect that the differential role of MTF2 versus JARID2 can be confirmed in more cell lines.

While the PRC2.1-dependent repression of D-type cyclins does not appear to be general, we have now demonstrated in Figures 5SE and 6F that there are multiple different cellular contexts in which our observations are consistent. Specifically, we demonstrate that GSK126 causes upregulation of CCND1 in both immortalized nontumor cells (COS7 cells) and in the breast cancer cell line MDA-MB-231. Moreover, in both cases we showed that this effect is PRC2.1-dependent, as shRNA knockdown of MTF2 increases expression of CCND1.

(2) In addition, it may be attractive to make use of publicly available RNA-seq data of MTF2 and JARID2 knockout/down cells, to investigate the generality of the finding that PRC2.1 regulates CCND1 and CCND2.

While it would be useful to address this issue, Figure S5E demonstrates that the repression of D-type cyclin expression by PRC2.1 is context dependent. Furthermore, prior to identifying the lines shown in Figure 6F and 5SE, we were not aware of which lines to focus our investigations on. However, we have now demonstrated a few cellular contexts in which either chemical inhibition of PRC2 or knockdown of MTF2 results in de-repression of CCND1 expression.

(3) At a bare minimum the authors should strongly discuss the limitations of the study, and tone down the conclusions.

We would agree with this based upon the data in the original submitted manuscript, however, now that we have shown that this effect is more general, this is less critical. That said, we do not see this effect in all cell lines, and we have made this apparent in the final version of the manuscript.

Minor point

(1) In my view, Figures 1-3 should be shortened to the most essential points, and some data/figures should be moved to the supplementary figures. Especially the STING genenetwork graphs are in my view not particularly meaningful.

While we understand the opinion of this reviewer, we feel that these data will be of significant interest to some readers.  

(2) Figure 6E and 6F/G appear to be largely redundant. This can perhaps be made more concise.

This has been addressed in the new version of Figure 6

(3) Figure 5D should be enlarged. 

We thank the reviewer for this suggestion and have enlarged the image.

Reviewer #3 (Recommendations For The Authors):

The manuscript could be edited to improve clarity. In several places, the scientific logic motivating an experiment is confusing, and there are several hypotheses and conclusions that seem opposite from what the data are suggesting. Some aspects of the figures were also unclear. Specific examples include the following:

(1) Last sentence of abstract : "Our results demonstrate a role for PRC2.1, but not PRC2.2, in promoting G1 progression." Data show that knockout of PRC2.1 components promotes G1 progression through upregulation of CycD, so the conclusion here is the opposite.

We thank the reviewer for catching this error. We have now changed this to “in antagonizing G1 progression”.

(2) In the second paragraph of the results, CCNE1, CDK2, etc are described as scoring high for palbociclib resistance, but those genes scored as sensitizing. Also, in that paragraph, it is described that a drug is sensitizing cells to loss of a gene, which seems like incorrect logic. It should be clarified that knock-out of a gene either sensitizes or desensitizes cells to the drug.

We thank the reviewer for catching this error. We have now corrected it.  

(3) In the motivation for the experiment in Figure 3D, it is written: "we asked whether chemical inhibition of oxidative phosphorylation could rescue sensitivity to palbociclib". Considering that knock-out of genes that mediate oxidative phosphorylation confer resistance to palbociclib, it is confusing why it was expected that chemical inhibitors would restore sensitivity.

We are sorry if the original wording was confusing. We have now changed this to “combined inhibition of oxidative phosphorylation and CDK4/6 activity mutually rescue the proliferation defect imposed by agents targeting the other process”.  

(4) If the intention of Figure 3D is to test the hypothesis that chemical inhibition of oxidative phosphorylation modulates sensitivity to palbociclib, the clarity of Figure 3D would be improved if data were shown such that palbociclib concentration is on the x-axis and the different curves are different drug concentrations.

It appears that there is some mutual suppression, which inhibition of each process rescues cells partly from inhibition of the other. In fact, with these drugs the stronger of the two is seen as the rescue of mitochondrial poisons by palbociclib. We have now discussed this in the text.  

(5) The authors should check the units on the x-axis in Figure 4D, should they be log[uM Palbo] or log [nM Palbo]?

We thank the reviewer for catching this error. We have now corrected it

(6) It should be clarified which data are summarized in the graph to the right in Figure 4G, are these experiments with palbociclib?

This is currently included in the figure legends.

(7) The text suggests that the control CCNE1 knockout is shown in Figure 4E, but those data are missing.

This has been corrected in Figure 4E.

Several conclusions are not well supported by the data and should be revised or more data and analysis should be added.

(1) The titular conclusion that the "PRC2.1 Subcomplex Opposes G1 Progression through Regulation of CCND1 and CCND2" has only been demonstrated in the context of a Cdk4/6 inhibitor in HAP1 cells. There is little evidence supporting this claim that is broadly applicable. For example, data in Figure 4G show small and not demonstrable significant differences in G1 and S phase populations in the mock experiments. Also, experiments in other cells are needed to support the rigor and generality of the conclusion.

Our chemogenetic screen and competitive proliferation assay data in Figure 4A, 4C and 4E support the conclusion that PRC2.1 and PRC2.2 play opposing roles in G1 progression. Furthermore, we have repeated the initial BrdU incorporation experiments shown in Figure 4G and have been able to demonstrate that JARID2∆ cells do indeed display a significant decrease of cells entering into S-phase when treated with palbociclib. Most importantly, in the Figures 6D and 6E we show additional cell lines where this is the case.  Therefore, we feel that this title is valid in the current version of the manuscript, where we have shown it to be the case in multiple tumor-derived human cell lines as well as immortalized non-human primate cells.  

(2) It is unclear how the data in Figure 3D support the conclusion that the administered inhibitors of oxidative phosphorylation influence response to palbociclib.

As noted in the response to point 4, we have now discussed this mutual rescue more thoroughly in the text.  

(3) In Figure 4D, the IC50 values should be calculated and statistical significance based on biological replicates should be determined. Also, the conclusion that "increasing doses of GSK126 withstood palbociclib-induced growth suppression" is overstated, as ultimately all drug conditions succumb to palbocilib suppression of proliferation, although there may be differences in sensitivity.

We have now  included a statical analysis of each data point in Figure 4D.  

Editorial comments:

(1) The title does not seem to optimally capture the content of the paper. Please consider changing it, e.g. focusing on palbociclib resistance. 

While we used this particular drug to make the original observation, we feel it is more general to discuss the underlying biology (cyclin gene control) than the pharmacological methodology. Moreover, we have now extended our findings about the regulation of D-type cyclins by PRC2.1 to several cell lines, derived from both cancers and primary cells, re-enforcing the fact that this effect is observed more broadly.   

(2) Please indicate the biological system (haploid human HAP1 cells) in either title or abstract.

The abstract now indicates that we have observed this in CML, breast cancer and immortalized primary cells.

Author response:

Reviewer #1 (Public review):

Summary:

The authors aim to investigate the relationship between low estrogen levels, postmenopausal hypertension, and the potential role of the molecule L-AABA as a biomarker for hypertension. By employing metabolomic analysis and various statistical methods, the study seeks to understand how estrogen deficiency affects blood pressure and identify key metabolites involved in this process, with a particular focus on L-AABA.

Strengths:

The study addresses a relevant and understudied area: the role of estrogen and metabolites in postmenopausal hypertension. It presents a novel hypothesis that L-AABA may serve as a protective factor against hypertension, which could have significant clinical implications if proven.

We appreciate the acknowledgment of our study’s focus on an important and understudied area. Our hypothesis regarding L-AABA’s role as a possible protective factor against hypertension indeed holds promise for advancing clinical implications.

Weaknesses:

The evidence linking L-AABA to hypertension is largely correlative, lacking experimental validation or mechanistic proof. Key limitations, such as the inadequacy of the ovariectomy model in replicating human menopause, are acknowledged but not addressed with alternative approaches. In summary, while the study offers an intriguing hypothesis, its conclusions are premature and require further experimental validation and human data to substantiate the claims.

We recognize the limitations regarding the correlative nature of our findings and the inadequacy of the OVX model in replicating human menopause. Future research will prioritize experimental validation and incorporate human studies to solidify our conclusions.

Reviewer #2 (Public review):

Summary:

In this manuscript, Dr. Yao Li et al. documented the metabolomic profile of the aorta from OVX rats and that from OVX plus E2. These conditions mimic post-menopause hypertension and hormonal replacement therapy.

Strengths:

The authors state that this is probably the first study to examine the metabolic changes in the aorta of post-menopause hypertension.

As pointed out by the reviewer, our study may be the first to investigate changes in aortic metabolism in postmenopausal hypertension. As an exploratory study, our goal is to depict the overall characteristics and explore possible research directions.

Weaknesses:

There are several weaknesses, and a few of them are quite serious.

(1) The aorta is not a resistant artery and has little to do with hypertension. The authors should have used resistant arteries for this study. The expression of several adrenergic receptors and cholinergic receptors in the aorta and resistant arteries are different. It is unknown whether the aorta metabolomic profile has any relevance to BP and whether they are similar to that of the resistant arteries. I understand the logistics issue of obtaining enough tissues from resistant arteries. At least, once some leads are discovered in the aorta, the authors should validate it in resistant arteries. This should be feasible.

We acknowledge the limitation of using the aorta and will aim to include studies on resistant arteries to validate our metabolomic findings.

(2) The aorta and all the arteries have three layers. It is critically important to know whether the metabolic changes occur in the intima or in the media, while the adventitia probably has little to do with vasoconstriction and hypertension. If the authors want to use the aorta to conduct the preliminary study, they should completely remove the adventitia and then use samples with and without their endothelium stripped and then assess their metabolomic profiles. After the leads are obtained from this preliminary profiling, they should be validated in endothelium and smooth muscles of the resistant artery. The current experiments are not appropriately designed.

Future studies will involve detailed profiling of specific arterial layers, focusing on the intima and media to enhance the relevance of our findings related to hypertension.

(3) The tail-cuff BP measurement is a technique of the last century. The current gold standard of BP measurement is by telemetry. The tail-cuff method is particularly problematic in this study because the 1-2 h restraining of the rats for more than 10 times BP measurement will cause significant stress in the animal, and their stress hormone secretion might cause biased metabolomic profiles in the OVX versus shames operated mice. The problem can be totally avoided by using telemetry.

We appreciate the suggestion and will consider telemetry for more accurate blood pressure measurements in future experiments to minimize stress-related bias.

(4) Although the L-AABA showed a high p-value (10^-4) of a decrease in the OVX rats, the fold change is small (2-3 folds). Such a small change should be validated using a different method to be convincing.

We plan to employ additional methods to validate the observed changes in L-AABA levels in the following research, ensuring robustness of our findings.

(5) The authors claim (or hypothesize) that the reduced AABA level in OVX can cause vascular remodeling. This can be easily validated by the histology of the OVX-resistant artery, and they should do that during the revision. The authors should also examine the M1 macrophage function from the OVX mice to validate their claimed link of AABA to M1.

We intend to conduct histological analyses and examine M1 macrophage function in OVX-resistant arteries to validate our hypothesis in the following research.

(6) As mentioned above, the authors need to pinpoint the changes of AABA to target cells, i.e., endothelial cells, SMC, or M1, and then use in vitro or in vivo cell biology approaches to assess whether these cells in the OVX rat indeed have an abnormality in function and, indeed, such functional changes are responsible for the BP phenotype.

Addressing these points, we aim to pinpoint specific cell types affected by AABA variations and conduct in vitro and in vivo studies to examine their physiological impacts in the following research.

(7) The results of the current study can be condensed into 1 or 2 figures that can serve as a base or a starting point for a deeper scientific study.

Thank you for your suggestion. As a omics research, our research approach may differ from traditional mechanism studies.

Summary

The experimental design of this manuscript is inappropriate, and the methods are not up to the current standards. The whole study is descriptive and rudimentary. It lacks validation and mechanism. The data from this manuscript might be of some value and can serve as the first step for more investigation of the mechanism of post-menopause hypertension.

Reviewer #3 (Public review):

Summary:

The decrease in estrogen levels is strongly associated with postmenopausal hypertension. Dr. Yao Li and colleagues aimed to investigate the metabolomic mechanisms of underlying postmenopausal hypertension using OVX and OVX+E2 rat models. They successfully established a correlation between reduced estrogen levels and the development of hypertension in rats. They identified L-alpha-aminobutyric acid (AABA) as a potential marker for postmenopausal hypertension. The research explored the metabolic alterations in aortic tissues and proposed several potential mechanisms contributing to postmenopausal hypertension.

Strengths:

The group performed a comprehensive enrichment analysis and various statistical analyses of the metabolomics data.

As summarized by the reviewer, our current study conducted a comprehensive analysis of metabolomics data. It is also a reliable foundation for further mechanism research.

Weaknesses:

(1) The manuscript is descriptive in nature, although they mentioned their primary objective is to explore the potential mechanisms linking low estrogen levels with postmenopausal hypertension. No mechanism insights have been interrogated in this study, which has been mentioned by the authors in the discussion. The connection between E2, AABA, and macrophage needs to be validated in endothelial cells, vascular smooth muscle cells, and other aortic tissue cells. Without such verification, the manuscript predominantly raises hypotheses only based on metabolomic data.

We have proposed research hypotheses based on detailed omics data. Further research on the mechanisms involving endothelial and vascular smooth muscle cells to validate the pathway connections between E2, AABA, and macrophages is undoubtedly the future direction of this study.

(2) The serum contains three forms of estrogen: Estradiol, Estrone, and Estriol. The authors used the Rat E2 ELISA kit. Ideally, all three forms of estrogen should be measured.

Future assays will aim to measure Estradiol, Estrone, and Estriol to capture a more comprehensive picture of estrogen’s role in postmenopausal hypertension.

Author response:

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

eLife Assessment

This useful study reports on the discovery of an antimicrobial agent that kills Neisseria gonorrhoeae. Sensitivity is attributed to a combination of DedA assisted uptake of oxydifficidin into the cytoplasm and the presence of a oxydifficidin-sensitive RplL ribosomal protein. Due to the narrow scope, the broader antibacterial spectrum remains unclear and therefore the evidence supporting the conclusions is incomplete with key methods and data lacking. This work will be of interest to microbiologists and synthetic biologists.

General comment about narrow scope: The broader antibacterial spectrum of oxydifficidin has been reported previously (S B Zimmerman et al., 1987). The main focus of this study is on its previously unreported potent anti-gonococcal activity and mode of action. While it is true that broad-spectrum antibiotics have historically played a role in effectively controlling a wide range of infections, we and others believe that narrow-spectrum antibiotics have an overlooked importance in addressing bacterial infections. Their advantage lies in their ability to target specific pathogens without markedly disrupting the human microbiota.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Kan et al. report the serendipitous discovery of a Bacillus amyloliquefaciens strain that kills N. gonorrhoeae. They use TnSeq to identify that the anti-gonococcal agent is oxydifficidin and show that it acts at the ribosome and that one of the dedA gene products in N. gonorrhoeae MS11 is important for moving the oxydifficidin across the membrane.

Strengths:

This is an impressive amount of work, moving from a serendipitous observation through TnSeq to characterize the mechanism by which Oxydifficidin works.

Weaknesses:

(1) There are important gaps in the manuscript's methods.

The requested additions to the method describing bacterial sequencing and anti-gonococcal activity screening will be made. However, we do not think the absence of these generic methods reduces the significance of our findings.

(2) The work should evaluate antibiotics relevant to N. gonorrhoeae.

(1) It is not clear to us why reevaluating the activity of well characterized antibiotics against known gonorrhoeae clinical strains would add value to this manuscript. The activity of clinically relevant antibiotics against antibiotic-resistant N. gonorrhoeae clinical isolates is well described in the literature. Our use of antibiotics in this study was intended to aid in the identification of oxydifficidin’s mode of action. This is true for both Tables 1 and 2.

(2) If the reviewer insists, we would be happy to include MIC data for the following clinically relevant antibiotics: ceftriaxone (cephalosporin/beta-lactam), gentamicin (aminoglycoside), azithromycin (macrolide), and ciprofloxacin (fluoroquinolone).

(3) The genetic diversity of dedA and rplL in N. gonorrhoeae is not clear, neither is it clear whether oxydifficidin is active against more relevant strains and species than tested so far.

(1) We thank the reviewer for this suggestion. We aligned the DedA sequence from strain MS11 with DedA proteins from 220 N. gonorrhoeae strains that have high-quality assemblies in NCBI. The result showed that there are no amino acid changes in this protein. Using the same method, we observed several single amino acid changes in RplL. This included changes at A64, G25 and S82 in 4 strains with one change per strain. These sites differ from R76 and K84, where we identified changes that provide resistance to oxydifficidin. Notably, in a similar search of representative Escherichia, Chlamydia, Vibrio, and Pseudomonas NCBI deposited genomes, we did not identify changes in RplL at position R76 or K84.

(2) While the usefulness of screening more clinically relevant antibiotics against clinical isolates as suggested in comment 2 was not clear to us, we agree that screening these strains for oxydifficidin activity would be beneficial. We have ordered Neisseria gonorrhoeae strain AR1280, AR1281 (CDC), and Neisseria meningitidis ATCC 13090. They will be tested when they arrive.

Reviewer #2 (Public Review):

Summary:

Kan et al. present the discovery of oxydifficidin as a potential antimicrobial against N. gonorrhoeae, including multi-drug resistant strains. The authors show the role of DedA flippase-assisted uptake and the specificity of RplL in the mechanism of action for oxydifficidin. This novel mode of action could potentially offer a new therapeutic avenue, providing a critical addition to the limited arsenal of antibiotics effective against gonorrhea.

Strengths:

This study underscores the potential of revisiting natural products for antibiotic discovery of modern-day-concerning pathogens and highlights a new target mechanism that could inform future drug development. Indeed there is a recent growing body of research utilizing AI and predictive computational informatics to revisit potential antimicrobial agents and metabolites from cultured bacterial species. The discovery of oxydifficidin interaction with RplL and its DedA-assisted uptake mechanism opens new research directions in understanding and combating antibiotic-resistant N. gonorrhoeae. Methodologically, the study is rigorous employing various experimental techniques such as genome sequencing, bioassay-guided fractionation, LCMS, NMR, and Tn-mutagenesis.

Weaknesses:

The scope is somewhat narrow, focusing primarily on N. gonorrhoeae. This limits the generalizability of the findings and leaves questions about its broader antibacterial spectrum. Moreover, while the study demonstrates the in vitro effectiveness of oxydifficidin, there is a lack of in vivo validation (i.e., animal models) for assessing pre-clinical potential of oxydifficidin. Potential SNPs within dedA or RplL raise concerns about how quickly resistance could emerge in clinical settings.

(1) Spectrum/narrow scope: The broader antibacterial spectrum of oxydifficidin has been reported previously (S B Zimmerman et al., 1987). The focus of this study is on its previously unreported potent anti-gonococcal activity and its mode of action. While it is true that broad-spectrum antibiotics have historically played a role in effectively controlling a wide range of infections, we and others believe that narrow-spectrum antibiotics have an overlooked importance in addressing bacterial infections. Their advantage lies in their ability to target specific pathogens without markedly disrupting the human microbiota.

(2) Animal models: We acknowledge the reviewer’s insight regarding the importance of in vivo validation to enhance oxydifficidin’s pre-clinical potential. However, due to the labor-intensive process needed to isolate oxydifficidin, obtaining a sufficient quantity for animal studies is beyond the scope of this study. Our future work will focus on optimizing the yield of oxydifficidin and developing a topical mouse model for subsequent investigations.

(3) Potential SNPs: Please see our response to Reviewer #1’s comment 3. We acknowledge that potential SNPs within dedA and rplL raise concerns regarding clinical resistance, which is a common issue for protein-targeting antibiotics. Yet, as pointed out in the manuscript, obtaining mutants in the lab was a very low yield endeavor.

Reviewer #3 (Public Review):

Summary:

The authors have shown that oxydifficidin is a potent inhibitor of Neisseria gonorrhoeae. They were able to identify the target of action to rplL and showed that resistance could occur via mutation in the DedA flippase and RplL.

Strengths:

This was a very thorough and clearly argued set of experiments that supported their conclusions.

Weaknesses:

There was no obvious weakness in the experimental design. Although it is promising that the DedA mutations resulted in attenuation of fitness, it remains an open question whether secondary rounds of mutation could overcome this selective disadvantage which was untried in this study.

We thank the reviewer for the positive comment. We agree that investigating factors that could compensate for the fitness attenuation caused by DedA mutation would enhance our understanding of the role of DedA.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The use of the term "N. gonorrhoeae wildtype" should not be used. It is uninformative, as the species contains a large amount of diversity. Instead, please name the strain. From Figure 1, it looks like the authors used MS11. Since MS11 is a longstanding lab strain and likely does not reflect circulating N. gonorrhoeae, and since H041 is no longer in circulation, the authors should ideally test the compound against more representative strains of N. gonorrhoeae. This includes panels of isolates available through the CDC, for example (https://www.cdc.gov/drugresistance/resistance-bank/index.html). I encourage the authors to include FC428 or another recently identified isolate with the penA 60 allele to demonstrate oxydifficidin's activity against contemporary concerning isolates/lineages.

(1) “N. gonorrhoeae MS11” is now used instead of “N. gonorrhoeae WT” in this manuscript.

(2) In our revised manuscript, we have added MIC data for recently identified Neisseria gonorrhoeae isolates AR#1280 and AR#1281 which contain the penA 60 allele (Table 1). The data shows oxydifficidin maintains its potent activity against these multidrug-resistant strains. We also added a description of this data to the results section as shown below.

Original text: “Oxydifficidin was more potent against N. gonorrhoeae MS11 than almost all other antibiotics we tested. In fact, it was only slightly less active than the highly optimized third-generation cephalosporin, ceftazidime.([18]) However, unlike third-generation cephalosporins, oxydifficidin retained activity against the multidrug resistant H041 clinical isolate (Table 1).([4]) H041 is resistant to the “standard of care” cephalosporin ceftriaxone (2 µg/mL) as well as a number of other antibiotics that are normally active against N. gonorrhoeae (penicillin G, 4 µg/mL; cefixime, 8 µg/mL; levofloxacin, 32 µg/mL).”

Changed to: “Oxydifficidin was more potent against N. gonorrhoeae MS11 than most other antibiotics we tested. Notably, unlike clinically used antibiotics such as ceftriaxone, azithromycin, and ciprofloxacin, oxydifficidin retained activity against all multidrug-resistant clinical isolates we examined (Table 1).” (Line 77-79)

(2) Does oxydifficidin have activity against N. meningitidis? It is the species most closely related to N. gonorrhoeae and the other pathogenic Neisseria.

Oxydifficidin has potent activity against N. meningitidis ATCC 13090. In our revised manuscript, we have included its MIC data in Figure 1c.

(3) Given claims that oxydifficidin activity in N. gonorrhoeae as compared to other Neisseria reflects N. gonorrhoeae's dedA and sensitive rplL, it would be good to assess the allelic diversity of these genes in N. gonorrhoeae. There are over 20,000 genomes from clinical isolates of N. gonorrhoeae in databases. It should be straightforward to check whether dedA and rplL allelic variants already exist in the population. Should variants be observed, oxydifficidin should be tested against the associated strains of N. gonorrhoeae.

Response: We thank the reviewer for this suggestion. We aligned the DedA sequence from strain MS11 with DedA proteins from 220 N. gonorrhoeae strains that have high-quality assemblies in NCBI. The result showed that there are no amino acid changes in this protein. Using the same method, we observed several single amino acid changes in RplL. This included changes at A64, G25 and S82 in 4 strains with one change per strain. These sites differ from R76 and K84, where we identified changes that provide resistance to oxydifficidin. Notably, in a similar search of representative Escherichia, Chlamydia, Vibrio, and Pseudomonas NCBI deposited genomes, we did not identify changes in RplL at position R76 or K84.

New text: “A survey of 220 N. gonorrhoeae strains with high-quality assemblies in NCBI found no mutations in the DedA protein.” (Line 104-105)

“These two mutations were not found in the survey of the same collection of N. gonorrhoeae strains used to look for DedA mutations.” (Line 143-144)

(4) Clinically relevant antibiotics for N. gonorrhoeae are penicillin, tetracycline, spectinomycin, gentamicin, ciprofloxacin, azithromycin, ceftriaxone; moreover, zoliflodacin and gepotidacin have reportedly successfully completed phase 3 trials. The authors should redo their MIC testing with these antibiotics (e.g., for Figures 1 and 2 and Tables 1 and 2), both because this will enable direct comparison with the many clinical isolates that have undergone testing and because these are the drugs most pertinent to clinical practice. Ampicillin, ceftazidime, chloramphenicol, bacitracin, and daptomycin are not relevant. Could the authors explain why they tested vancomycin, polymyxin B, irgasan, melittin, avilamycin, and thiostrepton?

Our use of antibiotics with diverse modes of action (e.g. vancomycin, polymyxin B, irgasan, melittin, avilamycin, and thiostrepton) in this study was intended to aid in the identification of oxydifficidin’s mode of action. This is true for both Tables 1 and 2.

To address the reviewer’s concern, in our revised manuscript, we have added MIC data for the following clinically relevant antibiotics: ceftriaxone (cephalosporin/beta-lactam), gentamicin (aminoglycoside), azithromycin (macrolide), and ciprofloxacin (fluoroquinolone) to Table 1.

(5) Please describe the characteristics of the transposon library (finding four transposons in a single strain does seem unexpected, given how most transposon libraries aim for one transposon insertion per strain).

We understand that one transposon insertion per strain is ideal for transposon libraries. This Bacillus strain proved to be recalcitrant to genetic manipulation. In the rare cases where we obtained resistance colonies upon electroporation with the transposon, all colonies contained multiple (≥ 4) transposon insertions. This made it impractical to build a library with one transposon insertion per library member.

We assumed that the anti-N. gonorrhoeae activity most likely originated from a natural product BGC, which typically range from 10-100 kb in size.

Based on the average of 50 kb per BGC, ~80 transposon insertions would be required to fully search the 4.2 Mb genome of Bacillus amyloliquefaciens BK for a BGC. At 4 mutations per transformant, 1x coverage of the genome would require only 20 library members.

After extensive electroporation of transposon into Bacillus amyloliquefaciens BK, we were able to obtain a library of 50 members, including one mutant (Tn5-3) that lacked anti-N. gonorrhoeae activity.

New text added to the methods section:

“A library containing 50 transposon mutants was obtained. In the mutants examined, each strain contained ≥4 transposon insertions” (Line 337-339)

(6) Please describe in the methods how you sequenced and annotated the genome of Bacillus amyloliquefaciens BK.

The sequencing method is now described in “Genomic Sequencing and annotation of Bacillus amyloliquefaciens” section. The genome of Bacillus amyloliquefaciens BK was not fully annotated. Mutations were identified as described in the updated methods section below.

New text:

“Genomic Sequencing and annotation of Bacillus amyloliquefaciens

Genomic DNA from Bacillus amyloliquefaciens BK WT and transposon mutant Tn5-3 was isolated using PureLink Microbiome DNA purification kit (Invitrogen) according to the manufacturer’s instructions.

The Bacillus amyloliquefaciens BK WT genome was assembled by mapping its sequencing data onto the annotated genome of Bacillus amyloliquefaciens FZB42 using Geneious Prime. Differences in the mutant strain Tn5-3 were identified by mapping its sequencing data onto the assembled Bacillus amyloliquefaciens BK WT genome. The mutated genes were then annotated using NCBI BLAST. The oxydifficidin BGC was annotated using the antiSMASH online server.” (Line 253-260)

(7) Please describe in the methods how you screened the library for strains that lacked anti-gonococcal activity.

The method is added to our revised manuscript as section “Screening of Bacillus Strains Lacking Anti-N. gonorrhoeae Activity”.

New text:

“Screening of Bacillus Strains Lacking Anti-N. gonorrhoeae Activity

The transposon mutants of Bacillus amyloliquefaciens BK were grown overnight in LB medium at 30 °C. Each overnight culture was then diluted 1:5000, and 1 μl of the diluted culture was spotted onto a GCB agar plate swabbed with N. gonorrhoeae cells. The plate was then incubated overnight at 37 °C with 5% CO2. The mutant strain (Tn5-3) lacking anti-N. gonorrhoeae activity was identified due to its failure to produce a zone of growth inhibition in the resulting N. gonorrhoeae lawn.” (Line 341-346)

(8) Was only one strain found that was a 'non-producer' of anti-N. gonorrhoeae activity? Line 68 suggests that this was only one of multiple non-producers. Is that correct? If so, did you work up the others, and did they also have disruptions in the same biosynthetic gene cluster?

Only one strain was identified as a “non-producer” of anti-N. gonorrhoeae activity. We have modified the text to clarify this point.

Original text: “The sequencing of one non-producer strain revealed that it surprisingly contained four transposon insertions and one frame shift mutation.”

Changed to: “The sequencing of the non-producer strain revealed that it surprisingly contained four transposon insertions and one frame shift mutation.” (Line 53-54 )

(9) All sequences (including Bacillus amyloliquefaciens BK) must be deposited in a public database (e.g., NCBI) and the accession numbers reported in the manuscript.

Genomic sequence data of Bacillus amyloliquefaciens BK has been deposited in GenBank, and its accession number (GCA_019093835.1) now appears in figure legend of Figure S1a.

Figure S1a legend:

“Genome-based phylogenetic tree containing Bacillus amyloliquefaciens BK and closely related Bacillus spp. The tree was built by Genome Clustering of MicroScope using neighbor-joining method. The NCBI accession numbers of Bacillus strains used in the tree are GCA_000196735.1, GCA_000204275.1, GCA_000015785.2, GCA_019093835.1, GCA_000009045.1, GCA_000011645.1, GCA_000172815.1, GCA_000008005.1, and GCA_000007845.1 (from top to bottom).”

Minor

(10) Statements in the article would benefit from fact-checking. For example:

- gonorrhea is not the second most prevalent sexually transmitted infection worldwide; it is the second most reported bacterial sexually transmitted infection.

- Treatment is ceftriaxone 500mg IM x1 in the US, but 1g IM x1 in the UK and Europe. The UK guidelines also permit ciprofloxacin, should sequencing indicate gyrA 91S. I suggest reviewing / specifying which treatment guidelines you're referring to.

We appreciate the reviewer’s corrections. The word “prevalent” is now changed to “reported”.

Original text: “Gonorrhea, which is caused by Neisseria gonorrhoeae, is the second most prevalent sexually transmitted infection worldwide.”

Changed to: “Gonorrhea, which is caused by Neisseria gonorrhoeae, is the second most reported sexually transmitted infection worldwide.” (Line 2-3)

Original text: “Gonorrhea is the second most prevalent sexually transmitted infection worldwide, its causative agent is the bacterium Neisseria gonorrhoeae.”

Changed to: “Gonorrhea is the second most reported sexually transmitted infection worldwide, its causative agent is the bacterium Neisseria gonorrhoeae.” (Line 18-19)

“In the USA” is now added to the sentence stating gonorrhea treatment.

Original text: “The high dose (500 mg) of the cephalosporin ceftriaxone is currently the only recommended therapy for treating gonorrhea infections.”

Changed to: “The high dose (500 mg) of the cephalosporin ceftriaxone is currently the only recommended therapy for treating gonorrhea infections in the USA.” (Line 20-22)

(11) Please make sure all results are in the results section. The report of cell morphology, for example, should be in the results, not the discussion.

In our revised manuscript, we have included the cell morphology data in the results section with the text changes below.

Original text: “Interestingly, not only was dedA deficient N. gonorrhoeae less susceptible to oxydifficidin, oxydifficidin also kills this mutant more slowly (Figure 2b) than WT N. gonorrhoeae MS11.”

Changed to: “Interestingly, not only was dedA deficient N. gonorrhoeae less susceptible to oxydifficidin, oxydifficidin also kills this mutant more slowly (Figure 2b) than WT N. gonorrhoeae MS11. The dedA deletion mutant also showed an altered cell morphology with reduced membrane integrity and lower formation of micro-colonies (Figure S4). (Line 100-104)

Original text: “The dedA deletion mutant also showed an altered cell morphology with reduced membrane integrity and lower formation of micro-colonies (Figure S4), indicating that it should show reduced pathogenesis and fitness, and, as a result, not accumulate in a clinical setting, which adds to the therapeutic appeal of oxydifficidin.”

Changed to: “The dedA deletion mutant exhibited altered cell morphology, characterized by diminished membrane integrity and reduced micro-colony formation, indicating that it should show reduced pathogenesis and fitness, and, as a result, not accumulate in a clinical setting, which adds to the therapeutic appeal of oxydifficidin” (Line 206-210)

(12) Tables 1 and 2 should be combined and should address the most relevant antibiotics

The MIC data of additional relevant antibiotics are now included in Table 1. However, we still believe that keeping Tables 1 and 2 separate enhances the clarity of the manuscript. Table 2 specifically focuses on diverse ribosomal targeting antibiotics, which highlights the unique binding site of oxydifficidin.

(13) Supplemental Figure 1a. The tree could be better resolved, and there are four entries with the identical listing of "Bacillus amyloliquefaciens subsp. plantarum" on different branches. In the methods or the legend, please indicate the accession numbers for these genomes. Also please specify how this tree was made-is it a maximum likelihood tree? Something else?

The tree is now better resolved and includes new entries. The requested information regarding accession numbers and tree construction method has been included in the figure legend.

New supplemental Figure 1a legend:

“a. Genome-based phylogenetic tree containing Bacillus amyloliquefaciens BK and closely related Bacillus spp. The tree was built by Genome Clustering of MicroScope using neighbor-joining method. The NCBI accession numbers of Bacillus strains used in the tree are GCA_000196735.1, GCA_000204275.1, GCA_000015785.2, GCA_019093835.1, GCA_000009045.1, GCA_000011645.1, GCA_000172815.1, GCA_000008005.1, and GCA_000007845.1 (from top to bottom).”

Reviewer #2 (Recommendations For The Authors):

The conclusions drawn in the manuscript are well-supported by the experimental data presented.

I have the below minor comments:

(1) "serendipitously identified" - I feel this wording should be avoided throughout the manuscript. The point of a research paper is to communicate methodology and experimental detail, and this language portrays the opposite.

While we agree that methodology and experimental procedures are paramount in scientific reporting, we believe it is equally important to convey, particularly to younger generations, that a part of the scientific process is often unplanned and can benefit from chance observations. Therefore, we would like to keep this wording.

(2) The introduction should include the biological roles/function of DedA proteins in bacteria.

DedA proteins perform a wide array of biological roles and functions in bacteria. In the results section (Line 107-116), we have described the most well-established of these functions, particularly the flippase activity, which appears to be directly related to oxydifficidin sensitivity. We believe that introducing this information in the results section enhances the manuscript’s clarity and flow.

(3) "When we screened this contaminant for antibacterial activity against lawns of other Gram-negative bacteria it did not produce a zone of growth of inhibition against any of the bacteria we tested (e.g., Escherichia coli, Vibrio cholerae, Caulobacter crescentus)." Can these data Figures be included in the Supplements?

This result was recorded in the lead author’s notebook, but no image was saved.

(4) Line 52: Was any base analyses performed on the Tn-mutants i.e., how many insertion-sites? Depth of mutants? Was a library constructed in this study or previously? Why were only BGC assessed?

Please see our response to Reviewer #1’s comment (5). We focused on BGCs because we believed the anti-N. gonorrhoeae activity most likely resulted from a molecule encoded by a natural product BGC.

(5) Line 98: Do the other 2 predicted DedA-like proteins also have a role in uptake of oxydifficidin? Is there some redundancy in uptake?

We generated knockout mutants for two other predicted DedA-like proteins in N. gonorrhoeae MS11, and the MIC of oxydifficidin for these mutants remained the same as for the N. gonorrhoeae MS11 wild type strain. Therefore, we believe that the DedA protein discussed in this manuscript is the primary transporter of oxydifficidin. However, we cannot completely rule out the possibility of redundancy in oxydifficidin uptake by other DedA-like proteins.

New text: “We also generated deletion mutants for two other predicted dedA-like genes, and the MIC of oxydifficidin for these mutants remained the same as for the N. gonorrhoeae MS11 wild type strain.” (Line 98-100)

Reviewer #3 (Recommendations For The Authors):

This is a well presented manuscript and I could not immediately see any issues with it.

We appreciate the reviewer’s positive feedback.

Author response:

We are submitting a revised manuscript with major additions that address the main concerns in the initial reviews. At the highest level, this revision provides i) orthogonal biochemical measurements that yield concrete evidence of lysosomal protein aggregates, and ii) a plausible mechanism linking lysosomal lipid handling and protein aggregation through disruption of ESCRT function. We believe these additions significantly improve the completeness of this study and the conclusions that can be drawn from the data.

Below are more specific highlights on the addition in this revision:

-       We included orthogonal techniques (thioflavin-T staining and Lyso-IP followed by differential extraction) and confirmed the accumulation of RIPA-insoluble protein aggregates at the lysosomes in cells under lipid perturbation (Figure 3).

-       We performed TMT-Proteomics and identified accumulation of insoluble ESCRT components at the lysosomes under lipid perturbation (Figure 4). Two new authors involved in this effort are added onto the manuscript.

-       The ESCRT result prompted us to revisit lysosomal membrane integrity. With improved imaging conditions and analysis we were able to see increased membrane permeabilization under lipid perturbation. VPS4A overexpression partially rescued this phenotype, suggesting that lipid accumulation impairs ESCRT disassembly (Figure 5).

-       Together, the results suggest that lipid perturbation impairs ESCRT function, compromising both lysosomal membrane repair and microautophagy, resulting in the accumulation of endogenous protein aggregates at the lysosomes (Graphical Abstract).

Reviewer #1 (Recommendations For The Authors):

(1) Perhaps the most prominent limitation of this work is the unilateral focus on native cells (i.e. cells under no endogenous or exogenous stress) as the model for protein aggregate formation. Furthermore, although the ProteoStat stain has been utilized by many investigators before, the sole reliance on this stain as the read-out for their assays is concerning. To compound the concern, the ProteoStat-positive puncta co-localize with lysosmal markers which was surprising even to the authors. All in all, it behooves the authors to test proteostasis in multiple parallel ways to actually define what they are studying. How is it possible that protein aggregates under native conditions are only co-localized with lysosomes? Are we really studying protein aggregates which should predominantly be cytoplasmic insoluble aggregates?

(a) They need to get away from a simple stain like ProteoStat and conduct co-stainings with other markers such as poly-ubiquitin antibodies and other chaperones to define what and where else exactly are these aggregates.

Co-staining with poly-ubiquitin was included in the original manuscript. We added orthogonal staining with another widely used amyloid dye, Thioflavin-T, and provided fine-grained quantification of lysosomal vs cytosolic localization of various signals (Figures S4A-C & 3A-B).

(b) They need to do Immunoblots with and without triton insolubility to see if these aggregates are insoluble as most would predict. They can do lysosomal isolation vs cytoplasmic to see if the insoluble aggregates are really lysosomal.

We performed Lyso-IP followed by differential detergent extraction to confirm the accumulation of insoluble proteins at the lysosomes (Figure 3C). Proteomic analysis identified some of these insoluble proteins as ESCRT subunits (Figure 4).

(c) They should compare aggregate formation in the native state versus cells with lysosomal inhibition via Bafilomycin or chloroquine versus cells with proteosomal inhibition. The lysosomal inhibition experiments are particularly informative given the lysosomal relevance they have uncovered.

We included other small molecule inhibitors and at different time points to compare the effect of different modes of proteostasis challenge (Figure S4A-D). Together with the ESCRT finding, our results suggest the role of microautophagy in our system, and provide a model of how ProteoStat- and/or ubiquitin- positive substrates become partitioned between the cytoplasm and lysosomes under different perturbations.

(d) Many protein aggregates which are too bulky for proteosome degradation will traditionally be dealt with by aggrephagy. Why is this not observed?

Knockdown of core macroautophagy components did not impact Proteostat intensity in our CRISPRi screen, suggesting that basal macroautophagy plays a negligible role in clearing endogenous amyloid-like structures in our experimental system. We provide an alternative model that these aggregates instead arrive at the lysosomes via microautophagy.

(2) After addressing #1, they can validate if the genes they identified by CRISPR screens are also important in modulation of protein aggregate burden in other systems. For example, if they inhibit lysosomes by Bafilo or Chloroquine to obtain protein aggregates and then Knockdown the identified genes in the CRISPR screens, will they get the same results?

We addressed the effect of different modes of proteostasis challenge as recommended above. Deacidifying the lysosomes alone causes intense protein aggregation (Figure S4A-D) and eventually cell death, and was thus not combined with other perturbations.

(3) They identify lysosomal lipid metabolism genes/pathways as the culprit for inducing proteostasis. In particular sphingolipid and cholesteryl ester species appear to be operational here. However, there are no specific lipids species or specific lipid metabolism gene that is causative. Rather, you have to knockdown entire processes to have an effect. This suggests that the focus on lysosome health (i.e. permeability, proteolysis, etc) is rudimentary. When you have to knockdown entire classes of lipids, this would indicate more broad effects on cellular lipids (including membrane lipids beyond the lysosome) and related cellular health?

We included data on the effect of knocking down MYLIP, PSAP, and as a comparison PSMD2 on the growth rate of K562 cells (Figure S5A). MYLIP and PSAP KDs, which cause predominantly an accumulation of lipids, do not impede cell growth. Increasing lipid uptake by MYLIP KD increases cell proliferation under our culture conditions, suggesting a general negative impact on cell health was not required for the association between lipid levels and protein aggregates.

(a) They conduct a superficial methyl-beta-cyclodextrin experiment with equivocal results. The use of MBCD for different time-courses to deplete various membrane cholesterol pools including the plasma membrane pool is important to ascertain what aspect of the cellular cholesterol is affecting proteostasis. MBCD +/- cholesterol reintroduction time-courses for rescue will also be key to determine the culprit cellular cholesterol pool.

The MBCD / Filipin experiment helped us determine that ProteoStat doesn’t directly stain cholesterol, nor any major plasma membrane components. Free cholesterol was implicated in neither the screen nor the lipidomics and was not the subject of targeted experiments.

(b) The same concept can be applied to sphingolipids. There are sphingolipids in abundance in multiple membrane compartments. Which ones are causal here? More nuanced evaluation of this with sphingolipid staining/tracking can be conducted.

We attempted experiments where sphingolipids were added back to cells grown in FBS-depleted media. Nevertheless, we were not able to consistently deliver these lipid species and doing so while ensuring the correct subcellular localization at physiologically relevant level would require substantial methods development.

(c) As part of this, are lipid rafts and/or caveolae being affected by the perturbations in cholesterol and sphingolipids? Lipid rafts are highly enriched in these 2 lipids which could link to their preteostasis observation.

Indeed, ceramides released from SM hydrolysis are proposed to self-assembled into microdomains with negative curvature that can promote the formation of intralumenal vesicles (Alonso and Goni, 2018; Niekamp et al 2022). We propose that SM accumulation may hinder this process by counteracting the negative membrane curvature and impede microautophagy.

(d) How about ER membrane lipids? The UPR and subsequent effects on proteostasis are intricately involved with ER lipid bilayer composition.

We did not perform lipidomics on ER membranes in this study, though we note that at steady state, sphingolipids and cholesterol esters are not expected to be enriched at the ER (Ikonen and Zhou, 2021). We checked whether lipid-related genetic perturbations induced the UPR in published perturb-seq data in K562 cells. Neither MYLIP nor PSAP knockdown induced a UPR.

In conclusion, the manuscript is interesting but the excitement over a link between lysosome-related lipid metabolism and proteostasis needs to be tamped until a more robust experimental approach is employed to generate supportive and corroborating results.

Reviewer #2 (Recommendations For The Authors):

- The paper has a number of grammatically awkward sentences. Editing these would enhance clarity.

- It is important to show the co-localization of aggregates with the lysosome. This is shown in supplements but should be in a main figure. Here the authors cite previous work indicating that ProteoStat puncta co-localize with ubiquitinated proteins and state that they do not see this, then essentially just move on. Is there an explanation for this discrepancy and can it be resolved? What do they think is really going on? What happens to levels of ubiquitinated proteins when lipid metabolism is perturbed as in these experiments?

We have included the lipid-induced lysosomal protein aggregation data in the main text (Figure 3A-B), and provided fine-grained quantification of the cytosolic-vs-lysosomal ProteoStat / Ub / ThT signals under different aggregate-inducing conditions (Figure S4A-D). We discuss these results in the main text and propose a model involving ESCRT-mediated microautophagy in the main text. This is supported further by the LysoIP-proteomics and LMP analysis.

- Please add an indicator of amino acid numbers to Fig. 3C.

These annotations are now included (now Figure S3C).

- The legend for 3D is mislabelled.

We have corrected the legend (now Figure S3D).

Reviewer #3 (Recommendations For The Authors):

Protein homeostasis and lipid homeostasis are both are important for maintaining cellular functions. However, the crosstalk remains largely unknown. The manuscript entitled as "Impairment of lipid homoeostasis causes accumulation of protein aggregates in the lysosome" deals with this interesting topic. An important link between lysosomal protein aggregation and sphingolipids/cholesterol esters metabolism were discovered. The topic belonging to the Cell Biology domain also falls into the aims and scope of eLife. Here are the revisions I recommend:

(1) From lipidomics analysis, a remarkable correlation between levels of sphingomyelin and cholesterol ester and ProteoStat staining was found. Could the authors explain how sphingomyelin and cholesterol ester are quantified? The two lipids are not included as internal standards from the lipidomics experiment.

Sphingomyelin and cholesterol ester internal standards are included in the Avanti 330707 SPLASH® LIPIDOMIX® Mass Spec Standard, which was supplied at 3% v/v to the MeOH/H2O cell lysis buffer. We have amended the Methods section to clarify this.

(2) Could the authors perhaps delete Figure 1B and show it on Figure 2A only? There is no need to show the same figure two times. The threshold of both False Discovery Rate and Median Enrichment needs to be added. From Figure 2A, the Lysosomal hydrolases (GBA, LIPA, GALC) seems located in statistically insignificant region. Based on previous studies, the GBA could have an effect on sphingolipid levels, then how to explain that sphingomyelin was highly correlated with ProteoSate staining?

We have combined the two volcano plots into a single figure (now Figure 1D), and added a line to help visualize the gene effects while considering the combined contribution of FDR and enrichment. Individual lysosomal hydrolases indeed have insignificant effects on ProteoStat and this is discussed in the main text as having relatively constrained impacts on the general lipidome. For example, while GBA and GALC KDs can lead to accumulation of their immediate substrates (glucosylceramide and galactosylceramide, respectively), they do not directly impinge on sphingomyelin.

(3) The authors show the corelation between ProteoState staining and different lipids/lipid classes in Figure 3B and Figure S3A. It is not necessary to show the corelation with individual lipids (such as sphingomyelin(d18:1/24:0) and cholesterol ester(18:2). The corelation with full collection of lipid classes would be more representative, which is only list in Figure 3B and Figure S3A. It is suggested to add the information of how many individual lipids in each chass are used for the correlation analysis. Replace Figure 3A to Figure S3A, and put Figure 3A as supplementary figure are suggested.

We decided to retain the correlation of two individual lipids (a sphingomyelin and a cholesterol ester species) with ProteoStat as examples to illustrate with clarity how we obtained the class-wide comparison. The number of individual lipids included in each class for correlation analysis is now included in Figures 2F and S3A.

(4) The authors state that lipid uptake and metabolism modulate proteostasis. However, only cholesterol and LDL were tested. It would be more precise to state as cholesterol uptake and metabolism modulate proteostasis. In addition, sphingolipids and cholesterol esters accumulate with increased lysosomal protein aggregation. It would be interesting to see the effects of sphingolipids uptake, since sphingolipids are correlated with proteostasis better than cholesterol.

We attempted to add back specific sphingolipids to assess sufficiency. However, we found it challenging to ensure that these lipids were distributed to the correct subcellular locations at physiologically relevant levels. Without this crucial information, it was difficult to draw any conclusions about the sufficiency of the sphingolipids we tested to impair proteostasis.

Alonso A, Goñi FM. 2018. The Physical Properties of Ceramides in Membranes. Annu Rev Biophys 47:633–654. doi:10.1146/annurev-biophys-070317-033309

Ikonen E, Zhou X. 2021. Cholesterol transport between cellular membranes: A balancing act between interconnected lipid fluxes. Dev Cell 56:1430–1436. doi:10.1016/j.devcel.2021.04.025

Niekamp P, Scharte F, Sokoya T, Vittadello L, Kim Y, Deng Y, Südhoff E, Hilderink A, Imlau M, Clarke CJ, Hensel M, Burd CG, Holthuis JCM. 2022. Ca2+-activated sphingomyelin scrambling and turnover mediate ESCRT-independent lysosomal repair. Nat Commun 13:1875. doi:10.1038/s41467-022-29481-4

Author response:

We thank the editors and reviewers for their thorough evaluation of our manuscript. We appreciate the constructive feedback and insights provided. 

We acknowledge that some of our conclusions would benefit from more measured statements and additional computational controls. We will revise the manuscript to better reflect the scope and limitations of our analytical approach. While we cannot add new experimental validations at this stage, we will strengthen our computational analyses and clarify our methodology.

Below, we outline our planned revisions to address the major points raised in the public reviews:

Clarification of Terms and Definitions:

(1) We will make it clearer in our manuscript to emphasize that we reuse the same raw datasets from our previous study as described in Calendrilli et al, 2023, and there is no modification to the experimental methods or data. 

(2) We will provide clear definitions for:

- "Non-differentially expressed" genes

- "Ctrl specific" RNA sets

- The composition of control populations in different analyses

(3) We will revise the use of "non-diffusive RNA-chromatin interactome" and “RNase-resistant” terminology to better reflect our actual findings.

(4) We will also improve clarity regarding:

- The rationale for focusing on specific genomic regions

- The interpretation of evolutionary conservation data

(5) We will provide additional rationale on the exclusion of short-range interactions.

Figure Revisions:

(1) Figure 3a: We will correct any discrepancy between text references and figure content.

(2) Figure 4: We will standardize the color scheme between control and RNase-treated samples.

(3) We will follow the reviewer's suggestion to move figure 1g to the supplementary file. 

Additional Computational Analyses:

(1) We will consider adding controls for RNA length effects and integrate any existing knowledge on the protection extent variation across different RBP.

Discussions:

(1) We will carefully rephrase our conclusions to more accurately reflect the scope and limitations of our computational findings, ensuring we do not overstate the implications.

(2) We will expand the discussion of limitations, including:

- The focus on RNase-resistant interactions only

- The cell-type specificity of our findings

- The lack of functional validation

- The limited ability to discern and study the transient or weak RNA-chromatin interactions using the current dataset

(3) Regarding the recent papers from Jenner and Davidovich groups about RNase treatment effects on chromatin solubility:

- We will discuss these findings in our revised manuscript

- We will address potential limitations this may impose on our interpretations

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work examines the binding of several phosphonate compounds to a membrane-bound pyrophosphatase using several different approaches, including crystallography, electron paramagnetic resonance spectroscopy, and functional measurements of ion pumping and pyrophosphatase activity. The work attempts to synthesize these different approaches into a model of inhibition by phosphonates in which the two subunits of the functional dimer interact differently with the phosphonate.

Strengths:

This study integrates a variety of approaches, including structural biology, spectroscopic measurements of protein dynamics, and functional measurements. Overall, data analysis was thoughtful, with careful analysis of the substrate binding sites (for example calculation of POLDOR omit maps).

Weaknesses:

Unfortunately, the protein did not crystallize with the more potent phosphonate inhibitors. Instead, structures were solved with two compounds with weak inhibitory constants >200 micromolar, which limits the molecular insight into compounds that could possibly be developed into small molecule inhibitors. Likewise, the authors choose to focus the spectroscopy experiments on these weaker binders, missing an opportunity to provide insight into the interaction between more potent binders and the protein.

We acknowledge the reviewer concern regarding the choice of weaker inhibitors. We attempted co-crystallization with all available inhibitors, including those with higher potency. However, despite numerous efforts, these potent inhibitors yielded low-resolution crystals, making them unsuitable for detailed structural analysis. Therefore, we chose to focus on the weaker binders, as we were able to obtain high-quality crystal structures for these compounds. This allowed us to perform DEER spectroscopy with the added advantage of accurately analyzing the data against structural models derived from X-ray crystallography. Using these weaker inhibitors enabled a more precise interpretation of the DEER data, thus providing reliable insights into the conformational dynamics and inhibition mechanism. However, as suggested by the reviewer, in the revised version, we will perform DEER analysis on the more potent inhibitors to provide additional insight into their interactions.

In general, the manuscript falls short of providing any major new insight into membrane-bound pyrophosphatases, which are a very well-studied system. Subtle changes in the structures and ensemble distance distributions suggest that the molecular conformations might change a little bit under different conditions, but this isn't a very surprising outcome. It's not clear whether these changes are functionally important, or just part of the normal experimental/protein ensemble variation.

We respectfully disagree with the reviewer. The scale of motions seen in this study correspond to those seen in the full panoply of crystal structures of mPPases. Some proteins undergo very large conformational changes during catalysis – such as the rotary ATPase. This one doesn’t, meaning that the precise motions we describe are likely to be relevant. Conformational changes in the ensemble, whether large or small, represent essential protein motions which underlie key mPPase catalytic function. Our DEER spectroscopy data demonstrate the sensitivity and resolution necessary to monitor these subtle changes in equilibria, even if these are only a few Angstroms. For several of the conditions we investigated by DEER in solution, corresponding x-ray structures have been solved, with the derived distances agreeing well with the DEER distributions. This further validates the biological relevance of the structures, including serial time-resolved ones that indicate asymmetry.

The ZLD-bound crystal structure doesn't predict the DEER distances, and the conformation of Na+ binding site sidechains in the ZLD structure doesn't predict whether sodium currents occur. This might suggest that the ZLD structure captures a conformation that does not recapitulate what is happening in solution/ a membrane.

We agree with the reviewer that the ZLD-bound crystal structure does not predict the DEER distances. However, we believe this discrepancy arises from the effect of the bulkiness of ZLD inhibitor, which prevents the closure of the hydrolytic centre. Additionally, the absence of Na+ at the ion gate in the ZLD-bound structure suggests that Na+ transport does not occur, a conclusion further supported by our electrometric measurements. We agree with the reviewer, that the distances observed in the DEER experiments might represent a potential new conformation in solution, which may not be captured by the static X-ray structure, thereby offering insights into the dynamic nature of the protein under physiological conditions. Finally, the static x-ray structures have not captured the asymmetric conformations that must exist to explain half-of-the-sites reactivity.

Reviewer #2 (Public review):

Summary:

Crystallographic analysis revealed the asymmetric conformation of the dimer in the inhibitor-bound state. Based on this result, which is consistent with previous time-resolved analysis, authors verified the dynamics and distance between spin introduced label by DEER spectroscopy in solution and predicted possible patterns of asymmetric dimer.

Strengths:

Crystal structures with inhibitor bound provide detailed coordination in the binding pocket thus useful information for the PPase field and maybe for drug development.

Weaknesses:

The distance information measured by DEER is advantageous for verifying the dynamics and structure of membrane protein in solution. However, regarding T211 data, which, as the authors themselves stated, lacks measurement precision, it is unclear for readers how confident one can judge the conclusion leading from these data for the cytoplasmic side.

We thank the reviewer for acknowledging the advantageous use of the DEER methodology for identifying dynamic states of membrane proteins in solution. We used two sites in our analysis: S525 (periplasm) and T211 (cytoplasm). As we clearly stated in the original manuscript, S525R1 yielded high-quality DEER data, while T211R1 yielded weak (or no) visual oscillations, leading to broad, though different distributions for the several conditions tested. Our main conclusions are based on the S525R1 data. We included the T211R1 data because, although it does not provide definitive evidence, it is consistent with our proposed model and offers additional insights into biologically relevant conditions. Furthermore, the shifts in the centre of mass (Fig EV8D) of the broad T211R1 distributions show a trend that is consistent with our model; although not proving it, it does not exclude it either. Lastly, these data do indeed confirm an important structural feature of mPPase in solution conditions which is the intrinsically high dynamic state of the loop5-6 where T211 is located, and consistent with our previous (Kellosalo et al., Science,  2012; Li et al., Nat. Commun, 2016; Vidilaseris et al., Sci. Adv., 2019; Strauss et al., EMBO Rep., 2024) and current x-ray crystallography data.

The distance information for the luminal site, which the authors claim is more accurate, does not indicate either the possibility or the basis for why it is the ensemble of two components and not simply a structure with a shorter distance than the crystal structure.

We thank the reviewer for pointing out this possibility and alternative interpretation of our DEER data. In the revised version, we will show that our DEER data are consistent with (and do not exclude) asymmetry and rephrase to be inclusive of other possibilities. Importantly, this additional possibility does not affect the current interpretation of the data in our manuscript.

Reviewer #3 (Public review):

Summary:

Membrane-bound pyrophosphatases (mPPases) are homodimeric proteins that hydrolyze pyrophosphate and pump H+/Na+ across membranes. They are attractive drug targets against protist pathogens. Non-hydrolysable PPi analogue bisphosphonates such as risedronate (RSD) and pamidronate (PMD) serve as primary drugs currently used. Bisphosphonates have a P-C-P bond, with its central carbon can accommodate up to two substituents, allowing a large compound variability. Here the authors solved two TmPPase structures in complex with the bisphosphonates etidronate (ETD) and zoledronate (ZLD) and monitored their conformational ensemble using DEER spectroscopy in solution. These results reveal the inhibition mechanism of these compounds, which is crucial for developing future small molecule inhibitors.

Strengths:

The authors show that seven different bisphosphonates can inhibit TmPPase with IC50 values in the micromolar range. Branched aliphatic and aromatic modifications showed weaker inhibition.

High-resolution structures for TmPPase with ETD (3.2 Å) and ZLD (3.3 Å) are determined. These structures reveal the binding mode and shed light on the inhibition mechanism. The nature of modification on the bisphosphonate alters the conformation of the binding pocket.

The conformational heterogeneity is further investigated using DEER spectroscopy under several conditions.

Weaknesses:

The authors observed asymmetry in the TmPPase-ELD structure above the hydrolytic center. The structural asymmetry arises due to differences in the orientation of ETD within each monomer at the active site. As a result, loop5-6 of the two monomers is oriented differently, resulting in the observed asymmetry. The authors attempt to further establish this asymmetry using DEER spectroscopy experiments. However, the (over)interpretation of these data leads to more confusion than any further understanding. DEER data suggest that the asymmetry observed in the TmPPase-ELD structure in this region might be funneled from the broad conformational space under the crystallization conditions.

See also the response below - We respectfully disagree with the reviewer. The asymmetry was previously established using serial time crystallography (Strauss et al., EMBO Rep, 2024) and biochemical assays (e.g. Malinen et al., Prot. Sci., 2022; Artukka et al., Biochem J, 2018; Luoto et al., PNAS, 2013) and also partially seen in one static structure (Vidilaseris et al., Sci Adv 2019). DEER data only show that the previously proposed asymmetry could also be present within the conformational ensemble in solution conditions. Indeed, our data do not (and cannot) exclude this possibility.

DEER data for position T211R1 at the enzyme entrance reveal a highly flexible conformation of loop5-6 (and do not provide any direct evidence for asymmetry, Figure EV8).

Please see relevant response above. We acknowledge that T211 is indeed situated on a highly dynamic loop, which is important for gating and our DEER data confirm its high flexibility. Given we have not observed oscillations of this site, leading to broad distributions, we have stated in the original manuscript that we will not establish the presence of any asymmetry in solution on the basis of T211, rather relying on the S525 site, for which we have acquired high-quality DEER data, as was also pointed out and have been commented on by all reviewers.

Similarly, data for position S521R1 near the exit channel do not directly support the proposed asymmetry for ETD.

The reviewer appears to suggest that we hold the S525R1 DEER data as direct proof of asymmetry; this is combative on the grounds that to directly prove asymmetry would require time-resolved DEER measurements, far beyond the scope of this work. Rather, we have applied DEER measurements to explore whether asymmetry (observed previously via time-resolved X-ray crystallography) is also present (or indeed a possibility) in solution. We simply state that the DEER data are consistent with asymmetry (i.e., that the mean distance increases in the presence of ETD compared to the apo-state). This is a restrained interpretation of the data.

Despite the high quality of the data, they reveal a very similar distance distribution. The reported changes in distances are very small (+/- 0.3 nm), which can be accommodated by a change of spin label rotamer distribution alone. Further, these spin labels are located on a flexible loop, thereby making it difficult to directly relate any distance changes to the global conformation

We thank the reviewer for recognising the high quality of our DEER data for the S525R1, where visual oscillations in the raw traces, as in our case, reportedly lead to highly accurate and reliable distributions, able to separate (in fortuitous cases) helical movements of only a few Angstroms. The ability of DEER/PELDOR offering near Angstrom resolution was previously demonstrated by the acquisition and solution of high resolution multi-subunit spin-labelled membrane protein structures (Pliotas at al., PNAS, 2012; Pliotas et al., Nat Struct Mol Biol, 2015; Pliotas, Methods Enzymol, 2017) as well as it ability in detecting small (and of similar to mPPase magnitude) conformational changes in different integral membrane proteins systems (Kapsalis et al., Nature Comms, 2019; Kubatova et al., PNAS, 2023; Schmidt et al., JACS, 2024; Lane et al., Structure, 2024; Hett et al., JACS, 2021; Zhao et al., Nature, 2024), occurring under different conditions and/or stimuli in solution and/or lipid environment. The changes here are not very small (e.g. ~ 7 Angstroms between the two mean distance extremes (Ca vs IDP)) for DEER’s proven detection sensitivity, and with all other conditions showing changes between those extremes.

These changes are relatively small, but they are expected for membrane ion pumps. Indeed, none of the mPPase structures show helical movements of greater than a half a turn, and that only in helices 6 and 12. There appear to be larger-scale loop closing motions of the 5-6 loop that includes T211, due to the presence of E217 which binds to one of the Mg2+ ions that coordinate the leaving group phosphate. (This is, inter alia, the reason that this loop is so flexible: it can not order before substrate is bound.) Here we have the resolution to detect such subtle differences by DEER, given there are clear shifts in our time domain data and these are reflected in the mean distances in the distributions. Therefore, our study demonstrates the sensitivity and resolution DEER offers in detecting subtle conformational transitions, key in membrane proteins pathways. To further belabour this point, we do not quantify the DEER data (for instance through parametric fitting) to extract populations of different conformational states and we appreciate that to do so would be highly prone to error; however we do (and can, we feel without overinterpretation) assert that the mean distances shift.

The interpretations listed below are not supported by the data presented:

(1) 'In the presence of Ca2+, the distance distribution shifts towards shorter distances, suggesting that the two monomers come closer at the periplasmic side, and consistent with the predicted distances derived from the TmPPase:Ca structure.' Problem: This is a far-stretched interpretation of a tiny change, which is not reliable for the reasons described in the paragraph above.

While the authors overall agree with the reviewer assessment that ±0.3 nm is a small (not a minor) change, there are literature examples quantifying (or using for quantification) distribution peaks separated by similar Δr. (Kubatova et al., PNAS, 2023; Schmidt et al., JACS, 2024; Hett et al., JACS, 2021; Zhao et al., Nature, 2024). In particular, none of the mPPase structures show helical movements of greater than a half a turn (in helices 6 and 12 in particular). There appear to be larger-scale loop closing motions of the 5-6 loop that includes T211, due to the presence of E217 which binds to one of the Mg2+ ions that coordinate the leaving group phosphate. (This is, inter alia, the reason that this loop is so flexible: it can not order before substrate is bound.)

Importantly, we have fitted Gaussians to the experimental distance distributions of 525R1 output by the Comparative Deer Analyzer 2.0 and observed a change in the distribution width in presence of Ca2+, implying the rotameric freedom of the spin label is restricted. However, the CW-EPR for 525R1 indicate that the rotational correlation time of the spin label is highly consistent between conditions (the spectra are almost identical); this cannot be explained simply by rotameric preference of the spin label (as asserted by the reviewer 3), as there is no (further) immobilisation observed from the CW-EPR of apo-state (Figure EV9) to that in presence of Ca2+. Furthermore, in the absence of conformational changes, it is reasonable to assume (and demonstrable from the CW-EPR data) that the rotamer cloud should not significantly change between conditions. However, Gaussian fits of the two extreme cases yielding the longest (i.e., in presence of IDP) and shortest (in presence of ZTD) mean distances for the 525R1 DEER data indicated significant (i.e., above the noise floor after Tikhonov validation) probability density for the IDP condition at 50 Å (P(r) = 0.18). This occurs at four standard deviations above the mean of the ZTD condition, which by random chance should occur with <0.007% probability. Indeed, one can say that to observe 18% probability density at four standard deviations above the mean by random chance would occur on the order of one in 4 x 10^6.

As in previous response the method can detect changes of such magnitude which are not small, but physiologically relevant and expected for integral membrane proteins, such as mPPases. Indeed, even in equal (or more) complex systems such as heptameric mechanosensitive channel proteins DEER provided sub-Angstrom accuracy, when a spin labelled high resolution XRC structure was solved (Pliotas et al., PNAS, 2012; Pliotas et al., Nat Struct Mol Biol, 2015). Despite this is ideal case where DEER accuracy was experimentally validated another high resolution structural method on modified membrane protein and is not very common it demonstrates the power of the method , especially when strong oscillations are present in the raw DEER data (as here for mPPase 525R1), even when multiple distances are present, Angstrom resolution is achievable in such challenging protein classes.

(2) 'Based on the DEER data on the IDP-bound TmPPase, we observed significant deviations between the experimental and the in silico distances derived from the TmPPase:IDP X-ray structure for both cytoplasmic- (T211R1) and periplasmic-end (S525R1) sites (Figure 4D and Figure EV8D). This deviation could be explained by the dimer adopting an asymmetric conformation under the physiological conditions used for DEER, with one monomer in a closed state and the other in an open state.'

Problem: The authors are trying to establish asymmetry using the DEER data. Unfortunately, no significant difference is observed (between simulation and experiment) for position 525 as the authors claim (Figure 4D bottom panel). The observed difference for position 112 must be accounted for by the flexibility and the data provide no direct evidence for any asymmetry.

Reviewer 3 is wrong in suggesting that we are trying to prove asymmetry through the DEER data. That is a well-known fact in the literature (eg Vidilaseris et al, Sci Adv 2019 where we show (1) that the exit channel inhibitor ATC (i.e., close to 525) binds better in solution to the TmPPase:PPi complex than the TmPPase:PPi2 complex, and (2) that ATC binds in an asymmetric fashion to the TmPPase:IDP2 complex with just one ATC dimer on one of the exit channels. We merely use the DEER data to support this well-established fact.

However, we agree that the DEER data in presence of IDP does not provide direct proof for asymmetry; particularly mutant T211R1 yields in silico distributions too short for measurement by DEER. It is possible that the deviations observed (and particularly likely for T211R1) arise from conformational heterogeneity in solution. We will rephrase this paragraph accordingly: “Owing to the broad nature of the T211R1 (cytoplasmic site) distance distributions, we refrain from interpreting shifts in this data. For the 525R1 (periplasmic site) for which we obtained data of high quality (as also pointed out by both reviewers 2 and 3) we observed deviations between the experimental and the in-silico distances derived from the TmPPase:IDP X-ray structure. While this deviation is less pronounced than for the +ZTD condition, the deviation is consistent with an asymmetric conformation in solution.”

(3) 'Our new structures, together with DEER distance measurements that monitor the conformational ensemble equilibrium of TmPPase in solution, provide further solid experimental evidence of asymmetry in gating and transitional changes upon substrate/inhibitor binding.'

Problem: See above. The DEER data do not support any asymmetry.

We feel that the reviewer comments here are somewhat unfounded. The DEER data (and we will limit discussion only to the 525R1 mutant in this regard) satisfy relevant criteria of the white paper (Schiemann et al., 2021, JACS) from the EPR community (signal-to-noise ratio w.r.t modulation depth of > 20 in all cases; replicates have been performed and will be added into the main-text or supplementary; near quantitative labelling efficiency (evidenced by lack of free spin label signal in the CW-EPR spectra); analysed using the CDA (now Figure EV10, this data we will promote to the main-text) to avoid confirmation bias).

While the DEER data do not prove asymmetry, we do not claim proof of asymmetry in the above sentence. We concede to rephrase the offending sentence above as: “Our new structures, together with DEER distance measurements that monitor the conformational ensemble of TmPPase in solution, do not exclude asymmetry in gating and transitional changes upon substrate/inhibitor binding and are consistent with our proposed model.” We feel that this reframed conjecture of asymmetry is well founded; indeed, comparing the experimental apo-state 525R1 distance distribution with in-silico modelling performed on the hybridised asymmetric structure (i.e., comprised of one monomer bound to Ca2+ and another bound to IDP) yields an overlap coefficient (Islam and Roux, JPC B, 2015) of >0.97. This implies the envelope of the modelled distance distribution is quantitatively inside the envelope of the experimental distance distribution. Thus, the DEER data do not exclude asymmetry (previously observed by time-resolved XRC) in solution. While we appreciate that ideally one would measure time-resolved DEER to directly correlate kinetics of conformational changes within the ensemble to the catalytic cycle of mPPase,(and this is something we aim to do in the future), it is beyond the the scope of this study.

Indeed, half-of-the-sites reactivity has been demonstrated in at least the following papers (Vidilaseris et al, Sci Acv. ,2019, Strauss et al, EMBO Rep. 2024, Malinen et al Prot Sci, 2022, Artukka et al Biochem J, 2018; Luoto et al, PNAS, 2013). Half-of-the sites activity requires asymmetry in the mechanism, and therefore asymmetric motions in the active site (viz 211) and exit channel (viz 525). As mentioned above, we have demonstrated this for other inhibitors (Vidilaseris et al 2019) and as part of a time-resolved experiment (Strauss et al 2024). In fact, given the wealth of evidence showing that the symmetrical crystal structures sample a non- or less-productive conformation of the protein, it would be quixotic to propose the DEER experiments - in solution - do not generate asymmetric conformations. It certainly doesn’t obey Occam’s razor of choosing the simplest possible explanation that covers the data.

(4) Based on these observations, and the DEER data for +IDP, which is consistent with an asymmetric conformation of TmPPase being present in solution, we propose five distinct models of TmPPase (Figure 7).

Problem: Again, the DEER data do not support any asymmetry and the authors may revisit the proposed models.

We respectfully disagree with the reviewer. Please see our detailed response above. However, in the revised version, we will clarify that the proposed models are not solely based on the DEER data but are grounded in both current and previously solved structures, with the DEER data providing additional consistency with these models.

(5) 'In model 2 (Figure 7), one active site is semi-closed, while the other remains open. This is supported by the distance distributions for S525R1 and T211R1 for +Ca/ETD informed by DEER, which agrees with the in silico distance predictions generated by the asymmetric TmPPase:ETD X-ray structure'

Problem: Neither convincing nor supported by the data

We respectfully disagree with the reviewer. However, owing to the conformational heterogeneity of T211R1, in the revised version, we will exclude it in the above sentence, to the effect: Please see our detailed response above.

Author Response:

Thank you for your interest in our paper. We would also like to thank the anonymous reviewers for their critical and constructive comments. Although the reviewers found our work interesting, they raised several important concerns about our study. To address these concerns, mostly we will perform new experiments as following.

1. Examine whether antioxidant-NAC can block SFN-induced TFEB-nuclear translocation in NPC cells;

2. Examine whether calcineurin inhibitor (FK506+CsA) or Ca 2+ inhibitor (Bapta-AM) can block SFN-induced TFEB-nuclear translocation in NPC cells.

3. Investigate whether cholesterol was cleared by activation of TFEB by SFN in vivo tissues.

4. Investigate whether SFN-evoked the lysosomal exocytosis is TFEB-dependent by using TFEB-KO cells.

5. Examine the effect of NPC1 deficiency on dextran trafficking by studying the localization of CF- dex and Lamp1.

6. Perform cytotoxicity experiments to examine whether SFN used in this study is cytotoxic in various cell lines

In addition, according to the reviewers’ suggestions, we will make clarifications and corrections wherever appropriate in the manuscript. Below please find our point-by-point responses and plans to the reviewers’ comments.

Reviewer #1 (Public review):

Summary:

The authors are trying to determine if SFN treatment results in dephosphorylation of TFEB, subsequent activation of autophagy-related genes, exocytosis of lysosomes, and reduction in lysosomal cholesterol levels in models of NPC disease.

Strengths:

(1) Clear evidence that SFN results in translocation of TFEB to the nucleus.

(2) In vivo data demonstrating that SFN can rescue Purkinje neuron number and weight in NPC1-/- animals.

Thank you for the support!

Weaknesses:

(1) Lack of molecular details regarding how SFN results in dephosphorylation of TFEB leading to activation of the aforementioned pathways. Currently, datasets represent correlations.

Thank you for this constructive comment. The reviewer is right that in this manuscript the molecular mechanism of SFN-activated TFEB has not been discussed in details. Because previously we have shown that SFN induces TFEB nuclear translocation via a Ca 2+ - dependent but MTOR (mechanistic target of rapamycin kinase)-independent mechanism through a moderate increase in reactive oxygen species (ROS). And calcineurin-mediated TFEB dephosphorylation underlies SFN-induced TFEB activation. These data have been published in 2021 autophagy (Li, Shao et al. 2021) . Therefore, in this study we did not mention this part. We will add the molecular mechanism of TFEB activation by SFN in the discussion part. And to further confirm this mechanism in NPC cells, we will also perform experiments including: 1) examine whether antioxidant-NAC can block SFN-induced TFEB-nuclear translocation in NPC cells; 2) examine whether calcineurin inhibitor (FK506+CsA) can block SFN-induced TFEB-nuclear translocation in NPC cells.

(2) Based on the manuscript narrative, discussion, and data it is unclear exactly how steady-state cholesterol would change in models of NPC disease following SFN treatment. Yes, there is good evidence that lysosomal flux to (and presumably across) the plasma membrane increases with SFN. However, lysosomal biogenesis genes also seem to be increasing. Given that NPC inhibition, NPC1 knockout, or NPC1 disease mutations are constitutively present and the cell models of NPC disease contain lysosomes (even with SFN) how could a simple increase in lysosomal flux decrease cholesterol levels? It would seem important to quantify the number of lysosomes per cell in each condition to begin to disentangle differences in steady state number of lysosomes, number of new lysosomes, and number of lysosomes being exocytosed.

Thank you for the suggestion. It is important to define the three states 1) original number of lysosomes, 2) number of new lysosomes, and 3) number of lysosomes being exocytosis. However, we have checked literature, so far it seems that there is no good method that could clearly differentiate the three states of lysosomes.

(3) Lack of evidence supporting the authors' premise that "SFN could be a good therapeutic candidate for neuropathology in NPC disease".

Suggestion was taken! We will investigate whether cholesterol was reduced by activation of TFEB by SFN in vivo to strength the point that SFN could be a potential therapeutic compound for NPC treatment. And to avoid confusion, we have removed this sentence.

Reviewer #2 (Public review):

Summary:

This study presents a valuable finding that the activation of TFEB by sulforaphane (SFN) could promote lysosomal exocytosis and biogenesis in NPC, suggesting a potential mechanism by SFN for the removal of cholesterol accumulation, which may contribute to the development of new therapeutic approaches for NPC treatment.

Strengths:

The cell-based assays are convincing, utilizing appropriate and validated methodologies to support the conclusion that SFN facilitates the removal of lysosomal cholesterol via TFEB activation.

Weaknesses:

(1) The in vivo experiments demonstrate the therapeutic potential of SFN for NPC. A clear dose-response analysis would further strengthen the proposed therapeutic mechanism of SFN. Additional data supporting the activation of TFEB by SFN for cholesterol clearance in vivo would strengthen the overall impact of the study

We understand the reviewer’s point. We examined two doses of SFN-30 and 50mg/kg. As shown in Fig.6, SFN (50mg/kg), but not 30mg/kg prevents a degree of Purkinje cell loss in the lobule IV/V of cerebellum, suggesting a dose-correlated preventive effect of SFN. In vivo experiments with higher concentrations of SFN and optimized dosage form of SFN were planned in the future study, but will not be included in this study.

We will investigate whether cholesterol was cleared by activation of TFEB by SFN in vivo.

(2) In Figure 4, the authors demonstrate increased lysosomal exocytosis and biogenesis by SFN in NPC cells. Including a TFEB-KO/KD in this assay would provide additional validation of whether these effects are TFEB-dependent.

Thank you for this valuable suggestion. We will investigate whether SFN-evoked the lysosomal exocytosis is TFEB-dependent by using TFEB-KO cells.

(3) For lysosomal pH measurement, the combination of pHrodo-dex and CF-dex enables ratiometric pH measurement. However, the pKa of pHrodo red-dex (according to Invitrogen) is ~6.8, while lysosomal pH is typically around 4.7. This discrepancy may account for the lack of observed lysosomal pH changes between WT and U18666A-treated cells. Notably, previous studies (PMID: 28742019) have reported an increase in lysosomal pH in U18666A-treated cells.

We understand the reviewer’s point. But we used pHrodo™ Green-Dextran (P35368, Invitrogen), but not pHrodo red-dex to measure the lysosomal luminal acidity. According to the product information from Invitrogen, pHrodo Green-dex conjugates are non-fluorescent at neural pH, but fluorescence bright green at acidic pH ranges 4-9, such as those in endosomes and lysosomes. Therefore, pHrodo Green-dex can be used to monitor the acidity of lysosome (Hu, Li et al. 2022) . We also used LysoTracker Red DND-99 (Thermo Scientific, L7528) to measure lysosomal pH (Fig. 4G, H), which is consistent with results of pHrodo Green/CF measurement. Overall, in our hands, we have not detected pH change of lysosomes in U18666A-treated NPC1 cell models.

(4) The authors are also encouraged to perform colocalization studies between CF-dex and a lysosomal marker, as some researchers may be concerned that NPC1 deficiency could reduce or block the trafficking of dextran along endocytosis.

Suggestion was taken! We will examine the effect of NPC1 deficiency on dextran trafficking by studying the localization of CF-dex and Lamp1.

(5) In vivo data supporting the activation of TFEB by SFN for cholesterol clearance would significantly enhance the impact of the study. For example, measuring whole-animal or brain cholesterol levels would provide stronger evidence of SFN's therapeutic potential.

We really appreciate the reviewer’s suggestions. We will investigate whether cholesterol was cleared by activation of TFEB by SFN in vivo.

Reviewer #3 (Public review):

Summary:

The authors demonstrate that activation of TFEB facilitates cholesterol clearance in cell models of Niemann-Pick type C (NPC). This is done through a variety of approaches including activation of TFEB by sulforaphane (SFN), a naturally occurring small-molecule TFEB agonist. SFN induces TFEB nuclear translocation and promotes lysosomal exocytosis. In an NPC mouse model, SFN dephosphorylates/activates TFEB in the brain and rescues the loss of Purkinje cells.

Strengths:

NPC is a severe disease and there is little in the way of treatment. The manuscript points towards some treatment options. However, the title, the title "Small-molecule activation of TFEB Alleviates Niemann-Pick Disease..." is far too strong and should be changed.

Weaknesses:

(1) The manuscript is extremely hard to read due to the writing; it needs careful editing for grammar and English.

We will thoroughly check grammar to improve the manuscript.

(2) There are a number of important technical issues that need to be addressed.

We will address the technical issues mentioned in the following.

(3) The TFEB influence on filipin staining in Figure 1A is somewhat subtle. In the mCherry alone panels there is a transfected cell with no filipin staining and the mCherry-TFEBS211A cells still show some filipin staining.

We understand the reviewer’s point. We will investigate whether cholesterol is cleared by activation of TFEB by SFN in vivo.

(4) Figure 1C is impressive for the upregulation of filipin with U18666A treatment. However, SFN is used at 15 microM. This must be hitting multiple pathways. Vauzour et al (PMID: 20166144) use SFN at 10 nM to 1microM. Other manuscripts use it in the low microM range. The authors should repeat at least some key experiments using SFN at a range of concentrations from perhaps 100 nM to 5 microM. The use of 15 microM throughout is an overall concern.

We understand the reviewer’s point. See RESPONSE #1, previously we have shown that SFN (10–15 μM, 2–9 h) induces robust TFEB nuclear translocation in a dose- and time-dependent manner in HeLa GFP-TFEB stable cells as well as in other human cell lines without cytotoxicity (Li, Shao et al. 2021) . According to previous results, in this study, we chose SFN (15 μM) to examine its effect on cholesterol clearance. We will add the information in the discussion part. In this study, we will perform dose-response TFEB nuclear translocation in NPC model cells as well as cytotoxicity experiments to examine whether the concentrations of SFN used in various cell lines are toxic.

References:

Hu, M. Q., P. Li, C. Wang, X. H. Feng, Q. Geng, W. Chen, M. Marthi, W. L. Zhang, C. L. Gao, W. Reid, J. Swanson, W. L. Du, R. Hume and H. X. Xu (2022). "Parkinson's disease-risk protein TMEM175 is a proton-activated proton channel in lysosomes.” Cell 185(13): 2292-+.

Li, D., R. Shao, N. Wang, N. Zhou, K. Du, J. Shi, Y. Wang, Z. Zhao, X. Ye, X. Zhang and H. Xu (2021). “Sulforaphane Activates a lysosome-dependent transcriptional program to mitigate oxidative stress.” Autophagy 17(4): 872-887.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The work from Petazzi et al. aimed at identifying novel factors supporting the differentiation of human hematopoietic progenitors from induced pluripotent stem cells (iPSCs). The authors developed an inducible CRISPR-mediated activation strategy (iCRISPRa) to test the impact of newly identified candidate factors on the generation of hematopoietic progenitors in vitro. They first compared previously published transcriptomic data of iPSCderived hemato-endothelial populations with cells isolated ex vivo from the aorta-gonadmesonephros (AGM) region of the human embryo and they identified 9 transcription factors expressed in the aortic hemogenic endothelium that were poorly expressed in the in vitro differentiated cells. They then tested the activation of these candidate factors in an iPSCbased culture system supporting the differentiation of hematopoietic progenitors in vitro. They found that the IGF binding protein 2 (IGFBP2) was the most upregulated gene in arterial endothelium after activation and they demonstrated that IGFBP2 promotes the generation of functional hematopoietic progenitors in vitro.

Strengths:

The authors developed an extremely useful doxycycline-inducible system to activate the expression of specific candidate genes in human iPSC. This approach allows us to simultaneously test the impact of 9 different transcription factors on in vitro differentiation of hematopoietic cells, and the system appears to be very versatile and applicable to a broad variety of studies.

The system was extensively validated for the expression of 1 transcription factor (RUNX1) in both HeLa cells and human iPSC, and a detailed characterization of this test experiment was provided.

The authors exhaustively demonstrated the role of IGFBP2 in promoting the generation of functional hematopoietic progenitors in vitro from iPSCs. Even though the use of IGFBP2interacting proteins IGF1 and IGF2 have been previously reported in human iPSC-derived hematopoietic differentiation in vitro (Ditadi and Sturgeon, Methods 2016; Ng et al., Nature Biotechnology 2016), and IGFBP-2 itself has been shown to promote adult HSC expansion ex vivo (Zhang et al., Blood 2008), its role on supporting in vitro hematopoiesis was demonstrated here for the first time.

Weaknesses:

Although the authors performed a very thorough characterization of the system in proof-ofprinciple experiments activating a single transcription factor, the data provided when 9 independent factors were used is not sufficient to fully validate the experimental strategy. Indeed, in the current version of the manuscript, it is not clear whether the results presented in both the scRNAseq analysis and the functional assays are the consequence of the simultaneous activation of all 9 TF or just a subset of them. This is essential to establish whether all the proposed factors play a role during embryonic hematopoiesis, and a more complete analysis of the scRNAseq dataset could help clarify this aspect.

Similarly, the data presented in the manuscript are not sufficient to clarify at what stage of the endothelial-to-hematopoietic transition (EHT) the TF activation has an impact. Indeed, even though the overall increase of functional hematopoietic progenitors is fully demonstrated, the assays proposed in the manuscript do not clarify whether this is due to a specific effect at the endothelial level or to an increased proliferation rate of the generated hematopoietic progenitors. Similar conclusions can be applied to the functional validation of IGFBP2 in vitro.

The overall conclusions are sometimes vague and not always supported by the data. For instance, the authors state that the CRISPR activation strategy resulted in transcriptional remodeling and a steer in cell identity, but they do not specify which cell types are involved and at what level of the EHT process this is happening. In the discussion, the authors also claim that they provided evidence to support that RUNX1T1 could regulate IGFBP2 expression. However, this is exclusively based on the enrichment of RUNX1T1 gRNA in cells expressing higher levels of IGFBP2 and it does not demonstrate any direct or indirect association of the two factors.

We thank the reviewer for the positive comments about the importance of our work and have now addressed the points raised as weaknesses by performing additional analysis and experiments, adding a new schematic of the mechanism, and rewording our claims.

We have clarified the different effects mediated by the activation and the IGFBP2 addition in a summary section at the end of the results and added Figure 6, showing this in visual form. We have also clearly stated the limitations related to the correlation between RUNX1T1 and IGFBP2 in the discussion and toned down our claims regarding this throughout the entire paper. We have also reworded the text to clarify the specific cell types identified in the sequencing data that we refer to.

Reviewer #2 (Public Review):

To enable robust production of hematopoietic progenitors in-vitro, Petazzi et al examined the role of transcription factors in the arterial hemogenic endothelium. They use IGFBP2 as a candidate gene to increase the directed differentiation of iPSCs into hematopoietic progenitors. They have established a novel induced-CRISPR mediated activation strategy to drive the expression of multiple endogenous transcription factors and show enhanced production of hematopoietic progenitors through expansion of the arterial endothelial cells. Further, upregulation of IGFBP2 in the arterial cells facilitates the metabolic switch from glycolysis to oxidative phosphorylation, inducing hematopoietic differentiation. While the overall study and resources generated are good, assertions in the manuscript are not entirely supported by the experimental data and some claims need further experimental validation.

We thank the reviewer for the positive comments, and we have provided new data and analysis to make sure that all our assertations are clearly supported and also reworded those where limitations were identified by the reviewers.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

The assessment could change from "incomplete" to "solid" if the authors: i) improve data analysis (for both scRNAseq and functional assays) by providing additional information that could strengthen their conclusions, as suggested in the specific comments by both reviewers; ii) either provide new functional evidence supporting their mechanistic conclusion or alternatively tone down the claims that are not fully supported by data and acknowledge the limitations raised by reviewers in the discussion; (iii) the issue of paracrine signaling to expand only hematopoietic progenitors needs to be addressed.

We have now improved the data analysis and provided additional functional tests to strengthen our conclusions and toned down those that were identified by the reviewers as not supported enough and included a discussion on these limitations. We have also reworded the section about the paracrine signaling throughout the paper.

Reviewer #1 (Recommendations For The Authors):

Figure 1 contains exclusively published data. It might be more appropriate to use it as a supplementary figure or as part of a more exhaustive figure (maybe combining Figures 1 and 2 together?).

Figure 1 contained novel bioinformatic analyses that represent the base of our research and it has a different content and focus to figure 2, which is already a large figure. We therefore believe it is better to keep it as a separate figure, containing a new panel now too. 

It seems there is an issue with Figure S3 labelling:

• In line 112, Figure S2A-B does not display genomic PCR and sequencing results;

• In line 123, Figure S3D-E does not show viability and proliferation data;

• In line 127, Figure S3G does not show mCherry expression in response to DOX;

We apologies for the confusion with the numbers, we have now correctly labelled the figures.

It would be more informative to include gates and frequency on flow cytometry plots in Figure S3, to be able to evaluate the extent of the reduction in mCherry expression.

We have now included the gating and frequency of mCherry-expressing cells in Supplementary Figure 3D.

It is not clear from the text and figures whether the SB treatment was maintained throughout the hematopoietic differentiation protocol (line 122):

• If so, it would be important to confirm that HDAC treatment does not affect EHT cultures

• If not, can the authors provide some evidence that transgene silencing is not occurring during hematopoietic differentiation?

We have clarified that we decided to treat the cells with SB exclusively in maintenance condihons because HDACs have been shown to be essenhal for the EHT (lines 138-142). We have now also included addihonal data showing the high expression of the mCherry tag reporhng the iSAM expression on day 8 (Supplementary Figure 4F).

Can the authors provide a simple diagram summarizing the experimental strategy for each differentiation experiment in the respective supplementary figure? For instance, at what stage of the protocol was DOX added in Figure 3? Or at what stage IGFBP2 was added in Figure 5? It would be a very useful addition to the interpretation of the results.

We have now included three schemahcs for all the experiments in the manuscript in supplementary figure 4 A-C.

In Figure 3, the authors should provide more detailed information about the data filtering of the scRNAseq experiment, and more specifically:

• How many cells were included in the analysis for each library after QC and filtering?

• How "cells in which the gRNAs expression was detected" were selected? Do they include only cells showing expression of gRNAs for all 9 TF?

This informahon is now included in the method sechon lines 773-781; the detailed code is available on the GitHub link provided in the same sechon. We have filtered the cells expressing one gRNA for the non-targehng gRNA (iSAM_NT) control and more than one for the iSAM_AGM sample. 

In Figure 3A, it is not clear whether the expression of the 9 factors is consistently detected in all cells or just a subset of them, and the heatmap in Figure 3A does not provide this information. It would be more accurate to provide expression on a per-cell basis, for instance, as a violin plot displaying single dots representing each cell. 

We have now included this violin plot in Supplementary Figure 4G as requested. However, this visualisation is difficult to interpret because some of the target genes’ expression seems variable in both experimental and control conditions. We had envisaged that this could have been the case and so this is why we had included the three different controls.  For this reason we chose to show the normalised expression which takes all the different variables into account (Figure 3A). 

In Figure 3B-C, it seems that clusters EHT1 and EHT2 do not express endothelial markers anymore. Are these fully differentiated hematopoietic cells rather than cells undergoing EHT? In general, it would be quite important to provide evidence of expressed marker genes characterizing each cluster (eg. heatmap summarizing top DEG in the supplementary figure?). 

We have now provided a spreadsheet containing the clusters’ markers that we used in

Supplementary Table 1) a heatmap in Figure 3E. Furthermor,e we have now edited Figure 3C to include Pan Endothelial markers (PECAM1 and CDH5). These data show that the EHT1 and EHT2 cluster both express endothelial markers but are progressively downregulated as expected during endothelial to hematopoietic transition. We have also included and discussed this in the manuscript lines 192-195 and a schematic for the mechanism in Figure 6.

In Figure 3E, displaying the proportion of clusters within each sample/library would be a more accurate way of comparing the cell types present in each library (removing potential bias introduced by loading different numbers of cells in each sample).

We have now included the requested data in Supplementary Figure 4I and it confirms again the expansion of arterial cells in the activated cells.    

In Figure 3G, by plating 20,000 total CD34+, the assay does not account for potential differences in sample composition. It is then hard to discriminate between the increased number of progenitors in the input or an enhanced ability of HE to undergo EHT. This is an important aspect to consider to precisely identify at what level the activation of the 9 factors is acting. A proper quantification of flow cytometry data summarizing the % of progenitors, arterial cells, etc. would be useful to interpret these results.

Lines 204-205 reworded. We are very much aware of the fact that the CD34+ cell population consists of a range of cells across the EHT process and this is precisely why we carried out this single cell sequencing analyses.  We purposely tested the effect of the observed changes in composition by colony assays

In Figure 3G, it seems that NT cells w/o DOX have very little CFU potential (if any). Can the authors provide an explanation for this?

We think that the limited CFU potential is due to the extensive genetic manipulation and selection that the cells underwent for the derivation of all the iSAM lines but this did not impede us from observing an effect of gene activation on CFU numbers. This is one of the primary reasons that we then validated our overall findings using the parental iPSC line in control condition and with the addition of IGFBP2. We show that the parental iPSC line gives rise to hematopoietic progenitor, both immunophenotypically (Figure 4D) and functionally, at expected levels (Figure 4B left column).

Figure 4A shows an upregulation of IGFBP2 in arterial cells as a result of TF activation. However, from the data presented here, it is not possible to evaluate whether this is specific to the arterial cluster, or it is a common effect shared by all cell types regardless of their identity. 

Data has now been included in Supplementary Figure 4H, which shows that all the cells show an increase in IGFBP2, but arterial cells show the highest increase. We have now edited the text to reflect this, in lines 228-230.

In Figure 5A-B only a minority of arterial cells express RUNX1 in response to IGFBP2 treatment. Is this sufficient to explain the very significant increase in the generation of functional hematopoietic progenitors described in Figure 4? Quantification and statistical analysis of RUNX1 upregulation would strengthen this conclusion.

We have now provided the statistical analysis showing significant upregulation of RUNX1 upon IGFBP2 addition. The p values are now provided in the figure 5 legend.

In Figure 5 the authors conclude that IGFBP2 remodels the metabolic profile of endothelial cells. However, it is not clear which cell types and clusters were included in the analysis of Figure 5C-G. Is the switch from Glycolysis to Oxidative Phosphorylation specific to endothelial cells? Or it is a more general effect on the entire culture, including hematopoietic cells? 

We based this conclusion on the fact that the single-cell RNAseq allows to verify that the metabolic differences are obtained in the endothelial cells. Given that we sorted the adherent cells, the majority of these are endothelial cells as shown in Figure 5A. The Seahorse pipeline includes a number of washing steps resulting in the analyses being performed on the adherent compartment which we know consists primarily of endothelial cells. We cannot exclude some contamination from non-endothelial cells but we highlight to this reviewer that the initial observation of the metabolic changes was identified in endothelial cells in the single cell sequencing data. Taken together, we believe that this implies that metabolic changes are specific to this population. We have clarified this in the line 317.

In the discussion, the authors conclude that they "provide evidence to support the hypothesis that RUNX1T1 could regulate IGFBP2 expression". To further support this conclusion, the authors could provide a correlation analysis of the expression of the two genes in the cell type of interest. 

Following the observation of the IGFBP2 high expression across clusters, we have now reworded this sentence in lines 382-385  We have tried to perform the correlation analysis but we believe this not to be appropriate due to the detection level of the gRNA, we have now included this as a limitation point in the discussion lines 416-427, and also toned down the conclusion we did draw about RUNX1T1 throughout the whole manuscript.

As mentioned by the authors, IGFBP2 binds IGF1 and IGF2 modulating their function. Both IGF1 (http://dx.doi.org/10.1016/j.ymeth.2015.10.001) and IGF2 (doi:10.1038/nbt.3702) have been used in iPSC differentiation into definitive hematopoietic cells. It would be relevant to discuss/reference this in the discussion.

We have now included the suggested reference in the section where we discuss the role of IGFBP2 in binding IGF1 and IGF2.

Reviewer #2 (Recommendations For The Authors):

(1) Figure 1 compares the transcriptome of human AGM and in-vitro derived hemogenic endothelial cells (HECs). It is not clear why only the genes downregulated in the latter were chosen. Are there any significantly upregulated genes, knockdown/knockout which could also serve a similar purpose? Single-cell transcriptome database analysis is very preliminary. A detailed panel with differences in cluster properties of HECs between the two systems should be provided. A heatmap of all differentially expressed genes between the two samples must be generated, along with a logical explanation for choosing the given set of genes. 

We have now included another panel in figure 1 to better clarify the logic behind the strategy used to identify our target genes (Figure 1A).

(2) Figure 2 - a panel describing the workflow of gRNA design and targeting for the 9 candidate genes, along with lentiviral packaging and transduction would make it easier to follow. 

We have now included three schematics for all the experiments in the manuscript in supplementary figure 4 A-C. 

(3) Figure 3- to assess the effect of arterial cell expansion on the emergence of hematopoietic progenitors, CD34+ Dll4+ cells should be sorted for OP9 co-culture assay.

Using only CD34+ cells does not answer the question raised. Also, the CFU assay performed does not fully support the claim of enhanced hematopoietic differentiation since only CFU-E and CFU-GM colonies are increased in Dox-treated samples, with no effect on other colony types. OP9 co-culture assay with these cells would be required to strengthen this claim. 

We wanted to clarify that the effect on the methylcellulose coming from the activated cells was not limited to CFU-E, as the reviewer reported; instead, it also affected CFU-GM and CFU-M. 

We have now performed additional experiments where we sorted the CD34+ compartment into DLL4- and DLL4+ in Supplementary Figure 5D-E, which we discussed in lines 250-258. 

(4) In Figure 3F, there appears to be a lot of variation in the DLL4% fold change values for

DOX treated iSAM_AGM sample, which weakens the claim of increased arterial expansion.

Can the authors explain the probable reason? It is suggested that the two other controls (iSAM_+DOX and iSAM_-DOX) should be included in this analysis. It is imperative to also show % populations rather than just fold change to gain confidence.

We agree that there is a lot of variability. That is because differentiation happens in 3D in embryoid bodies, which contain many different cell types that differentiate in different proportions across independent experiments. We have now included the raw data in Supplementary Figure 4 D, with additional statistical analysis to show the expansion of arterial cells including also the suggested additional controls.

(5) How does activation of these target genes cause increased arterialization? Is the emergence of non-HE populations suppressed? Or is it specific to the HE? The data on this should be clarified and also discussed. ANTO/Lesley text

We have provided additional data clarifying the connection between increased arterialisation and hemogenic potential. We showed that the activation induces increased arterialisation and that IGFBP2 acts by supporting the acquisition of hemogenic potential. We have discussed this in lines 326-348 and provided a new figure to explain this in detail (figure 6)

(6) Considering that IGFBP2 was chosen from the activated target gene(s) cluster, can the authors explain why the reduced CFU-M phenomenon observed in Figure 3G does not appear in the MethoCult assay for IGFBP2 treated cells (Figure 4B)?

The difference could be explained by the fact that in Figure 3G, the cells underwent activation of multiple genes, while in Figure 4B, they were only exposed to IGFBP2. Our results show that IGFBP2 could at least partially explain the phenotype that we see with the activation, but we believe that during the activation experiments, there might be other signals available that might not be induced by IGFBP2 alone. We have also added a summary section and a figure to clarify the different mechanisms of action of the gene activation and IGFBP2.

(7) Figure 4- while the experiments conducted support the role of IGFBP2 in increasing hematopoietic output, there is no experimental evidence to prove its function through paracrine signalling in HECs. The authors need to provide some evidence of how IGFBP2 supplementation specifically expands only the hematopoietic progenitors. Experimental strategies involving specifically targeting IGFBP2 in hemogenic/arterial endothelial cells are required to prove its cell type specific function. Additionally, assessing the in vivo functional potential of the hematopoietic cells generated in the presence of IGFBP2, by bone-marrow transplantation of CD34+ CD43+ cells, is essential. 

The role of IGFBP2 in the context of HSC production and expansion was not the topic of our research, and we have not claimed that IGFBP2  affects the long-term repopulating capacity of HSPCs. Therefore, we believe that the requested experiments are not required to support the specific claims that we do make. We have now provided more experiments and bioinformatic analysis that support the role of IGFBP2 in inducing the progression of EHT from arterial cells to hemogenic endothelium, and to avoid misunderstandings, we have toned down our claims by editing the text regarding its paracrine effect s. 

(8) Figure 4C-D -It is recommended to plot % populations along with fold change value. As this is a key finding, it is important to perform flow cytometry for additional hematopoietic markers- CD144, CD235a and CD41a to demonstrate whether this strategy can also expand erythroid-megakaryocyte progenitors. Telma

Figure 4C already shows the percentage values; we have now added the percentage for Figure 4D in SF5C. We have also performed additional analysis as requested and added the data obtained to Supplementary Figure 5D.

(9) In Figure 5, analysis showing the frequency of cells constituting different clusters, between untreated and IGFBP2-treated samples in the single-cell transcriptome analysis is essential. Additional experiments are required to validate the function of IGFBP2 through modulation of metabolic activity. Inhibition of oxidative phosphorylation in the IGFBP2treated cells should reduce the hematopoietic output. Authors should consider doing these experiments to provide a stronger mechanistic insight into IGFBP2-mediated regulation of hematopoietic emergence.

We have now included the requested cluster composition in Supplementary Figure 5F. We decided not to include further tests on the metabolic profile of IGFBP2 as we already discussed in other papers that showed, using selective inhibitors, that the EHT coincides with a glycol to OxPhos switch. 

(10) It is very striking to see that IGFBP2 supplementation changes the transcriptional profile of developing hematopoietic cells by increasing transcription of OXPHOS-related genes with concomitant reduction of glycolytic signatures, particularly at Day 13. However, the mitochondrial ATP rate measurements do not seem convincing. The bioenergetic profiles show that when mitochondrial inhibitors are added, both groups exhibit decreased OCR values and, on the other hand, higher ECAR. This indicates that both groups have the capability to utilize OXPHOS or glycolysis and may only differ in their basal respiration rates.

Differences in proliferation rate can cause basal respiration to change. There is no information on how the bioenergetic profile was normalized (cell no./protein amount). Given that IGFBP2 has been shown to increase proliferation, it is very likely that the cells treated with IGFBP2 proliferated faster and therefore have higher OCR. The data needs to be normalized appropriately to negate this possibility.

We have previously tested whether IGFBP2 causes an increase in proliferation by analysing the cell cycle of cells treated with it, as we initially thought this could be a mechanism of action. We have now provided the quantification of the cell cycle in the cells treated with IGFBP2, showing no effect was observed in cell cycle Supplementary Figure 4E. Following this analysis, we decided to plate the same number of cells and test their density under the microscope before running the experiment; each experiment was done in triplicate for each condition. We have now added this info to the method sections lines 806-813.  We did not comment on the basal difference, which we agree might be due to several factors, but we only compared the difference in response to the inhibitors, which isn’t affected by the basal level but exclusively by their D values. We have also included the formulas used to calculate the ATP production rate.

Overall, it appears that IGFBP2 does not seem to primarily cause metabolic changes, but simply accelerates the metabolic dependency on OXPHOS. Hence, the term 'metabolic remodelling' must be avoided unless IGFBP2 depletion/loss of function analysis is shown.

We thank the reviewer for suggesting how to interpret the data about the dependency on OXPHOS. We have now changed the conclusions and claims about the effect of IGFBP2. We have also included a cell cycle analysis of the hematopoietic cells derived upon IGFBP2 addition to show that they don’t show differences in proliferation that could cause the increase in colony formation we observed. Regarding the assay, we have plated the same number of cells for each group to make sure we were comparing the same number of cells, which we also assessed in the microscope before the test, and we eliminated the suspension cells during the washes that preceded the measurement. The review is correct in indicating that there is a basal difference in the value of OCR and ECAR where the IGFBP2 is lower at the start and not higher, which would not conceal higher proliferation. Finally, the ATP production rate is calculated on the variation of OCR and ECAR upon the addition of inhibitors, which normalizes for the basal differences.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Summary:

In this manuscript, the molecular mechanism of interaction of daptomycin (DAP) with bacterial membrane phospholipids has been explored by fluorescence and CD spectroscopy, mass spectrometry, and RP-HPLC. The mechanism of binding was found to be a two-step process. A fast reversible step of binding to the surface and a slow irreversible step of membrane insertion. Fluorescence-based titrations were performed and analysed to infer that daptomycin bound simultaneously two molecules of PG with nanomolar affinity in the presence of calcium. Conformational change but not membrane insertion was observed for DAP in the presence of cardiolipin and calcium.

Strengths:

The strength of the study is skillful execution of biophysical experiments, especially stoppedflow kinetics that capture the first surface binding event, and careful delineation of the stoichiometry.

Weaknesses:

The weakness of the study is that it does not add substantially to the previously known information and fails to provide additional molecular details. The current study provides incremental information on DAP-PG-calcium association but fails to capture the complex in mass spectrometry. The ITC and NMR studies with G3P are inconclusive. There are no structural models presented. Another aspect missing from the study is the reconciliation between PG in the monomer, micellar, and membrane forms.

Besides the two-stage process, another important finding in the current work is the stable complex that plays a critical role in the drug uptake both in vitro and in B. subtilis. This complex has been shown to be a stable species in HPLC and its binding stoichiometry and affinity have been quantitatively characterized. The complex may not be stable enough in gas phase to be detected in the MS analysis, which was designed to detect the phospholipid and Dap components, not the complex itself. The structural model of this complex is clearly proposed and presented in Figure 6. 

The NMR and ITC studies have a very clear conclusion that Dap has a weak interaction with the PG headgroup alone, which is unable to account for the Dap-PG interaction observed in the fluorescence studies. Thus, the whole PG molecule has to be involved in the interaction, leading to the discovery of the stable complex.  

Reviewer #2 (Recommendations For The Authors):

(1) I appreciate and agree with the comment that there are stages of daptomycin insertion, and these might involve the formation of different complexes with different binding partners (e.g. pre-insertion vs quaternary vs bactericidal). However, it seems like lipid II is an apparent participant in daptomycin membrane dynamics (Grein et al. Nature Communications 2020). It's not clear why this was excluded from analysis by the authors, or what basis there is for the discussion statement that the quaternary complex can shift into the bactericidal complex by exchanging 1 PG for lipid II. 

We agree that lipid II and other isoprenyl lipids may be involved in the uptake and insertion of daptomycin into membrane according to the results of the Nat. Comm. paper. However, these isoprenyl lipids are very small components of the membrane in comparison to PG and their contribution to the drug uptake is thus expected to be much less significant. Nonetheless, we included farnesyl pyrophosphate (FPP) as an analog of bactoprenol pyrophosphate (C55PP), which was reported to have the same promoting effect as lipid II in the previous study, in our study but found no promoting effect in the fluorescence assay (Fig. 2B). In addition, no complex was formed when FPP replaced PG in our preparation and analysis of the drug-lipid complex. In consideration of these negative results and the expected small contribution, other isoprenyl lipids or their analogs were not included in the study.

The statement of forming the proposed bactericidal complex from the identified complex is a speculation that is possible only when lipid II has a higher affinity for Dap than a PG ligand. To avoid confusion, we deleted the sentence’ in the revision. 

(2) The detailed examination of daptomycin dynamics, particularly on the millisecond scale, in this paper is ideal for characterizing the effect of lipid II on daptomycin insertion. It would be helpful to either include lipid II in some analyses (micelle binding, fluorescence shifts, CD) or at least address why it was excluded from the scope of this work.

As mentioned in the response to the first comment, we did not exclude isoprenyl lipids in our study but used some of their analogs in the fluorescence assay. Besides FPP mentioned above, we also tested geranyl pyrophosphate and geranyl monophosphate but obtained the same negative results. Lipid II was not directly used because it is one of the three isoprenyl lipids reported to have the same promoting effects in the Nat. Comm. paper and also because its preparation is not easy. Even if lipid II were different from other isoprenyl lipids in promoting membrane binding, its contribution is likely negligible at the reversible stage compared to the phospholipids because of its minuscule content in bacterial membrane. This is the main reason we did not use the isoprenyl lipids in the fast kinetic study (this stage only involves reversible binding, not insertion). 

(3) Grein et al. 2020 saw that PG did not have a strong effect on daptomycin interaction with membranes. I believe this discrepancy is more likely due to the complex physical parameters of supported bilayers versus micelles/vesicles or some other methodological variable, but if the authors have more insight on this, it would be valuable commentary in the discussion.

We totally agree that the discrepancy is likely due to the different conditions in the assays. It is hard to tell exactly what causes the difference. Thus, we did not attempt to comment on the cause of this difference in the discussion.

(4) Isolation of the daptomycin complex from B. subtilis cells clearly had different traces from the in vitro complex; is it possible that lipid II is present in the B. subtilis complex? If not, a time-course extraction could be useful to support the model that different complexes have different activities. Isolates from early-stage incubation with daptomycin may lack lipid II but isolates from longer incubations may have lipid II present as the complex shifts from insertion to bactericidal.

From the day we isolated the complex from B. subtilis, we have been looking for evidence for the previously proposed lipid complexes containing lipid II or other isoprenyl lipids but have not been successful. We did not see any sign of lipid II or other isoprenyl lipids in the MALDI or ESI mass spectroscopic data. The minute peaks in the HPLC traces are not the expected complexes in separate LC-MS analysis. However, this does not mean that such complexes are not present in the isolated PG-containing complex because: (1) the amount of such complexes may be too small to be detected due to the low content of the isoprenyl lipids; (2) the isoprenyl lipids, particularly lipid II, are not easily ionizable due to their size and unique structure for detection in mass spectrometry. 

We don’t think the drug treatment time is the reason for the failure in detecting lipid II or other isoprenyl lipids. In our reported experiment, the cells were treated with a very high dose of Dap for 2 hours before extraction. In a separate experiment done recently, we treated B. subtilis at 1/3 of the used dose under the same condition and found all treated cells were dead after 1 hour in a titration assay, consistent with the results from reported time-killing assays in the literature. From this result, the proposed bactericidal lipid-containing complex should have been formed in the treated cells used in our extraction and isolated along with the PG-containing complex. It was not detected likely due to the reasons discussed above. To avoid the interference of the PG-containing complex, a large amount of bacterial cells might have to be treated at a low dose to isolate enough amount of the lipid II-containing complex for identification. However, isolation or identification of the lipid II-containing complex is outside the scope of the current investigation and is therefore not pursued. 

(5) Part of the daptomycin mechanism of interacting with bacterial membranes involves the flipping of daptomycin from one leaflet to another. There was some mentioned work on the consistency of results between micelles and vesicles, but the dynamics or existence of a flipping complex in the bilayer system wasn't addressed at all in this paper.

The current investigation makes no attempt to solve all problems in the daptomycin mode of action and is limited to the uptake of the drug, up to the point when Dap is inserted into the membrane. Within this scope, flipping of the complex is not yet involved and is thus irrelevant to the study. How the complex is flipped and used to kill the bacteria is what should be investigated next.  

(6) The authors mention data with phosphatidylethanolamine in the text, but I could not find the data in the main or supplemental figures. I recommend including it in at least one of the figures.

It is much appreciated that this error is identified. The POPE data was lost when the graphic (Fig. 2B) was assembled in Adobe to create Figure 2. We re-draw the graphic and reassemble the figure to solve this problem. Fig. 2B has also been modified to use micromolar for the concentration of the lipids.

(7) Readability point: I'd suggest some consistency in the concentrations mentioned. Making the concentrations either all molar-based or all percentage-based would make comparison across figures easier.

As suggested, we have changed the % into micromolar concentrations in Fig. 2B and also in Fig. 3A. 

(8) The model figure is quite difficult to interpret, particularly the final stage of the tail unfolding. I recommend the authors use a zoomed-in inset for this stage, or at least simplify the diagram by removing the non-participating lipid structures. The figure legend for the model figure should also have a brief description of the events and what the arrows mean, particularly the POPS PG arrow in the final panel of the figure. I am assuming here the authors are implying that daptomycin can transiently interact with one lipid species and move to another, but the arrow here suggests that daptomycin is moving through the lipid headgroup space.

We really appreciate the suggestions. As suggested, we put an inset to show the preinsertion complex more clearly. In addition, we have removed the green arrows originally intended to show the re-organization/movement of the phospholipids. Moreover, the legend is changed to ‘Proposed mechanism for the two-phased uptake of Dap into bacterial membrane. In the first phase, Dap reversibly binds to negative phospholipids with a hidden tail in the headgroup region, where it combines with two PG molecules to form a pre-insertion complex. In the second phase, the hidden tail unfolds and irreversibly inserts into the membrane. The inset shows the headgroup of the pre-insertion complex with the broad arrow showing the direction for the unfolding of the hidden tail. The red dots denote Ca2+.’  

(9) The authors listed the Kd for daptomycin and 2 PG as 7.2 x 10-15 M2. Is this correct? This is an affinity in the femtomolar range.

Please note that this Kd is for the simultaneous binding of two PG molecules, not for the binding of a single ligand that we usually refer to. Assuming that each PG contributes equally to this interaction, the binding affinity for each ligand is then the squared root of 7.2 x 10-15 M2, which equals to 8.5 x 10-8 M. This is equivalent to a nanomolar affinity for PG and is a reasonably high affinity.

Reviewer #3 (Recommendations For The Authors):

(1) The authors reported an increase in daptomycin intensity with the increasing amount of negatively charged DMPG. A similar observation has been reported for GUVs, however, the authors did not refer to this paper in their manuscript: E. Krok, M. Stephan, R. Dimova, L. Piatkowski, Tunable biomimetic bacterial membranes from binary and ternary lipid mixtures and their application in antimicrobial testing, Biochim. Biophys. Acta - Biomembr. 1865 (2023) [1]. This paper is also consistent with the authors' observation that there is negligible fluorescence detected for the membranes composed of PC lipids upon exposure to the Dap treatment.

As suggested, this paper is cited as ref. 29 in the revision by adding the following sentence at the end of the section ‘Dependence of Dap uptake on phosphatidylglycerol.’: ‘PG-dependent increase of the steady-state fluorescence was also observed in giant unilamellar vesicles (GUVs).29’. The numbering is changed accordingly for the remaining references.  

(2) Please include the plot of the steady-state Kyn fluorescence vs the content of POPA (Figure 2C shows traces for DMPG, CL, and POPS). Both POPA and POPS lipids are negatively charged, however, POPS seems to interact with Dap, while POPA does not. In my opinion, this observation is really interesting and might deserve a more thorough discussion. The authors might want to describe what could be the mechanism behind this lipid-specific mode of binding.

As suggested, a plot is now added for POPA in Fig. 2C, which is basically a flat line without significant increase for the Kyn fluorescence. Indeed, the different effect of the negative phospholipids is very interesting, indicating that the reversible binding of Dap to the lipid surface is dependent not only on the Ca2+-mediated ionic interaction but also the structure of the headgroup. In other words, Dap recognizes the phospholipids at the surface binding stage. Considering this headgroup specificity, the last sentence in the second paragraph in “Discussion’ is changed from ‘In addition, due to the low lipid specificity, this reversible binding likely involves Ca2+-mediated ionic interaction between Dap and the phosphoryl moiety of the headgroups.’ to ‘In addition, due to the specificity for negative phospholipids (Fig. 2B and 2C), this reversible binding of Dap likely involves both a nonspecific Ca2+-mediated ionic interaction and a specific interaction with the remaining part of the headgroups.’

(3) The authors write that they propose a novel mechanism for the Ca2+-dependent insertion of Dap to the bacterial membrane, however, they rather ignored the already published findings and hypotheses regarding this process. In fact the role of Ca2+, as well as the proposed conformational changes of Dap, which allow its deeper insertion into the membrane are well known:

The role of Ca2+ ions in the mechanism of binding is actually three-fold: (i) neutralization of daptomycin charge [2], (iii) creating the connection between lipids and daptomycin and (iii) inducing two daptomycin conformational changes. It should be noted that the interactions between calcium ions and daptomycin are 2-3 orders of magnitude stronger than between daptomycin and PG lipids [3,4]. Thus, upon the addition of CaCl2 to the solution, the divalent cations of calcium bind preferentially to the daptomycin, rather than to the negatively charged PG lipids, which results in the decrease of daptomycin net negative charge but also leads to its first conformational change [4]. Upon binding between calcium ions and two aspartate residues, the area of the hydrophobic surface increases, which allows the daptomycin to interact with the negatively charged membrane. In the next step, Ca2+ acts as a bridge connecting daptomycin with the anionic lipids. This event leads to the second conformational change, which enables deeper insertion of daptomycin into the lipid membrane and enables its fluorescence [4]. The overall mechanism has a sequential character, where the binding of daptomycin-Ca2+ complex to the negatively charged PG (or CA) occurs at the end.

The authors should focus on emphasizing the novelty of their manuscript, keeping in mind the already published paper.

We agree with the comments on the three general roles of calcium ion in the Dap interaction with membrane. The current investigation does not ignore the previous findings, which involve many more works than mentioned above, but takes these findings as common knowledge. Actually, the role of calcium ion is not the focus of current work. Instead, the current work focuses on how the drug is taken up and inserted into the membrane in the presence of the ion and how its structure changes in this process. With the known roles of calcium ion in mind, we propose an uptake mechanism (Fig. 6) that shows no conflict with the common knowledge.

We would like to point out that the ‘deeper insertion into the membrane’ in the comment is different from the membrane insertion referred to in our manuscript. This ‘deeper insertion’ still remains in the reversible stage of binding to the membrane surface because all negative phospholipids can do this (causing a conformational change and fluorescence increase, as quantified in Fig.2C) but now we know that only PG can enable irreversible membrane insertion because of our work. In addition, the comment that calcium binding to daptomycin causes first conformational change is not supported by our finding that no conformational change is found for Dap in the presence of calcium in a lipid-free environment (Fig. 3B). One important aspect of novelty and contribution of our work is to clear up some of these ambiguities in the literature. Another contribution of our work is to demonstrate the formation of a stable complex between Dap and PG with a defined stoichiometry and its crucial role in the drug uptake. 

(4) One paragraph in the section "Ca2+- dependent interaction between Dap and DMPG" is devoted to a discussion of the formation of precipitate upon extraction of DMPG-containing micelles, exposed to Dap in the calcium-rich environment. Contrary, in the absence of Dap, no precipitate was detected. The authors did not provide any visual proof for their statement. Please include proper photographs in the supplementary information.

The precipitate formed upon extraction of the DMPG-containing micelles was too little to be visually identifiable but could be collected by centrifugation and detected by fluorescence or HPLC after dissolving in DMSO. For visualization, we show below the precipitate formed using higher amount of Dap and DMPG. The Dap-DMPG-Ca2+ complex (left tube) was formed by mixing 1 mM Dap, 2 mM DMPG and 1 mM Ca2+ and the control (right tube) was a mixture of 2 mM DMPG and 1 mM Ca2+. This is now added as Fig. S7 in the supplementary information (the index is modified accordingly) and cited in the main text.

(5) The authors wrote that it is not clear how many calcium ions are bound to Dap-2PG complex (page 11, Discussion section). There are already reports discussing this issue. I recommend citing the paper discussing that exactly two Ca2+ ions bind to a single Dap molecule: R. Taylor, K. Butt, B. Scott, T. Zhang, J.K. Muraih, E. Mintzer, S. Taylor, M. Palmer, Two successive calcium-dependent transitions mediate membrane binding and oligomerization of daptomycin and the related antibiotic A54145, Biochim. Biophys. Acta - Biomembr. 1858, (2016) 1999-2005 [5]

We were aware of the cited work that shows binding of two Ca2+ but also noted that there are more works showing one Ca2+ in the binding, such as the paper in [Ho, S. W., Jung, D., Calhoun, J. R., Lear, J. D., Okon, M., Scott, W. R. P., Hancock, R. E. W., & Straus, S. K. (2008), Effect of divalent cations on the structure of the antibiotic daptomycin. European Biophysics Journal, 37(4), 421–433.]. That was the reason we said ‘it is not clear how many calcium ions are bound to Dap-2PG complex’. Now, both papers are cited (as Ref. #33, 34) to support this statement.

(6) The authors wrote two contradictory statements:

-  PG cannot be found in mammalian cell membranes:

"Moreover, the complete dependence of the membrane insertion on PG also explains why Dap selectively attacks Gram-positive bacteria without affecting mammalian cells, because PG is present only in bacterial membrane but not in mammalian membrane. " (Page 10, Discussion section, last sentence of the first paragraph)

"However, Dap absorbed on bacterial surface is continuously inserted into the acyl layer via formation of complex with PG in a time scale of minutes, whereas no irreversible insertion of Dap occurs on mammalian membrane due to the absence of PG while the bound Dap is continuously released to the circulation as the drug is depleted by the bacteria." (Page 13, Discussion section)

-  PG in trace amounts is present in mammalian membranes:

"The proposed requirement of the pre-insertion quaternary complex increases the threshold of PG content for the membrane insertion to happen and thus makes it impossible on the surface of mammalian cells even if their plasma membrane contains a trace amount of PG." (Page 13, Discussion section).

In fact, phosphatidylglycerol comprises 1-2 mol% of the mammalian cell membranes. Please, correct this information, which in this form is misleading to the readers.

We appreciate the comments about the PG content in mammalian cells. Changes are made as listed below:

(1) p10, the sentence is changed to ‘Moreover, the complete dependence of the membrane insertion on PG also explains why Dap selectively attacks Gram-positive bacteria without affecting mammalian cells, because PG is a major phospholipid in bacterial membrane but is a minor component in mammalian membrane.’ 

(2) p13, the sentence is changed to ‘However, Dap absorbed on bacterial surface is continuously inserted into the acyl layer via formation of complex with PG in a time scale of minutes, whereas little irreversible insertion of Dap occurs on mammalian membrane due to the low content of PG while the bound Dap is continuously released to the circulation as the drug is depleted by the bacteria.’

(3) p13, another sentence is modified to ‘The proposed requirement of the pre-insertion quaternary complex increases the threshold of PG content for the membrane insertion to happen and thus makes it less likely on the surface of mammalian cells that contain PG at a low level in the membrane.’ 

(7) Please include information that Dap is effective only against Gram-positive bacteria and does not show antimicrobial properties against Gram-negative strains. The authors focused on emphasizing that Dap does not affect mammalian membranes, most likely due to the low PG content, however even membranes of Gram-negative bacteria are not susceptible to the Dap, despite the relatively high content of negatively charged PG in the inner membrane (e.g. inner cell membrane of E. coli has ~20% PG).

The requested information is already included in ‘Introduction’. In this part, Dap is introduced to be only active against Gram-positive bacteria, implicating that it is not active against Gram-negative bacteria. The reason Dap is inactive against E. coli or other Gramnegative bacteria is because the outer membrane prevents the antibiotic from accessing the PG in the inner membrane to cause any harm. When the outer membrane is removed, Dap will also attack the plasma membrane of Gram-negative bacteria. 

Literature cited in the comments:

(1) E. Krok, M. Stephan, R. Dimova, L. Piatkowski, Tunable biomimetic bacterial membranes from binary and ternary lipid mixtures and their application in antimicrobial testing, Biochim. Biophys. Acta - Biomembr. 1865 (2023). https://doi.org/10.1101/2023.02.12.528174.

(2) S.W. Ho, D. Jung, J.R. Calhoun, J.D. Lear, M. Okon, W.R.P. Scott, R.E.W. Hancock, S.K. Straus, Effect of divalent cations on the structure of the antibiotic daptomycin, Eur. Biophys. J. 37 (2008) 421-433. https://doi.org/10.1007/S00249-007-0227-2/METRICS.

(3) A. Pokorny, P.F. Almeida, The Antibiotic Peptide Daptomycin Functions by Reorganizing the Membrane, J. Membr. Biol. 254 (2021) 97-108. https://doi.org/10.1007/s00232-02100175-0.

(4) L. Robbel, M.A. Marahiel, Daptomycin, a bacterial lipopeptide synthesized by a nonribosomal machinery, J. Biol. Chem. 285 (2010) 2750127508. https://doi.org/10.1074/JBC.R110.128181.

(5) R. Taylor, K. Butt, B. Scott, T. Zhang, J.K. Muraih, E. Mintzer, S. Taylor, M. Palmer, Two successive calcium-dependent transitions mediate membrane binding and oligomerization of daptomycin and the related antibiotic A54145, Biochim. Biophys. Acta - Biomembr. 1858 (2016) 1999-2005. https://doi.org/10.1016/J.BBAMEM.2016.05.020.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work used a comprehensive dataset to compare the effects of species diversity and genetic diversity within each trophic level and across three trophic levels. The results showed that species diversity had negative effects on ecosystem functions, while genetic diversity had positive effects. These effects were observed only within each trophic level and not across the three trophic levels studied. Although the effects of biodiversity, especially genetic diversity across multi-trophic levels, have been shown to be important, there are still very few empirical studies on this topic due to the complex relationships and difficulty in obtaining data. This study collected an excellent dataset to address this question, enhancing our understanding of genetic diversity effects in aquatic ecosystems.

Strengths:

The study collected an extensive dataset that includes species diversity of primary producers (riparian trees), primary consumers (macroinvertebrate shredders), and secondary consumers (fish). It also includes the genetic diversity of the dominant species at each trophic level, biomass production, decomposition rates, and environmental data.

The conclusions of this paper are mostly well supported by the data and the writing is logical and easy to follow.

Weaknesses:

(1) While the dataset is impressive, the authors conducted analyses more akin to a "meta-analysis," leaving out important basic information about the raw data in the manuscript. Given the complexity of the relationships between different trophic levels and ecosystem functions, it would be beneficial for the authors to show the results of each SEM (structural equation model).

We understand the point raised by the reviewer. We now provide individual SEMs (Figure 3), although we limit causal relationships to those for which the p-value was below 0.2 for the sake of graphical clarity. We also provide the percentage of explained variance for each ecosystem function. We detail the graph in the Results section (see l. 317-328) and discuss them (see l. 387-398). Note that we do not detail each function separately as this would (in our opinion) result in a long descriptive paragraph from which it might be difficult to get some key information. Rather, we summarize the percentage of explained variance for each function and discuss the strength of environmental vs biodiversity effects for some examples. In the Discussion, we explain why environmental effects (on functions and biodiversity) are relatively weak. We mainly attribute this to the sampling scheme that follows an East-West gradient (weak altitudinal range) rather than an upstream-downstream gradient as it is traditionally done in rivers. The reasoning behind this sampling scheme is explained in our companion paper (Fargeot et al. Oikos 2023) to which we now refer more explicitly in the MS. Briefly, using an upstream-downstream gradient would have certainly push up the effects of the environment, but this would have made extremely complex the inference of biodiversity effects due to strong collinearity among environmental and biodiversity parameters.

(2) The main results presented in the manuscript are derived from a "metadata" analysis of effect sizes. However, the methods used to obtain these effect sizes are not sufficiently clarified. By analyzing the effect sizes of species diversity and genetic diversity on these ecosystem functions, the results showed that species diversity had negative effects, while genetic diversity had positive effects on ecosystem functions. The negative effects of species diversity contradict many studies conducted in biodiversity experiments. The authors argue that their study is more relevant because it is based on a natural system, which is closer to reality, but they also acknowledge that natural systems make it harder to detect underlying mechanisms. Providing more results based on the raw data and offering more explanations of the possible mechanisms in the introduction and discussion might help readers understand why and in what context species diversity could have negative effects.

(We now provide more details. However, we are unfortunately not sure that this helped reaching some stronger explanation regarding underlying mechanisms. To be frank, we did not succeed in improving mechanistic inferences based on the outputs of the SEM models. We explored visually some additional relationships (e.g. relationships between the biomass of the focal species and that of other species in the assemblage) that we now discuss a bit more, but again, this did not really help in better understanding processes. We realize this is a limitation of our study and that this can be frustrating for readers. Nonetheless, as said in the Discussion, field-based study must be taken for what they are; observational studies forming the basis for future mechanistic studies. Although we failed to explain mechanisms, we still think that we provide important field-base evidence for the importance of biodiversity (as a whole) for ecosystem functions.

3) Environmental variation was included in the analyses to test if the environment would modulate the effects of biodiversity on ecosystem functions. However, the main results and conclusions did not sufficiently address this aspect.

This is now addressed, see our response to your first comment. We now explain (result section) and discuss environmental effects. As explained in the MS, environmental effects are similar in strength to those of biodiversity and are not that high, which is partly explained by the sampling scheme (see Fargeot et al. 2023). This is a choice we’ve made at the onset of the experiment, as we wanted to focus on biodiversity effects and avoid strong collinearity as it is generally the case in rivers (which impedes any proper and strong statistical inferences).

Reviewer #2 (Public review):

Summary:

Fargeot et al. investigated the relative importance of genetic and species diversity on ecosystem function and examined whether this relationship varies within or between trophic-level responses. To do so, they conducted a well-designed field survey measuring species diversity at 3 trophic levels (primary producers [trees], primary consumers [macroinvertebrate shredders], and secondary consumers [fishes]), genetic diversity in a dominant species within each of these 3 trophic levels and 7 ecosystem functions across 52 riverine sites in southern France. They show that the effect of genetic and species diversity on ecosystem functions are similar in magnitude, but when examining within-trophic level responses, operate in different directions: genetic diversity having a positive effect and species diversity a negative one. This data adds to growing evidence from manipulated experiments that both species and genetic diversity can impact ecosystem function and builds upon this by showing these effects can be observed in nature.

Strengths:

The study design has resulted in a robust dataset to ask questions about the relative importance of genetic and species diversity of ecosystem function across and within trophic levels.

Overall, their data supports their conclusions - at least within the system that they are studying - but as mentioned below, it is unclear from this study how general these conclusions would be.

Weaknesses:

(4) While a robust dataset, the authors only show the data output from the SEM (i.e., effect size for each individual diversity type per trophic level (6) on each ecosystem function (7)), instead of showing much of the individual data. Although the summary SEM results are interesting and informative, I find that a weakness of this approach is that it is unclear how environmental factors (which were included but not discussed in the results) nor levels of diversity were correlated across sites. As species and genetic diversity are often correlated but also can have reciprocal feedbacks on each other (e.g., Vellend 2005), there may be constraints that underpin why the authors observed positive effects of one type of diversity (genetic) when negative effects of the other (species). It may have also been informative to run SEM with links between levels of diversity. By focusing only on the summary of SEM data, the authors may be reducing the strength of their field dataset and ability to draw inferences from multiple questions and understand specific study-system responses.

We have addressed this remark and we ask the reviewers and the readers to refer to our response to comment 1 from reviewer 1. Regarding co-variation among biodiversity estimates (SGDCs according to Vellend’s framework), we have addressed these issues in a companion paper that we now cite and expand further in the MS (Fargeot et al. Oikos, 2023). Given the size of the dataset and its complexity (and associated analyses), we have decided to focus on patterns of species and genetic biodiversity in a first paper (Oikos paper) and then on the link between biodiversity and functions (this paper). As it can be read in the Oikos’s paper, there are no co-variation in term of biodiversity estimates; species diversity is not correlated to genetic diversity, and within facet, there are not co-variation among species. In addition, environmental predictors are highly estimate-specific (i.e. environmental predictors sustaining species and genetic estimates are idiosyncratic). As a result (see the new Figure 3), environmental effects are relatively weak (the same intensity that those of biodiversity) and collinearity among parameters is relatively weak. The second point is important, as this permit to better infer parameters from models, and this allows to discuss direct relationships (as observed in Figure 3, indirect environmental effects are relatively rare). We provide in the Discussion a bit more explanation about the absence of co-variation among biodiversity estimates (see l. 433-440).

(5) My understanding of SEM is it gives outputs of the strength/significance of each pathway/relationship and if so, it isn't clear why this wasn't used and instead, confidence intervals of Z scores to determine which individual BEFs were significant. In addition, an inclusion of the 7 SEM pathway outputs would have been useful to include in an appendix.

We now provide p-values (Table S2) and the seven models (Figure 3).

(6) I don't fully agree with the authors calling this a meta-analysis as it is this a single study of multiple sites within a single region and a specific time point, and not a collection of multiple studies or ecosystems conducted by multiple authors. Moreso, the authors are using meta-analysis summary metrics to evaluate their data. The authors tend to focus on these patterns as general trends, but as the data is all from this riverine system this study could have benefited from focusing on what was going on in this system to underpin these patterns. I'd argue more data is needed to know whether across sites and ecosystems, species diversity and genetic diversity have opposite effects on ecosystem function within trophic levels.

We agree. “Meta-regression” would perhaps be more adequate than “meta-analyses”. We changed the formulation.

Reviewer #3 (Public review):

The manuscript by Fargeot and colleagues assesses the relative effects of species and genetic diversity on ecosystem functioning. This study is very well written and examines the interesting question of whether within-species or among-species diversity correlates with ecosystem functioning, and whether these effects are consistent across trophic levels. The main findings are that genetic diversity appears to have a stronger positive effect on function than species diversity (which appears negative). These results are interesting and have value.

However, I do have some concerns that could influence the interpretation.

(7) Scale: the different measures of diversity and function for the different trophic levels are measured over very different spatial scales, for example, trees along 200 m transects and 15 cm traps. It is not clear whether trees 200 m away are having an effect on small-scale function.

Trees identification and invertebrate (and fish) sampling are done on the same scale. Trees are spread along the river so that their leaves fall directly in the river. Traps have been installed all along the same transect in various micro-habitats. Diversity have been measured at the exact same scale for all organisms. We have modified the MS to make this clear.

(8) Size of diversity gradients: More information is needed on the actual diversity gradients. One of the issues with surveys of natural systems is that they are of species that have already gone through selection filters from a regional pool, and theoretically, if the environments are similar, you should get similar sets of species, without monocultures. So, if the species diversity gradients range from say, 6 to 8 species, but genetic diversity gradients span an order of magnitude more, you can explain much more variance with genetic diversity. Related to this, species diversity effects on function are often asymptotic at high diversity and so if you are only sampling at the high diversity range, we should expect a strong effect.

Fish species number varies from 1 to 11, invertebrate family number varies from 15 to 42 and the tree species number varies from 7 to 20 (see Fargeot et al. 2023 for details). We have added this information in the M&M. The gradients are hence relatively large and do not cover a restricted set of values. There is a variance in species number among sites, even if sites are collected along a relatively weak altitudinal gradient. This is obviously complex to compare to SNP (genomic) diversity. Genetic and species effects are similar in effect sizes (percentage of explained variance), so it does not seem we have biased one of the two gradients of biodiversity.

(9) Ecosystem functions: The functions are largely biomass estimates (expect decomposition), and I fail to see how the biomass of a single species can be construed as an ecosystem function. Aren't you just estimating a selection effect in this case?

The biomass estimated for a certain area represents an estimate of productivity, whatever the number of species being considered. Obviously, productivity of a species can be due to environmental constraints; the biomass is expected to be lower at the niche margin (selection effect). But if these environmental effects are taken into account (which is the case in the SEMs), then the residual variation can be explained by biodiversity effects. We provide an explanation (l. 217-219).

(10) Note that the article claims to be one of the only studies to look at function across trophic levels, but there are several others out there, for example:

Thanks, we now cite some of these studies (Li et al 2020, Moi et al. 2021, Seibold et al. 2018).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Introduction:

The introduction of the manuscript is generally well-structured, and the scientific questions are clearly presented. However, in each paragraph where specific aspects are introduced, the authors do not focus sufficiently on the given points. The current introduction discusses the weaknesses of previous studies extensively but lacks detailed explanations of mechanisms and a clear anticipation of this study's contributions.

For example:

L72-77: The authors mention that "genetic diversity may functionally compensate for a species loss," but this point is not highly relevant to the main analyses of this study, which focus on comparing the relative effects of species diversity and genetic diversity.

Yes true, we understand the point made by the reviewers. We deleted this part of the sentence.

L87-95: As previously noted, "whether environmental variation decreases or enhances the relative influence of genetic and species diversity on ecosystem functions" was not addressed in this study. Additionally, the last sentence seems unnecessary here, as it does not relate to "environmental variation." The phrase "generate insightful knowledge for future mechanistic models" is vague. It would be helpful to specify what kind of knowledge and what types of future mechanistic models are being referred to.

We modified these two sentences. We now posit the prediction that what has been observed under controlled conditions (that genetic and species have effects of similar magnitude) might not be the norm under fluctuating environments (because it has been shown that environmental variation modulates the strength of interspecific BEFS and create huge variance).

L96-116: The use of "for instance" three times in this paragraph makes the structure seem scattered, as only examples are provided. Improving the transition words can help the text focus better on the main point.

We have modified some parts of this section to better reflect predictions

L115-116: Again, it would be beneficial to specify what kind of insightful information can be provided.

We have modified this sentence by making more explicit some of the information that may be gained.

L117-134: Stating clear expectations can help the introduction focus on the mechanisms and assist readers in following the results.

We now provide some predictions. We were reluctant to make predictions in the first version of the MS as we have the feeling that predictions can go on very different direction depending on how we set the scene. We therefore stick to predictions that we think are the most logical (the simplest ones). This illustrates the lack of theoretical papers on these issues.

Methods:

L287-293: The method for estimating the standard effect size is unclear. I assume it was derived from the SEM models? This needs further clarification.

Yes, it is derived from the standardized estimate from each pSEM. This is now explained in the MS.

Results:

As mentioned in the public review, it is very important to show the results of analyzing raw data.

Done, see Figure 3 and Results section.

Table 1: The font and format of the PCA table are different from other tables and appear vague, resembling a picture rather than a table.

Changed.

Table 2 (and supplementary table): "D.f." is not explained in the table legend. Is 1 the numerator df and 30 the denominator df? Is the denominator the residual? Additionally, the table legend mentions "magnitude and direction." ANOVA only tests if the biodiversity effects are significantly different between species or genetic diversity, but not the magnitude. For example, -0.5 and 0.5 are very different, but their effect magnitudes are the same.

This is a mistake; sorry the format of the Table was from a previous version of the MS in which we used linear models rather that linear mixed models (both lead to the same results). The ANOVA used to test the significance of fixed terms in linear mixed model are based on Wald chi-sqare tests, and it should have been read “Chi-value” rather than “F-value” in both tables and the only degree of freedom in this test is the one at the numerator. This has been changed. We have changed the caption of the Table (“ANOVA table for the linear mixed model testing whether the relationships between biodiversity and ecosystem functions measured in a riverine trophic chain differ between the biodiversity facets (species or genetic diversity) and the types of BEF (within- or between-trophic levels)”)

Minor:

There should always be a space between a number and a unit. In the manuscript, spaces are inconsistently used between numbers and units.

Corrected

Reviewer #2 (Recommendations for the authors):

(1) In the introduction, the authors could focus more and build out what they predicted/hypothesized as well as what has been found in the manipulated experiments that examined the role of species and genetic diversity. That would enhance the background information for a more general audience, and highlight expected results and why.

We modified the Introduction according to comments made by reviewer 1 and clarified the predictions as best as we can.

(2) Similarly, the discussion is fairly big picture, but this dataset focused exclusively on this 3-trophic interaction in a riverine system. It could be beneficial to dig into the ecology to find out why the opposite effects of species and genetic diversity are seen within trophic levels in this system.

We have added some explanations based on the specific pSEM (see our responses to the public reviews for details). But as said in the responses to the public reviews, even with mode detailed models, it is hard to tease apart mechanisms. One important point is that genetic and species diversity do not correlate one to each other (they do not co-vary over space), which means the effect of one facet is independent from the other. However, apart from that, we can’t really tell more without more mechanistic approaches. We understand this is frustrating, but this is the nature of field-based data. This does not mean they are useless. On the contrary, they confirm and expand patterns found under controlled conditions (which for ecologists is quite important as nature is our playground), but they are limited in inferences of mechanisms.

(3) It would also be informative if the authors specified what positive and negative Z scores mean. It seems counterintuitive in Figure 3. For example, in the upper left, it's denoted as a larger intraspecific effect - which I'd assume is higher genetic (within species) diversity - but is this not where species diversity effects are higher? In theory this figure could be similar to Figure 1 from Des Roches et al. 2018 - where showing the 1:1 line of where species and genetic diversity effects are similar and then how some are more impacted by SD or GD as that links to the overall question, right?

For example: Figure 3 makes it seem that GD effects are stronger (more positive) for within trophic responses (which is reflected in the text), but in that quadrant, it states that the interspecific effect is larger?

yes, you’re true Figure 3 (now Figure 4) is not ideal. We added an explicit explanation for interpreting Zr in the main text. In addition, we modified the text in the quadrat as this was not correct. Note that it cannot be directly be compared to that of DesRoches et al. In DesRoches et al., there is a single effect size (ES) per situation (which is roughly expressed as “ES = effect of species - effect of genotypes”). Here, there are two ES per situation, one for the species effect, the other for the genetic effect, which makes the biplot more complex (as species and genetic can be similar in magnitude, but opposite in direction, e.g., 0.5 and -0.5). We may have done as DesRoches et al. (“ES = effect of species - effect of genotypes”), but as we don’t have absolute ES (as in DesRoches) the resulting signs of the ES are non sensical…Not easy for us to find a clever solution (or said differently, we were not clever enough to find an easy solution).  Nonetheless, we tried another visualization by including “sub-quadrats” into the four main quadrats. We hope this will be clearer

(4) It's unclear why authors included both a simplified linear mixed model with diversity type and biodiversity facet as fixed factors, and then a second linear model that included trophic level (with those other 2 factors and interactions), but only showed results of trophic level from that more complex model. It is unclear why they include two models when the more complex one would have evaluated all aspects of their research question and shown the same patterns.

You’re true, the more complex model evaluates both aspects. Nonetheless, as the hypotheses were strictly separated, we thought it is simpler to associate one model to one hypothesis. We agree that this duplicates information, but we would like to keep the two models to make the text more gradual.

Author response:

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

Reviewer #1 (Public Review):

This manuscript reports the substrate-bound structure of SiaQM from F. nucleatum, which is the membrane component of a Neu5Ac-specific Tripartite ATP-dependent Periplasmic (TRAP) transporter. Until recently, there was no experimentally derived structural information regarding the membrane components of the TRAP transporter, limiting our understanding of the transport mechanism. Since 2022, there have been 3 different studies reporting the structures of the membrane components of Neu5Ac-specific TRAP transporters. While it was possible to narrow down the binding site location by comparing the structures to proteins of the same fold, a structure with substrate bound has been missing. In this work, the authors report the Na+-bound state and the Na+ plus Neu5Ac state of FnSiaQM, revealing information regarding substrate coordination. In previous studies, 2 Na+ ion sites were identified. Here, the authors also tentatively assign a 3rd Na+ site. The authors reconstitute the transporter to assess the effects of mutating the binding site residues they identified in their structures. Of the 2 positions tested, only one of them appears to be critical to substrate binding.

Strengths:

The main strength of this work is the capture of the substrate-bound state of SiaQM, which provides insight into an important part of the transport cycle.

Weaknesses:

The main weakness is the lack of experimental validation of the structural findings. The authors identified the Neu5Ac binding site, but only tested 2 residues for their involvement in substrate interactions, which was very limited. The authors tentatively identified a 3rd Na+ binding site, which if true would be an impactful finding, but this site was not tested for its contribution to Na+ dependent transport, and the authors themselves report that the structural evidence is not wholly convincing. This lack of experimental validation undermines the confidence of the findings. However, the reporting of these new data is important as it will facilitate follow-up studies by the authors or other researchers.

The main concern, also mentioned by other reviewers, is the lack of mutational data and functional studies on the identified binding sites. Two other structures of TRAP transporters have been determined, one from Haemophilus influenzae (Hi) and the other from Photobacterium profundum (Pp). We will refer to the references in this paper as [1], Peter et al. as [2], and Davies et al. as [3]. The table below lists all the mutations made in the Neu5Ac binding site, including direct polar interactions between Neu5Ac and the side chains, as well as the newly identified metal sites.

The structure of Fusobacterium nucleatum (Fn) that we have reported shows a significant sequence identity with the previously reported Hi structure. When we superimpose the Pp and Fn structures, we observe that nearly all the residues that bind to the Neu5Ac and the third metal site are conserved. This suggests that mutagenesis and functional studies from other research can be related to the structure presented in our work.

The table below shows that all three residues that directly interact with Neu5Ac have been tested by site-directed mutagenesis for their role in Neu5Ac transport. Both D521 and S300 are critical for transport, while S345 is not. We do not believe that a mutation of D521A in Fn, followed by transport studies, will provide any new information.

However, Peter et al. have mutated only one of the 5 residues near the newly identified metal binding site, which resulted in no transport. The rest of the residues have not been functionally tested. We propose to mutate these residues into Ala, express and purify the proteins, and then carry out transport assays on those that show expression. We will include this information in the revised manuscript.

Author response table 1.

Reviewer #2 (Public Review):

In this exciting new paper from the Ramaswamy group at Purdue, the authors provide a new structure of the membrane domains of a tripartite ATP-independent periplasmic (TRAP) transporter for the important sugar acid, N-acetylneuraminic acid or sialic acid (Neu5Ac). While there have been a number of other structures in the last couple of years (the first for any TRAP-T) this is the first to trap the structure with Neu5Ac bound to the membrane domains. This is an important breakthrough as in this system the ligand is delivered by a substrate-binding protein (SBP), in this case, called SiaP, where Neu5Ac binding is well studied but the 'hand over' to the membrane component is not clear. The structure of the membrane domains, SiaQM, revealed strong similarities to other SBP-independent Na+-dependent carriers that use an elevator mechanism and have defined Na+ and ligand binding sites. Here they solve the cryo-EM structure of the protein from the bacterial oral pathogen Fusobacterium nucleatum and identify a potential third (and theoretically predicted) Na+ binding site but also locate for the first time the Neu5Ac binding site. While this sits in a region of the protein that one might expect it to sit, based on comparison to other transporters like VcINDY, it provides the first molecular details of the binding site architecture and identifies a key role for Ser300 in the transport process, which their structure suggests coordinates the carboxylate group of Neu5Ac. The work also uses biochemical methods to confirm the transporter from F. nucleatum is active and similar to those used by selected other human and animal pathogens and now provides a framework for the design of inhibitors of these systems.

The strengths of the paper lie in the locating of Neu5Ac bound to SiaQM, providing important new information on how TRAP transporters function. The complementary biochemical analysis also confirms that this is not an atypical system and that the results are likely true for all sialic acid-specific TRAP systems.

The main weakness is the lack of follow-up on the identified binding site in terms of structure-function analysis. While Ser300 is shown to be important, only one other residue is mutated and a much more extensive analysis of the newly identified binding site would have been useful.

Please see the comments above.

Reviewer #3 (Public Review):

The manuscript by Goyal et al reports substrate-bound and substrate-free structures of a tripartite ATP-independent periplasmic (TRAP) transporter from a previously uncharacterized homolog, F. nucleatum. This is one of the most mechanistically fascinating transporter families, by means of its QM domain (the domain reported in his manuscript) operating as a monomeric 'elevator', and its P domain functioning as a substrate-binding 'operator' that is required to deliver the substrate to the QM domain; together, this is termed an 'elevator with an operator' mechanism. Remarkably, previous structures had not demonstrated the substrate Neu5Ac bound. In addition, they confirm the previously reported Na+ binding sites and report a new metal binding site in the transporter, which seems to be mechanistically relevant. Finally, they mutate the substrate binding site and use proteoliposomal uptake assays to show the mechanistic relevance of the proposed substrate binding residues.

The structures are of good quality, the functional data is robust, the text is well-written, and the authors are appropriately careful with their interpretations. Determination of a substrate-bound structure is an important achievement and fills an important gap in the 'elevator with an operator' mechanism. Nevertheless, I have concerns with the data presentation, which in its current state does not intuitively demonstrate the discussed findings. Furthermore, the structural analysis appears limited, and even slight improvements in data processing and resulting resolution would greatly improve the authors' claims. I have several suggestions to hopefully improve the clarity and quality of the manuscript.

We appreciate your feedback and will make the necessary modifications to the manuscript incorporating most of the suggestions. We will submit the revised version once the experiments are completed. We are also working on improving the quality of the figures and have made several attempts to enhance the resolution using CryoSPARC or RELION, but without success. We will continue to explore newer methods in an effort to achieve higher resolution and to model more lipids, particularly in the binding pocket.

Reviewing Editor (Recommendations for the Authors):

After discussing the reviews, the reviewers and reviewing editor have agreed on a list of the most important suggested revisions for the authors, which, if satisfactorily addressed, would improve the assessment of the work. These suggested revisions are listed below. We also include the full Recommendations For The Authors from each of the individual reviewers.

(1) The authors tentatively identified a 3rd Na+ binding site, which if true would be an impactful finding, but this site was not tested for its contribution to Na+ dependent transport, and the authors themselves report that the structural evidence is not wholly convincing. Additional mutagenesis and activity experiments to test the contribution of this site to transport would strengthen the manuscript. Measuring Na+ concentration-response relations and calculating Hill slopes in WT vs. an M site mutant would be a good experiment. Given the lack of functional data and poor density, it does not seem appropriate to build the M site sodium in the PDB model.

The density is well defined to suggest a metal bound (waters would not be clearly defined at this resolution).  While our modeling of the site as a Na+ is arbitrary, this was done to satisfy the refinement programs where we have a known scatterer modeled.  We could model this density with other metals, but unlike crystallographic refinement, real-space refinement of cryoEM maps does not produce a difference map that might allow us to identify the metal but not conclusively.   The density of the maps is good (we have added better figures to demonstrate this).  We tried making multiple mutations to test for activity – unfortunately, we are still struggling to express proteins with mutations in this site in sufficient quantities to carry out transport assays.

In the absence of being able to do the experiments, we did MD simulations (carried out by Senwei Quan and Jane Allison at University of Auckland).  Our results are shown below – we are not certain without further studies that these should be included in the current paper (we will add them as authors if the editor feels that this evidence is critical).

Author response table 2.

We are showing this for review to suggest that K+, Ca2+, and Na+ were tried, and only Na+ stays stably in the binding pocket. The rest of the results will also have to be explained, which would change the focus of the paper.

We also provided the sequence to Alphafold3 and asked it to identify the possible metal binding sites—when the input was Na+, it found all three binding sites. 

Summary:  Both our experimental data and computational studies suggest the observed metal binding site is real but at the moment, it is not possible to refine the structure and put an unidentified metal.  Computational studies suggest that this is a high-probability Na+ site. 

Demonstration of cooperativity between the Na+ site and transport require carrying out these experiments with mutations in these sites in a concentration-dependent manner. Unfortunately, our inability to produce well-expressed and purified proteins with mutations in a short time frame failed. 

(2) The authors identified the Neu5Ac binding site but only tested 2 residues for their involvement in substrate interactions, which was very limited. Given that the major highlight of this paper is the identification of the Neu5Ac binding site, it would strengthen the manuscript if the authors provided a more extensive series of mutagenesis experiments - testing at least the effect of D521A would be important. One inconsistency is Ser345 mutagenesis not affecting transport, and the authors should further discuss in the text why they think that is.

D521A has been tested in H. influenzae, and this mutation results in loss of transport.  This residue is highly conserved and occupies the same position. We expect the result to remain the same. 

We have added a few extra lines to discuss Serine 345: “Ser 345 OG is 3.5Å away from the C1-carboxylate oxygen – a distance that would result in a weak interaction between the two groups. It is, therefore, not surprising that the mutation into Ala did not affect transport. The space created by the mutation can be occupied by a water molecule.”

(3) The purification and assessment of the stability of the protein are described in text alone with no accompanying data. It would be beneficial to include these data (e.g. in the Supplementary info) as it allows the reader to evaluate the protein quality.

This is now added as Supplementary Figure 2.

(4) The structural figures throughout the paper could benefit from more clarity to better support the conclusions. Specific critiques are listed below:

- Figure 1: since the unbound map has a similar reported resolution, displaying the unbound structure's substrate binding site with the same contour would clearly demonstrate that the appearance of this density is substrate-dependent.

- Figure 1: the atomic fit of the ligand to the density, and the suggested coordination by side chain and backbone residues, would be useful in this figure.

- Figure 1: I think it would be more intuitive to compare apo and bound structures with the same local resolution scale.

We have remade Figure 1 “Architecture of FnSiaQM with nanobody. (A and B) Cryo-EM maps of FnSiaQM unliganded and sialic acid bound at 3.2 and 3.17 Å, respectively. The TM domain of FnSiaQM is colored using the rainbow model (N-terminus in blue and C-terminus in red). The nanobody density is colored in purely in red. The density for modeled lipids is colored in tan and the unmodelled density in gray. The figures were made with Chimera at thresholds of 1.2 and 1.3 for the unliganded and sialic acid-bound maps. (C and D) The cytoplasmic view of apo and sialic acid bound FnSiaQM, respectively. Color coding is the same as in panels A and B. The density corresponding to sialic acid and sodium ions are in purple. The substrate binding sites of apo and sialic acid bound FnSiaQM are shown with key residues labeled. The density (blue mesh) around these atoms was made in Pymol with 2 and 1.5 s for the apo and the sialic acid, respectively, with a carve radius of 2 Å.”

The local resolution maps have been moved to Supplementary Figure 3.

- Figure 3, Figure 5a: The mesh structures throughout the manuscript are blocky and very difficult to look at and interpret, especially for the ion binding sites, which are currently suggestive of but not definitively ion densities. Either using transparent surfaces, higher triangle counts, or smoothing the surface might help this.

We have made Figure 3 again with higher triangle counts.  We tried all three suggestions and this provided the best figure. We have replaced Figure 5A with density for Neu5Ac and residues around it.

- Figure 5A: It would be important to show the densities of the entire binding pocket, especially coordinating side chains, to show the reader what is and isn't demonstrated by this structure.

- It's not clear how Figure 5D is supposed to show that the cavity can accommodate Neu5Gc, as suggested by the text - please make the discussed cavity clearer in the Figure.

We have now marked with an arrow the Methyl Carbon where the hydroxyl group is added.  We have mentioned that in the legend.  It is open to the periplasmic side of the cavity.

- Supplementary Figure 4: Please label coordinating residue sites.

Labels have been added to Supplementary Figure 6 which was earlier Supplementary Figure 4.

(5) Intro section: the authors should introduce the work on HiSiaP around the role of the R147 residue in high-affinity Neu5Ac binding, which coordinates the carboxylate of Neu5Ac, and which is a generally conserved mechanism for organic acid binding in other TRAP transporters. This context will help magnify their discovery later that in the membrane domains, it is a key serine and not an arginine that coordinates the carboxylate group (probably as the local concentration of Neu5Ac is high and tight binding site is not desirable for rapid transport, which is mentioned in the discussion).

Thank you for pointing this out. We have added a new sentence to the introduction.

“All the SiaP structures show the presence of a conserved Arginine that binds to the C1-carboxylate of Neu5Ac, and this Arg residue is critical as the high electrostatic affinity may be important to have a strong binding affinity that sequesters the small amounts that reach the bacterial periplasmic space  (Glaenzer et al., 2017).”

(6) TRAP transporters exist for many organic compounds and not just sialic acid, which might be nice to make the reader aware of.

We initially did not do this as this is an advance paper and this was discussed in the earlier paper (Currie et. al., 2024). However, we have now added a sentence to the introduction. “Additionally, amino acids, C4-dicarboxylates, aromatic substrates and alpha-keto acids are also transported by TRAP transporters (Vetting et al., 2015). “

(7) On p. 12, the authors describe the Neu5Ac binding site as a large solvent-exposed vestibule, having previously described the substrate-bound state as occluded. These descriptions should be adjusted to make clear which structure is being referenced. The clarity of this would be substantially improved if the authors included a figure that showed this occlusion - currently none of the structure figures clearly demonstrate what the authors are referring to. There are several conspicuous unmodeled densities proximal to the substrate, reminiscent of lipids (in between transport and scaffold domain) and possibly waters/ions. Given this, it is really surprising that the substrate binding site is described as "solvent-exposed" since the larger molecules seem to occlude the pocket. The authors should further process their dataset and discuss the implications of these surrounding densities.

We have processed the data sets carefully both with cryosparc and relion and the resolution described here is same with both software with the cryosparc maps slightly better in terms of interpretability of peripheral helices and described in the manuscript. The current sample (FnTRAP) with the nanobody is a relatively stable sample (in our experience with other similar proteins) as evident from the number of images and particles to achieve a decent resolution and thus the workflow is straightforward and simple.  There are number of non-protein densities, which in principle can be modelled but we have chosen a conservative approach not to model these extra densities (except for the two lipids, few ions) due to limit of the resolution. It is possible that increasing the number of particles will result in an increase in resolution but from the estimated B-factor (125 or 135 Å2 for unliganded and liganded), this will certainly require lot of more images with no guarantee of increased resolution.

The question of outward open Vs outward occluded is a valid point. We have now modified this in the manuscript. “The Neu5Ac binding site has a large solvent-exposed vestibule towards the cytoplasmic side, while its periplasmic side is sealed off. Cryo-EM map shows the presence of multiple densities that could be modeled as lipids, possibly preventing the substrate from leaving the transporter. However, the densities are not well defined to model them as specific lipids, hence they have not been modeled.  We describe this as the “inward-facing open state” with the substrate-bound.”

(8) On p.15, the activity of FnSiaPQM in liposomes is reported, although the impetus for this study is not clear. Presumably, the reason for its inclusion is to ensure that the structurally characterized protein is active. It would be useful to say this at the start of the section if this is the case. This study nicely shows that the energetics and requirements of transport are identical to all the previous studies on Neu5Ac TRAP transporters - it would be good to acknowledge this somewhere in this section as well.

These changes have been incorporated.  We have added a line to say why we did this and added as the last line that this is similar to other SiaPQM’s characterized.

(9) Figure 5C. The authors show the transport activity with and without valinomycin. The authors do not explain the rationale for testing and reporting both conditions for these mutants; an explanation is required, or the data should be simplified. The expected membrane potential induced by valinomycin should be mentioned in the legend.

We have simplified Figure 5C and added the expected membrane potential value.

(10) The authors state that the S300A mutant is inactive. However, unless the authors also measured the background binding/transport of radiolabelled substrate in the absence of protein, then the accuracy of this statement is not clear because Figure 5C does indicate some activity for S300A, albeit much lower than WT. This is an important point in light of the authors' suggestion that the membrane protein does not need a binding site of high affinity or stringent selectivity.

We thank the reviewer for pointing this out we have now added a line in the experimental protocols “The experimental values were corrected by subtracting the control, i.e. the radioactivity taken up in liposomes reconstituted in the absence of protein. The radioactivity associated with the control samples, i.e. empty liposomes was less than 10% with respect to proteoliposomes.”.

(11) There are several issues and important omissions in the work cited:

- It is not normal practice to cite a reference in the abstract and the citation is only to the second structure of HiSiaQM, which does not fairly reflect previous work in the field by only referring to their own work. Also throughout the article, it is normal practice with in-text citations to order them chronologically, i.e. earliest first. Please update this.

This article was submitted as an “Research advance article”.  The instructions specifically say that “Research advance article should cite the article in eLife this paper advances.  Hence the citation of the “second structure of HiSiaQM”.  In fact, in the manuscript we explicitly say “The first structure of _Hi_SiaQM (4.7 Å resolution) demonstrated that it is composed of 15 transmembrane helices and two helical hairpins.”   We are following the policy laid out.  

Zotero organizes multiple references in alphabetical order, we did not choose to do it that way – the suggestion of bias is not true. The final version of the accepted paper will have numbers, and this argument will automatically be corrected.

- Intro: please cite the primary papers discovering other families of sialic acid transporters.

- Intro: When introducing information on the binding site, dissociation constant of Neu5Ac, and thermodynamics of ligand binding to SiaP, the authors should also include references to the work done by others in addition to their own work.

The Setty et al. paper was the first to demonstrate that the two-component systems are distinct, and that the binding protein of the TRAP system binds enthalpically while the binding protein of the ABC system binds entropically (SiaP vs SatA). As the reviewer points out, this is significant because it highlights how the Arg binding to the carboxylate, which is the enthalpic driver in this case and contributes to the difference between sugar binding to SiaP and SatA. Many studies have published binding affinities of molecules to SiaP, but this paper offers valuable insight into the differences between these systems. We have cited a number of the SiaP papers from other groups, including acknowledging the first structure of SiaP from H. influenzae by Muller et al., in 2006.

- p.5 "TRAP transporters are postulated to employ an elevator-type mechanism...". This postulation has been experimentally tested and published, so should be discussed and referenced (Peter et al. 2024. https://doi.org/10.1038/s41467-023-44327-3).

We have now corrected this error. We removed “are postulated to” and added the reference.

- p.5 "Notably, the transport of Neu5Ac by TRAP transporters requires at least two sodium ions (Davies et al., 2023)." The requirement for at least 2 Na+ ions for Neu5Ac transport was first demonstrated in Mulligan et al. PNAS 2009, so should also be cited (for completion, so should Mulligan et al. JBC. 2012 and Currie et al. elife 2023, which have also shown this requirement is a commonality amongst all Neu5Ac TRAP transporters).

Added.

- P.12, Mulligan et al, JBC, 2012 should be added to the citations in the first sentence.

Added.

- p.19 "Interestingly, even the dicarboxylate transporter from V. cholerae (VcINDY) binds to its ligand via electrostatic interactions with both carboxylate groups". Other references are more appropriate than the one used to support this statement.

Also added references for Mancusso et. al, 2012, Nie et.al, 2017 and Sauer et.al., 2022 here.

- p.19. "The structure of the protein in the outward-facing conformation is unknown". The authors do not discuss the mechanistic findings from Peter et al 2024 Nat Comm here. The work described in that paper revealed an experimentally verified model of the OFS of HiSiaQM, so really needs to be included.

This is not an experimentally determined 3D structure. They have shown the possible existence of this by microscopy, but the structure is not determined. The work mentioned is a wonderful piece of work, but it does not report the three-dimensional structure of the protein in the outward-facing conformation to allow us to understand the nature of the molecular interactions. 

- The reference to Kinz-Thompson et al 2022 on p. 6 is not appropriate - neither the HiSiaQM papers nor the PpSiaQM paper makes reference to this work when identifying the binding site. More suitable references are used, for example, Mancusso et al 2012, Nie et al 2017 and Sauer et al 2022; this should be reported accurately.

Added the suggested references.  We think the paper (Kinz-Thomposin et al 2022) is relevant and have also kept that reference.

- Garaeva et al report the opposite of what the authors mention - "In the human neutral amino acid transporter (ASCT2), which also uses the elevator mechanism, the HP1 and HP2 loops have been proposed to undergo conformational changes to enable substrate binding and release (Garaeva et al., 2019)." In fact, this paper suggested a one-gate model of transport (HP2), where HP1 seems uninvolved in gating.

The Reviewer is correct.  We were wrong and not clear.  The entire paragraph has been rewritten.

“While, both the HP1 and HP2 loops have been hypothesized to be involved in gating, in the human neutral amino acid transporter (ASCT2), (which also uses the elevator mechanism), only the HP2 loops have been shown to undergo conformational changes to enable substrate binding and release (Garaeva et al., 2019). Hence, it is suggested that there is a single gate that controls substrate binding. Superposition of the _Pp_SiaQM and _Hi_SiaQM structures do not reveal any change in these loop structures upon substrate binding. For TRAP transporters, the substrate is delivered to the QM protein by the P protein; hence, these loop changes may not play a role in ligand binding or release. This may support the idea that there is minimal substrate specificity within SiaQM and that it will transport the cargo delivered by SiaP, which is more selective.”

- p.19 "suggesting that SSS transporters have probably evolved to transport nine-carbon sugars such as Neu5Ac (Wahlgren et al, 2018)." Surely this goes without saying since Wahlgren et al 2018 demonstrated that SiaT, an SSS, could transport sialic acid? It's unclear why this was included here - perhaps it needs to be rewritten to make the point more clearly, but as it stands, this statement appears self-evident. Furthermore, these proteins can transport all kinds of molecules (see TCDB 2.A.21). This statement needs to be clarified. 

This was a comparison to other Neu5Ac binding sites in other Neu5Ac transporters. We have modified the sentence. “The polar groups bind to both the C1-caboxylate side of the molecule and the C8-C9 carbonyls, suggesting that Proteus mirabilis Neu5Ac transporter (SSS type) evolved specifically to transport nine-carbon sugars such as Neu5Ac (Wahlgren et al., 2018)”.  These were arguments we were making to suggest that the lack of tight binding could also mean reduced specificity.

- The authors reconstitute the FnSiaQM and measure transport with SiaP, which resembles closely what is known for both HiSiaPQM, VcSiaPQM, which is not cited (https://doi.org/10.1074/jbc.M111.281030).

- Regarding lipids between transport and scaffold domains: there is precedent for such lipids in the elevator transporter GltPh, Wang, and Boudker (eLife 2020) proposed similar displacements during transport and would be appropriate to cite here.

We have now cited the reference to the Mulligan et al., 2012 paper.  We also added a sentence on the findings of GltPh paper by Wang and Boudker.  Thank you for pointing this out.

(12) p.9 "TRAP transporters, as their name suggests, comprise three units: a substrate-binding protein (SiaP) and two membrane-embedded transporter units (SiaQ and SiaM) (Severi et al., 2007)." This is somewhat odd phrasing because the existence of fused membrane components has been well-documented for a long time. The addition of "Many" at the start of the sentence fixes this.

Added Many.

(13) On p.12 the authors compare the ligand-induced conformational changes of FnSiaQM with ASCT2, citing Garaeva et al, 2019. This comparison does not make sense considering TRAP transporters and ASCT2 do not share a common fold. A far superior comparison is with DASS transporters, which actually do have the same fold as TRAP transporters. And, importantly, the Na+ and substrate-induced conformational changes have been investigated for DASS transporters revealing a unique mechanism likely shared by TRAP transporters (Sauer et al, Nat Comm, 2022). The text on p.12 should be adjusted to replace the ASCT comparison with a VcINDY comparison.

The purpose of citing the ASCT2 paper was only concerning the HP1 and HP2 gates.  The authors show that HP2 changes conformation only.  Comparing the two FnSiaQM structures – with and without ligand, we see no change in either the HP1 or the HP2 loops.  On Page 17, when we describe the structure, we do specifically mention that the overall architecture is similar to VcINDY and the DASS transporters.

(14) p.12 "For TRAP transporters, the substrate is delivered to the QM protein by the SiaP" protein;" "SiaP protein" should be "P protein"

Corrected.

(15) p.18. "periplasmic membrane" should be "cytoplasmic membrane".

Corrected.

(16) p.19. "This prevents Neu5Ac from binding..." There is no evidence for this so this needs to be softened, e.g. "This likely prevents Neu5Ac from...".

Agree – Modified.

(17) Figure 2B is rather small, cramped, and difficult to see. We suggest that the authors make that panel larger, or include it as a stand-alone supplementary figure.

We have moved this figure into a supplementary figure as suggested by the reviewer.

(18) The authors describe the Neu5Ac binding site in SiaQM. It would be helpful if the authors provided a figure in support of the statement that the Neu5Ac binding site architecture is similar to dicarboxylate in VcINDY (especially as Neu5Ac is a monocarboxylate).

The Neu5Ac binding site is NOT similar to the VcINDY binding site. But, we understand the origin of the comment. We have now changed the sentence: “The overall architecture of the Neu5Ac binding site is similar to that of citrate/malate/fumarate in the di/tricarboxylate transporter of V. cholerae (Vc_INDY), but the residues involved in providing specificity are different (Kinz-Thompson _et al., 2022; Mancusso et al., 2012; Nie et al., 2017; Sauer et al., 2022). Neu5Ac binds to the transport domain without direct interactions with the residues in the scaffold domain. The majority of the interactions are with residues in the HP1 and HP2 loops of the transport domain (Figure 5B). Asp521 (HP2), Ser300 (HP1), and Ser345 (helix 5) interact with the substrate through their side chains, except for one interaction between the main chain amino group of residue 301 and the C1-carboxylate oxygen of Neu5Ac. Mutation of the residue equivalent to Asp521 has been shown to result in loss of transport (Peter et al., 2022). To evaluate the role of residues Ser-300 and Ser-345, we mutated them to alanine and performed the transport assays.”  

(19) When comparing the binding modes of Neu5Ac to different proteins in Figure 6, it would be helpful to include the structure in this paper as well.

The Neu5Ac binding site is present in figure 5. We would prefer not to show it again in Figure 6.

Additionally, there is a clear binding mode of Neu5Ac in Figure 1 as well.

(20) The manuscript would benefit from a more detailed comparison between Na+-bound (described as apo) and Na+/Neu5Ac structures, especially the prospective gates. If this transporter behaves anything like the archetypical ion-coupled glutamate transporters, some structural changes in the gates might be expected to facilitate transport domain movement when the substrate is loaded, but not when only Na+ is bound. It would be important to discuss and visualize these changes.

We have described in the manuscript that there is NO change in the HP1 and HP2 gates between the unliganded structure and the Neu5Ac bound structure. The major difference we observe is the ordering of the third metal binding site.

A figure comparing the substrate binding pockets between the different high-resolution structures would also be informative. Do the bonding distances between ligands and side chains significantly change between homologs?

This is the only Neu5Ac bound structure.  Since the specificity to the substrate comes from the variability of the residues that interact it, we do not believe that this figure would not add much value.  

(21) A supplementary figure (or an inset to Figure 2) showing pairwise percent identity between different characterized QM transporters would be useful.

We have now added a Supplementary Figure 4 showing the comparison of the three QM sequences whose structures have been determined.

(22) There is relatively minimal EM processing. More rigorous processing would require relatively little effort and could boost resolution, making this a vastly improved manuscript with a much more confident interpretation of structures.

We described the overall workflow. The processing was rigorous. After obtaining the first maps, we created templates with the structure and did template-based picking.  We then did several rounds of 2D classification followed by homogenous refinement, Non-Uniform Refinement.  We then made masks and carried out local refinement.  We then got the best maps and did a 3D classification. Refined the 3D classes independently.  Then, we regrouped them based on how similar they were. We then went back and picked particles again (we used different methods of particle picking, but template-based picking resulted in the final set of particles used) and went through the whole process again.  At the end of the refinement, we carried out global and local CTF refinement followed by reference-based motion correction. The final refinement was then done with the Bayesian polished particles.  The final refinement was local refinement with a mask over only the transporter and the nano-body. After the reviews came, we tried multi-body refinement in Relion5.  It did not improve resolution. We have expanded the legend to supplementary Figure 2 (without listing all the different things we tried). The best resolution we obtained for the structure was 3.1 Å. However, it is important to note that the local resolution of the map around the ligand is good. 

We realized this is not easy to depict in a local resolution map.  So, we wrote a script to take every atom, then take a radius of 5 Å (again we tried different radii and used the optimal one; we are preparing a manuscript to describe this), take all the local resolution values within the 5 Å spere and average it and add it as B-factor that atom. We have moved the local resolution map figure to the supplement and replaced Figure 1 with a Cartoon, where the color represents the local resolution in which the atom is. 

(23) Calling the structure without Neu5Ac bound an "apo" structure is confusing since it indeed has the ligand Na+ present and bound. "Na+" and "Na+/Neu5Ac" structures would be more appropriate.

Changed all “apo” to “unliganded”.

Author response:

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

Reviewer 1:

- The manuscript needs comprehensive proofreading for language and formatting. In many instances, spaces are missing or not required.

Thank you for your comments. The manuscript has been thoroughly proofread for errors in language and formatting.

- Could the authors explore correlation network analyses to get additional insights into the structure of different clusters? 

We have added a co-occurrence analysis (at species taxonomic level) based on SparCC to the manuscript (Figure 2).

This is described on Page 9 line 141-148

- The GitHub link is not correct. 

The github repository has now been made public.

- It is not possible to access the dataset on ENA. 

We have changed the ENA study PRJEB57401 status to open.

- Add the graphs obtained with decontam analysis as a supplementary figure. 

We have added the outputs of decontam (.csv files with feature lists of ASVs that were filtered based on the prevalence and frequency tests) to the github repository.

- There is nothing about the RPL group in the results section, while the authors discuss this issue in the introduction. What about the controls with proven fertility? 

Thank you. We have amended the manuscript to compare characteristics between the RPL, unexplained subfertility and controls groups.

Line 1279-130 page 8:  

“The study group represented 85% of samples with high sperm DNA fragmentation, 85% of samples with elevated ROS and 79% of samples with oligospermia. Rates of abnormal seminal parameters including low sperm concentration, reduced progressive motility and ROS concentrations were found to be highest in the MFI group (Supplementary Figure 1). Baseline characteristics between the RPL, unexplained subfertility and controls groups were similar.

Line 150-154 Page 9: 

“Bacterial richness, diversity and load were similar between all patient groups examined in the study (Supplementary Figure 4).

- While correctly stated in the title, the term microbiota should be used throughout the manuscript instead of "microbiome" 

Thank you. This misnomer has been amended throughout the manuscript.

Minor corrections:

Line 25: provoke is not a good term here. 

Thank you. The term ‘provoke’ has been removed

Line 26: why does semen culture have a limited scope? 

Thank you. Line 40-41 Page 3 has been amended:

“It is therefore plausible that asymptomatic seminal infections may be associated with impaired reproductive function in some men. Since semen culture has a limited scope for studying the seminal microbiota due to its inability to identify all present microbiota next generation sequencing (NGS) approaches have been reported recently by a growing number of investigators (13, 14, 15, 16, 17, 18, 19)”.

Line 68: write μl correctly

Thank you. This has been corrected

Line 131: several organisms at the genus level. 

Thank you. This has been corrected

Line 136: what are the relative abundances of these genera? Is this relevant? 

The mean relative abundances for the key taxa mention in each cluster are all above 20%. This information has been added to the manuscript text on page 9, line 153.

Line 173: Molina et al. 

Thank you. This has been corrected

Line 173: the contaminations are referred to the low biomass nature of testicular samples. If present, bacteria of accessory gland secretions are an integral part of the seminal microbiota itself. Please review these sentences. 

Thank you. This had been reworked to highlight the important of urethral contamination, which you later allude to as a limitation of our study is the failure to provide paired urine and semen samples.

Page 11 line 194-196

“Molina et al report that 50%-70% of detected bacterial reads may be environmental contaminants in a sample from extracted testicular spermatozoa (35); with the addition of passage along the urethra it is likely that contamination of ejaculated semen would be much higher.”

Table 1: remove results interpretation from table caption. 

Thank you this has been acted upon.

Table 1: why in some cases, like in DNA fragmentation index, the total is not equal to n=223? 

This is due to missing data/ analysis not possible for some men due to the requirement of a minimum number of sperm in the ejaculate to perform DNA fragmentation testing.

Table 1: "frag" is not defined. 

Thank you, this has been amended

Tables 2, 3 & 4: bacterial genera in italics. 

Thank you, this has been amended

Figure 1A: add the fertility status information above the cluster colors. 

Thank you, this has been amended in Figure 1.

Figure 1C: the color code is confusing. Use different colors for each cluster. 

Figure 1 legend: bacterial genera in italics. 

Figures 1 & 2: the authors should use similar chart formatting in the two tables. 

Thank you, this has been amended

Reviewer 2:

(1) The patient groups have different diagnoses and should be handled as different groups, and not fused into one 'patient' group in analyses. <br /> Why are the data in tables presented as controls and cases? I would consider men from couples with recurrent pregnancy loss, unexplained infertility, and male factor infertility to have different seminal parameters (not to fuse them into one group). This means, that the statistical analyses should be performed considering each group separately, and not to fuse 3 different infertility diagnoses into one patient group. 

We have conducted detailed analyses, requested by the reviewer, comparing seminal DNA, ROS and microbiota characteristics between each individual patient groups (Supplimental figures 1 and 4). No specific taxa (at either genera or species-level) were found to differ in relative abundance between the diagnostic groups. However, we expect associations between parameters such as reactive oxygen species, or DNA fragmentation, and relative abundance of bacterial species, to be general and not restricted to or specific to each diagnostic group. Therefore, we also conducted further analyses aggregating data from all patient groups to investigate relationships common to these different forms of male reproductive dysfunction.

(2) Were any covariables included in the statistical analyses, e.g. age, BMI, smoking, time of sexual abstinence, etc? 

Covariates were not included in the statistical analyses. This has been added in the manuscript to the limitations.

Page 14 line 267-268

“Additionally, we did not have other covariables such as smoking status with which to include in further analyses”.

(3) Furthermore, it is known that 16S rRNA gene analysis does not provide sensitive enough detection of bacteria on the species level. How much do the authors trust their results on the species level? 

The limitations of taxonomic assignment using 16S rRNA gene metataxonomics are well documented. However, the capacity to assign sequence amplicons at species level depends on the sequence variability of the 16S rRNA gene for each of the taxa reported and the specific gene region chosen. In this study, amplification of the V1-V2 region was performed using a mixed 28f primer set (see methods for details) that enables resolution and assignment of several bacterial species highly relevant to the reproductive tract including Lactobacillus spp., such as L. crispatus and L. iners, (e.g. https://doi.org/10.3389/fcell.2021.641921, https://doi.org/10.1128/msystems.01039-23, https://doi.org/10.1186/s12915-023-01702-2). In this study, we report the presence of L. iners, but not L. crispatus in semen samples, and we have also identified a specific association/co-occurrence between Gardnerella vaginalis and Lactobacillus iners, similar to that observed in vaginal bacterial communities.

(4) Were the analyses of bacterial genera and species abundances with seminal quality parameters controlled for diagnosis and other confounders? 

As stated in point 2, no adjustment was made for co-variates. No differences in microbiome composition were observed among the three diagnostic groups, so no adjustments were made to our analysis.

(5) The authors stress that their study is the biggest on the microbiome in semen. However, when considering that the study consists of 4 groups (with n=46-63), it does not stand out from previous studies. 

Our study is overall the largest investigating interactions between the seminal microbiome and male reproductive dysfunction. Other studies have included greater numbers of men with infertility.

(6) Weaknesses: There is a lack of paired seminal/urinal samples. 

Thank you. This limitation has been added.

Page 14 line 266-267

“A further limitation of this study, and others, is the lack of reciprocal genital tract microbiota testing of the female partners, or paired seminal and urinary samples from male participants”.

Recommendation for authors to consider:

Including previous classical reviews in the introduction: DOI:10.1097/MOU.0000000000000742 <br /> DOI: 10.1038/s41585-019-0250-y 

Thank you. This has been added.

Mentioning in the M&M section that there is a supplementary text with a more detailed M&M part. 

Thank you. This has been added. Further methodological detail can be found in supplementary text.

Revising the use of 'microbiota' and 'microbiome', they are not synonyms. When talking of 16S rRNA gene analysis, we consider 'microbiome' analysis. 

Thank you. This misnomer has been amended throughout the manuscript.

Revising the text, there are several erratas (e.g. verb missing, etc). 

Thank you for your comments. The manuscript has been thoroughly proofread for errors in language and formatting.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review):

Summary: 

In the manuscript entitled "Magnesium modulates phospholipid metabolism to promote bacterial phenotypic resistance to antibiotics", Li et al demonstrated the role of magnesium in promoting phenotypic resistance in V. alginolyticus. Using standard microbiological and metabolomic techniques, the authors have shown the significance of fatty acid biosynthesis pathway behind the resistance mechanism. This study is significant as it sheds light on the role of an exogenous factor in altering membrane composition, polarization, and fluidity which ultimately leads to antimicrobial resistance. 

Strengths: 

(1) The experiments were carried out methodically and logically. 

(2) An adequate number of replicates were used for the experiments. 

Weaknesses: 

(1) The introduction section needs to be more informative and to the point.  

Thank you so much for your suggestion. We have revised the introduction to make it more informative and to the point as following:

“Non-inheritable antibiotic or phenotypic resistance represents a serious challenge for treating bacterial infections. Phenotypic resistance does not involve genetic mutations Phenotypic resistance does not involve genetic mutations and is transient, allowing bacteria to resume normal growth. Biofilm and bacterial persisters are two phenotypic resistance types that have been extensively studied (Brandis et al., 2023; Corona & Martinez, 2013). Biofilms have complex structures, containing elements that impede antibiotic diffusion, sequestering and inhibiting their activity (Ciofu et al., 2022). Biofilm-forming bacteria and persisters also have distinct metabolic states that significantly reduce their antibiotic susceptibility (Yan & Bassler, 2019). These two types of phenotypic resistance share the common feature in their retarded or even cease of growth in the presence of antibiotics (Corona & Martinez, 2013). However, specific factors that promote phenotypic resistance and allow bacteria to proliferate in the presence of antibiotics remain poorly defined.

Metal ions have a diverse impact on the chemical, physical, and physiological processes of antibiotic resistance  (Booth et al, 2011; Lu et al, 2020; Poole, 2017). This includes genetic elements that confer resistance to metals and antibiotics (Poole, 2017) and metal cations that directly hinder (or enhance) the activity of specific antibiotic drugs (Zhang et al., 2014). The metabolic environment can also impact the sensitivity of bacteria to antibiotics (Jiang et al., 2023; Lee & Collins, 2012; Peng et al., 2015; Zhang et al., 2020; Zhao et al., 2021). Light metal ions, such as magnesium, sodium, and potassium, can behave as cofactors for different enzymes (Du et al., 2016) and influence drug efficacy. Heavy metal ions, including Cu2+ and Zn2+, confer resistance to antibiotics (Yazdankhah et al., 2014; Zhang et al., 2018). Recent reports suggest that sodium negatively regulates redox states to promote the antibiotic resistance of Vibrio alginolyticus (Yang et al., 2018), while actively growing Bacillus subtilis cope with ribosome-targeting antibiotics by modulating ion flux (Lee et al, 2019). In Gram-negative bacteria, by contrast, zinc enhances antibiotic efficacy by potentiating carbapenem, fluoroquinolone, and β-lactam-mediated killing (Isaei et al., 2016; Zhang et al., 2014). Magnesium influences bacterial structure, cell motility, enzyme function, cell signaling, and pathogenesis (Wang et al., 2019). This mineral also modulates microbiota to harvest energy from the diet (Garcia-Legorreta et al., 2020), allowing Bacillus subtilis to cope with ribosome-targeting antibiotics by modulating ion flux (Lee et al., 2019). However, the role of magnesium in promoting phenotypic resistance is less well understood.

Vibrios inhabit seawater, estuaries, bays, and coastal waters, regions full of metal ions such as magnesium (Kumarage et al., 2022). Magnesium is the second most dissolved element in seawater after sodium. At a salinity of 3.5% seawater, the magnesium concentration is about 54 mM (Potis, 1968), and in deep seawater, can be as high as 2,500 mM (Wang et al., 2024). Vibrio parahaemolyticus and V. alginilyticus are two representative Vibrio pathogens that infect humans and aquatic animals, resulting in illness and economic loss, respectively (Grimes, 2020). (Fluoro)quinolones such as balofloxacin are used to treat Vibrio infection, however, resistance has emerged due to overuse (Suyamud et al., 2024). Indeed, (fluoro)quinolones are one of China's two primary residual chemicals associated with aquaculture (Liu et al., 2017). Vibrio can develop quinolone resistance through mutations in the DNA gyrase gene or through plasmid-mediated mechanisms (Dutta et al., 2021). Thus, the use of V. parahaemolyticus and V. alginilyticus as bacterial representatives, and balofloxacin as a quinolone-based antibacterial representative, can help to define novel magnesiumdependent phenotypic resistance mechanisms of pathogenic Vibrio species. 

The current study evaluated whether magnesium induces phenotypic resistance in Vibrio species and defined the molecular/genetic basis for this resistance. Genetic approaches, GC-MS analysis of metabolite and membrane remodeling upon antibiotic exposure, membrane physiology, and extensive antimicrobial susceptibility testing were used for the evaluations.”

(2) The weakest point of this paper is in the logistics through the results section. The way authors represented the figures and interpreted them in the results section (or the figure legends) does not match. The figures are difficult to interpret and are not at all self-explanatory. 

Thank you so much for your suggestion. We have followed your suggestion to check the match between result and figures. They are now revised. 

(3) There are too many mislabeling of the figure panels in the main text which makes it difficult to find out which figures the authors are explaining. There should be more explanation on why and how they did the experiments and how the results were interpreted. 

Thank you so much for your suggestion. We have checked the figures and main text to ensure that we make every figure clearly stated.  

Reviewer #2 (Public Review): 

Summary: 

In this study, the authors aimed to identify if and how magnesium affects the ability of two particular bacteria species to resist the action of antibiotics. In my view, the authors succeeded in their goals and presented a compelling study that will have important implications for the antibiotic resistance research community. Since metals like magnesium are present in all lab media compositions and are present in the host, the data presented in this study certainly will inspire additional research by the community. These could include research into whether other types of metals also induce multi-drug resistance, whether this phenomenon can be observed in other bacterial species, especially pathogenic species that cause clinical disease, and whether the underlying molecular determinants (i.e. enzymes) of metal-induced phenotypic resistance could be new antimicrobial drug targets themselves. 

Strengths: 

This study's strengths include that the authors used a variety of methodologies, all of which point to a clear effect of exogenous Mg2+ on drug resistance in the targeted species. I also commend the authors for carrying out a comprehensive study, spanning evaluation of whole cell phenotypes, metabolic pathways, genetic manipulation, to enzyme activity level evaluation. The fact that the authors uncovered a molecular mechanism underlying Mg2+-induced phenotypic resistance is particularly important as the key proteins should be studied further.

Weaknesses: 

I believe there are weaknesses in the manuscript, however. The authors take for granted that the reader is familiar with all the assays utilized, and do not properly explain some experiments, and thus I highly suggest that the authors add a brief statement in each situation describing the rationale for each selected methodology (more details are in the private review to the authors). The Results section is also quite long and bogs down at times, and I suggest that the authors reduce its length by 10 to 20%. In contrast, the Introduction is sparse and lacks key aspects, for example, there should be mention of the study's main purpose and approaches, plus an introduction to the authors' choice of species and their known drug resistance properties, as well as the drug of choice (balofloxacin). Another notable weakness is that the authors evaluated Mg2+-induced phenotypic resistance only against two closely related species, and thus the generalizability of this mechanism of drug resistance is not known. The paper would be strengthened if the authors could demonstrate this type of phenotypic resistance in at least one more Gram-negative species and at least one Gram-positive species (antimicrobial susceptibility evaluations would suffice), each of which should be pathogenic to humans. Demonstrating magnesium-induced phenotypic drug resistance in the WHO Priority Bacterial Pathogens would be particularly important. 

In general, the conclusions drawn by the authors are justified by the data, except for the interpretation of some experiments. Importantly, this paper has discovered new antimicrobial resistance mechanisms and has also pointed to potential new targets for antimicrobials. 

Thank you so much for your suggestion! We followed your idea the revise the manuscript as following:

(1) We added a brief statement in the situation to explain the result and methodology according to your suggestion in the private review.

(2) To make the streamline of the story more logic, we moved the whole second result to supplementary text and supplementary figure. 

(3) We revised the introduction part by adding additional information to make it informative and to the point as following:

“Non-inheritable antibiotic or phenotypic resistance represents a serious challenge for treating bacterial infections. Phenotypic resistance does not involve genetic mutations Phenotypic resistance does not involve genetic mutations and is transient, allowing bacteria to resume normal growth. Biofilm and bacterial persisters are two phenotypic resistance types that have been extensively studied (Brandis et al., 2023; Corona & Martinez, 2013). Biofilms have complex structures, containing elements that impede antibiotic diffusion, sequestering and inhibiting their activity (Ciofu et al., 2022). Biofilm-forming bacteria and persisters also have distinct metabolic states that significantly reduce their antibiotic susceptibility (Yan & Bassler, 2019). These two types of phenotypic resistance share the common feature in their retarded or even cease of growth in the presence of antibiotics (Corona & Martinez, 2013). However, specific factors that promote phenotypic resistance and allow bacteria to proliferate in the presence of antibiotics remain poorly defined.

Metal ions have a diverse impact on the chemical, physical, and physiological processes of antibiotic resistance  (Booth et al, 2011; Lu et al, 2020; Poole, 2017). This includes genetic elements that confer resistance to metals and antibiotics (Poole, 2017) and metal cations that directly hinder (or enhance) the activity of specific antibiotic drugs (Zhang et al., 2014). The metabolic environment can also impact the sensitivity of bacteria to antibiotics (Jiang et al., 2023; Lee & Collins, 2012; Peng et al., 2015; Zhang et al., 2020; Zhao et al., 2021). Light metal ions, such as magnesium, sodium, and potassium, can behave as cofactors for different enzymes (Du et al., 2016) and influence drug efficacy. Heavy metal ions, including Cu2+ and Zn2+, confer resistance to antibiotics (Yazdankhah et al., 2014; Zhang et al., 2018). Recent reports suggest that sodium negatively regulates redox states to promote the antibiotic resistance of Vibrio alginolyticus (Yang et al., 2018), while actively growing Bacillus subtilis cope with ribosome-targeting antibiotics by modulating ion flux (Lee et al, 2019). In Gram-negative bacteria, by contrast, zinc enhances antibiotic efficacy by potentiating carbapenem, fluoroquinolone, and β-lactam-mediated killing (Isaei et al., 2016; Zhang et al., 2014). Magnesium influences bacterial structure, cell motility, enzyme function, cell signaling, and pathogenesis (Wang et al., 2019). This mineral also modulates microbiota to harvest energy from the diet (Garcia-Legorreta et al., 2020), allowing Bacillus subtilis to cope with ribosome-targeting antibiotics by modulating ion flux (Lee et al., 2019). However, the role of magnesium in promoting phenotypic resistance is less well understood.

Vibrios inhabit seawater, estuaries, bays, and coastal waters, regions full of metal ions such as magnesium (Kumarage et al., 2022). Magnesium is the second most dissolved element in seawater after sodium. At a salinity of 3.5% seawater, the magnesium concentration is about 54 mM (Potis, 1968), and in deep seawater, can be as high as 2,500 mM (Wang et al., 2024). Vibrio parahaemolyticus and V. alginilyticus are two representative Vibrio pathogens that infect humans and aquatic animals, resulting in illness and economic loss, respectively (Grimes, 2020). (Fluoro)quinolones such as balofloxacin are used to treat Vibrio infection, however, resistance has emerged due to overuse (Suyamud et al., 2024). Indeed, (fluoro)quinolones are one of China's two primary residual chemicals associated with aquaculture (Liu et al., 2017). Vibrio can develop quinolone resistance through mutations in the DNA gyrase gene or through plasmid-mediated mechanisms (Dutta et al., 2021). Thus, the use of V. parahaemolyticus and V. alginilyticus as bacterial representatives, and balofloxacin as a quinolone-based antibacterial representative, can help to define novel magnesiumdependent phenotypic resistance mechanisms of pathogenic Vibrio species. 

The current study evaluated whether magnesium induces phenotypic resistance in Vibrio species and defined the molecular/genetic basis for this resistance. Genetic approaches, GC-MS analysis of metabolite and membrane remodeling upon antibiotic exposure, membrane physiology, and extensive antimicrobial susceptibility testing were used for the evaluations.”

(4) We examined the effect of magnesium in WHO listed priority strains, which confirmed the results as following:

“Importantly, exogenous MgCl2 also increased MICs of clinic isolates, carbapenemresistant Escherichia coli, carbapenem-resistant Klebsiella pneumoniae, carbapenemresistant Pseudomonas aeruginosa and carbapenem-resistant Acinetobacter baumannii to balofloxacin (Fig 1G).”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

(1) There are many grammatical mistakes to point out. The manuscript needs proofreading and editing.

We appreciate this comment! The manuscript has been revised by a native speaker.

(2) The introduction could be more informative. A little more description of magnesium - such as what it does to antibiotics and how it's known to affect the microbiome - might be helpful for the general readers. The question remains why out of all the metal ions that might affect antibiotic resistance (many of them are less explored), authors particularly decided to work on the effect of magnesium. The introduction should cover the rationale of their hypothesis. Also, the authors might want to briefly talk about the model organisms (V. algonolyticus and V. parahemolyticus) describing how threatening they are and how they are becoming resistant to antibiotics. 

We appreciate this comment! We revise the introduction by providing additional information as following:

“In Gram-negative bacteria, by contrast, zinc enhances antibiotic efficacy by potentiating carbapenem, fluoroquinolone, and β-lactam-mediated killing (Isaei et al., 2016; Zhang et al., 2014). Magnesium influences bacterial structure, cell motility, enzyme function, cell signaling, and pathogenesis (Wang et al., 2019). This mineral also modulates microbiota to harvest energy from the diet (Garcia-Legorreta et al., 2020), allowing Bacillus subtilis to cope with ribosome-targeting antibiotics by modulating ion flux (Lee et al., 2019). However, the role of magnesium in promoting phenotypic resistance is less well understood.

Vibrios inhabit seawater, estuaries, bays, and coastal waters, regions full of metal ions such as magnesium (Kumarage et al., 2022). Magnesium is the second most dissolved element in seawater after sodium. At a salinity of 3.5% seawater, the magnesium concentration is about 54 mM (Potis, 1968), and in deep seawater, can be as high as 2,500 mM (Wang et al., 2024). Vibrio parahaemolyticus and V. alginilyticus are two representative Vibrio pathogens that infect humans and aquatic animals, resulting in illness and economic loss, respectively (Grimes, 2020). (Fluoro)quinolones such as balofloxacin are used to treat Vibrio infection, however, resistance has emerged due to overuse (Suyamud et al., 2024). Indeed, (fluoro)quinolones are one of China's two primary residual chemicals associated with aquaculture (Liu et al., 2017). Vibrio can develop quinolone resistance through mutations in the DNA gyrase gene or through plasmid-mediated mechanisms (Dutta et al., 2021). Thus, the use of V. parahaemolyticus and V. alginilyticus as bacterial representatives, and balofloxacin as a quinolone-based antibacterial representative, can help to define novel magnesiumdependent phenotypic resistance mechanisms of pathogenic Vibrio species. 

The current study evaluated whether magnesium induces phenotypic resistance in Vibrio species and defined the molecular/genetic basis for this resistance. Genetic approaches, GC-MS analysis of metabolite and membrane remodeling upon antibiotic exposure, membrane physiology, and extensive antimicrobial susceptibility testing were used for the evaluations. ”

(3) Figure 1C is mislabeled as 1B (line 100). Line 101: The sentence is not clear and very confusing. What is meant by 15.6mM - 62.4 mM? Are they talking about the concentration of BLFX (though in the figure the concentration was shown in µg)? Please rewrite the sentence in a simplified way. Also, the zone of inhibition was decreased with increasing MgCl2, not increased. 

We appreciate this comment! These have been revised, including that Fig 1B is now corrected as Fig. 1C. Line 101, which is now Line 122. The sentence was revised as following:

“At balofloxacin doses of 1.56, 3.125, 6.25, and 12.5 µg, the zone of inhibition decreased with increasing MgCl2 (Fig 1D)”

(4) In the western blot images, it would be nice to indicate the MW of the protein bands shown. The loading control used for the experiments should be clearly mentioned in the figure legends. 

We appreciate this comment! The MWs are indicated in the western-blot image throughout the manuscript. 

The loading control is clearly stated in the figure legend as following:

“Whole cell lysates resolved by SDS-PAGE gel was stained with Coomassie brilliant blue as loading control.”. 

(5) Figures 2 B and C: the figure legend does not explain what the authors wanted to show. It's not clear how they plotted the inhibitory curve, or the binding efficacy. These panels need an explanation of how the analysis was done.

We appreciate this comment! The figure 2 is now removed to Suppl. Fig 2, and the description of figure 2 is moved to Suppl. Text. We revise the description of the result as following, which is in Suppl. Text:

“Prior studies suggest that the chelation of antibiotics by magnesium ions inhibits antibiotic uptake (Deitchman et al., 2018; Lunestad and Goksøyr, 1990). To investigate whether magnesium binds to balofloxacin, balofloxacin was pre-incubated with magnesium, and zone of inhibition (ZOI) analysis was conducted. Six different concentrations of balofloxacin were separately incubated with six different concentrations of MgCl2, and then spotted on filter paper so that a defined amount of balofloxacin could be used for ZOI. While lower concentrations of MgCl2, (0.78, 3.125, or 12.5 mM) did not alter the ZOI, higher concentrations, including 50 and 200 mM MgCl2, decreased the ZOI (Suppl. Fig 2A), suggesting that even high doses of magnesium had only a partial effect on balofloxacin through direct binding. For example, at 200 mM MgCl2 and 5 or 10 μg/mL balofloxacin, the balofloxacin ZOI was 53.2 and 70.3% of the ZOI at 0 mM MgCl2, suggesting that  50% of the antibiotics were still functional. Intracellular BLFX also decreased with increasing MgCl2 (Suppl. Fig 2B), while exogenous Mg2+ increased intracellular Mg2+ levels in a dose-dependent manner. For example, exogenous 50 and 200 mM MgCl2 increased intracellular Mg2+ levels to 1.21 and 1.31 mM, respectively (Suppl. Fig 2C). The relationship between TolC, an efflux pump that transports quinolones from bacterial cells, and Mg2+ was also assessed (Kobylka et al., 2020; Song et al., 2020). The expression of TolC/tolC was unaffected by Mg2+ (Suppl. Fig 2D). Magnesium is critical for LPS stability. LPS levels increased at 200 mM Mg2+ (Suppl. Fig 2E), however, the loss of waaF, lpxA, and lpxC, three key genes involved in LPS biosynthesis, did not influence balofloxacin sensitivity/resistance in the presence of Mg2+ (Suppl. Fig 2F). These findings suggest that magnesium-induced LPS biosynthesis does not contribute directly to BLFX resistance and demonstrate that Mg2+ influx is involved in balofloxacin resistance.”

(6) For the metabolomics results, it will help immensely if the authors provide a volcano plot of the identified metabolites and plot the heat map according to the -log2 metabolite intensities. In Figure 3A, it's not clear what information is conveyed through Euclidean distance calculations of the heat map. In Figure 3 B, the authors mentioned that the OPLS-DA test was conducted, although the figure shows a PCA plot, so it's not clear how these two are connected. Figure 3 E: the figure legend says scattered plot, but the panel represents color-coded numerical values, not a scattered plot. Also, it's not clear how they got those values. 

We appreciate this comment! We quite agree with you that if the differential metabolites could be shown as volcano plot. However, we didn’t adopt volcano plot in this study because this is a magnesium concentration-dependent metabolomes that includes 6 groups in parallel. Volcano plots may give a complex view of the comparison among different groups. We also tried to plot the heat map according to the -log2 metabolite intensities. Although this analysis cluster 200 mM and 50 mM groups better, the data of low magnesium concentrations was not consistent, which may be due to the minor metabolic change of low concentrations magnesium. Thank you for your understanding. 

For Euclidean distance calculations, we explain in the figure legend as following:

“Euclidean distance calculations were used to generate a heatmap that shows clustering of the biological and technical replicates of each treatment.” 

In Figure 2B, which was Figure 3B in previous version, it has been replaced with OPLS-DA analysis in the revised version. 

In Figure 2E, which was Figure 3E in previous version, it is revised as following:

“E. Areas of the peaks of palmitic acid and stearic acid generated by GC-MS analysis.” 

(7) In Figure 4, the figure legends (as well as the in the text) are not properly referred to. Please make sure to refer to the correct panel. 

We appreciate this comment! The figure legends have been corrected to match the panel and text. 

Figure 4F: how was the synergy analysis done? In the methods section, the authors described the antibiotic bactericidal assay protocol, but there was no clear indication of how they generated the isobologram. 

We appreciate this comment! We provide additional information in the Figure 3F legend, which was Figure 4F in previous version,  as following: 

“Synergy analysis for BFLX with palmitic acid for V. alginolyticus. Synergy was performed by comparing the dose needed for 50% inhibition of the synergistic agents (white) and non-synergistic (i.e., additive) agents (purple).”

(8) Figure 5 A: the scatter plot is plotted according to the area along the Y axis: which "area" is represented here? There is absolutely no explanation, neither in the results nor in the figure legends. Using box plots might be a better option than using a scattered plot.

We appreciate this comment! “Area” has been noted in the revised manuscript as following:

“The area indicates the area of the peak of the metabolite in total ion chromatography of GC-MS.” 

(9) In Figure 6 A, the heat map is plotted according to the column Z scores. What is meant by "column Z score"? The corresponding figure legend says, "heat map showing differential abundance of lipid". Z scores do not represent an abundance of a variable, so the conclusion might not be appropriate here. 

We appreciate this comment! In Figure 5A, which was Figure 6A in previous version, column Z score shows the abundance of metabolites analyzed, which is automatically generated in the heat map analysis to give a sign of these metabolites tested. The legend has been revised as following: 

“Heatmap showing changes in differential lipid levels at the indicated concentration of MgCl2.”  

(10) Line 313-314: it should be Figure EV6C.  

We appreciate this comment! The citation has been corrected.

(11) The authors have shown that Mg+2 does not alter the LPS transport system, however, there was some significant increase in LPS expression at 200mM MgCl2. It would be interesting if the authors could also check if Mg+2 has any effect on the outer membrane protein (OMP) integrity (by checking OMP components BamA and LptD).  

We appreciate this comment!  We have carefully examined the membrane permeability in Figure 7. We thus didn’t perform additional experiment here to see the change of BamA and LptD. Thank you very much for your understanding.

(12) I wonder if the authors could check the effect of extracellular Mg+2 during the co-treatment of palmitic acid, linoleic acid, and balofloxacin. Will there still be the antagonistic effect or the presence of Mg+2 could change the phenotype? 

We appreciate this comment! Additional experiments is performed as following:

“Furthermore, magnesium had a minimal effect on the antagonistic effect of palmitic acid, linolenic acid, and balofloxacin (Fig 4G), suggesting that this mineral functions through lipid metabolism.” 

Reviewer #2 (Recommendations For The Authors): 

(1) As mentioned in the Public Review, I strongly believe that the impact of this study will be more significant if magnesium-induced phenotypic drug resistance could be demonstrated in at least one other Gram-negative and one other Grampositive species, both of which should be human pathogens. The full suite of experiments would not be necessary for this suggestion; evaluation of the effect of Mg concentration in growth media on the drug resistance of other species, testing the different antibiotic types used in this study, would be sufficient. 

We appreciate this comment! Additional experiments have performed to test this idea. Mg2+ has the similar effect on carbapenem-resistant Escherichia coli, carbapenem-resistant Klebsiella pneumoniae, carbapenem-resistant Pseudomonas aeruginosa and carbapenem-resistant Acinetobacter baumannii as the similar as on the Vibrio species in shown in Figure 1G. These have been described following as

“Importantly, exogenous MgCl2 also increased MICs of clinic isolates, carbapenemresistant Escherichia coli, carbapenem-resistant Klebsiella pneumoniae, carbapenemresistant Pseudomonas aeruginosa and carbapenem-resistant Acinetobacter baumannii to balofloxacin (Fig 1G).”

(2) I recommend that the Introduction section be expanded. I recommend one or two sentences introducing the two Vibrio species selected for study. I.e. why did the authors choose these two species? What is known about their phenotypic drug resistance in the literature? Why did the authors select balofloxacin for their studies, is it a common antimicrobial used vs Vibrios? As well, the end of the Introduction section ends abruptly with no transition to the present study itself. The end of the introduction should include one or two sentences introducing the main purpose of the study, its approach, and the techniques undertaken. For example, "In this study, we evaluated whether magnesium induces phenotypic resistance in Vibrio species and the molecular/genetic basis for such resistance. We used genetic approaches, GC-MS analysis of metabolite and membrane remodeling upon antibiotic exposure, membrane physiology, and extensive antimicrobial susceptibility evaluations." 

We appreciate this comment! We revise the introduction by providing additional information as following:

“In Gram-negative bacteria, by contrast, zinc enhances antibiotic efficacy by potentiating carbapenem, fluoroquinolone, and β-lactam-mediated killing (Isaei et al., 2016; Zhang et al., 2014). Magnesium influences bacterial structure, cell motility, enzyme function, cell signaling, and pathogenesis (Wang et al., 2019). This mineral also modulates microbiota to harvest energy from the diet (Garcia-Legorreta et al., 2020), allowing Bacillus subtilis to cope with ribosome-targeting antibiotics by modulating ion flux (Lee et al., 2019). However, the role of magnesium in promoting phenotypic resistance is less well understood.

Vibrios inhabit seawater, estuaries, bays, and coastal waters, regions full of metal ions such as magnesium (Kumarage et al., 2022). Magnesium is the second most dissolved element in seawater after sodium. At a salinity of 3.5% seawater, the magnesium concentration is about 54 mM (Potis, 1968), and in deep seawater, can be as high as 2,500 mM (Wang et al., 2024). Vibrio parahaemolyticus and V. alginilyticus are two representative Vibrio pathogens that infect humans and aquatic animals, resulting in illness and economic loss, respectively (Grimes, 2020). (Fluoro)quinolones such as balofloxacin are used to treat Vibrio infection, however, resistance has emerged due to overuse (Suyamud et al., 2024). Indeed, (fluoro)quinolones are one of China's two primary residual chemicals associated with aquaculture (Liu et al., 2017). Vibrio can develop quinolone resistance through mutations in the DNA gyrase gene or through plasmid-mediated mechanisms (Dutta et al., 2021). Thus, the use of V. parahaemolyticus and V. alginilyticus as bacterial representatives, and balofloxacin as a quinolone-based antibacterial representative, can help to define novel magnesiumdependent phenotypic resistance mechanisms of pathogenic Vibrio species. 

The current study evaluated whether magnesium induces phenotypic resistance in Vibrio species and defined the molecular/genetic basis for this resistance. Genetic approaches, GC-MS analysis of metabolite and membrane remodeling upon antibiotic exposure, membrane physiology, and extensive antimicrobial susceptibility testing were used for the evaluations. ”

(3) The authors introduce the acronym AWST but never use it again in the paper, instead they use SWT. The authors should introduce SWT only for consistency. 

We appreciate this comment! We have corrected all the “SWT” to “ASWT”

(4) Line 76 is not clear: what is meant by "some of which could influence drug efficacy" - the enzymes that utilize light metal ions are co-factors? Or the metals directly?  

We appreciate this comment! The information we wanted to deliver is that light metal ions can serve as cofactors to catalyze biochemical reaction. Such chemical reaction would alter the drug efficacy, e.g. the Fe-S cluster are metallocofactor for proteins which regulates redox chemistry including antibioticinduced redox change. However, this information is not appropriate for this manuscript, so we delete this sentence. 

(5) Line 90: add a reference corroborating that this chemical composition is a mimic of marine water. The NaCl concentration used in particular looks quite low. 

We appreciate this comment! It was a typo error. The NaCl concentration was 210 mM as shown in Suppl. Table 1. We also provide details of the chemical composition of the marine water as following:

“Marine environments and agriculture, where antibiotics are commonly used, are rich in magnesium. To investigate whether this mineral impacts antibiotic activity, the minimal inhibitory concentration (MIC) of V. alginolyticus ATCC33787 and V. parahaemolyticus VP01, which we referred as ATCC33787 and VP01 afterwards, isolated from marine aquaculture, to balofloxacin (BLFX) in Luria-Bertani medium

(LB medium) plus 3% NaCl as LBS medium and “artificial seawater” (ASWT) medium that included the major ion species in marine water (Wilson, 1975) (LB medium plus 210 mM NaCl, 35 mM Mg2SO4, 7 mM KCl, and 7 mM CaCl2) were assessed”

(6) Line 98 and Figure 1B. M9 is indicated in the text but does not appear in the figure, the figure only shows SWT. This should be checked. Line 99: based on Figure 1C, the authors are adding MgCl2 to SWT, SWT should be mentioned in this line. Line 100: I believe this is referring to Figure 1C, which should be checked. 

We appreciate this comment! 

Line 98, which is now Line 118: We have corrected M9 to ASWT as following:

“However, the MIC for BLFX was higher in ASWT medium supplemented with Mg2SO4 or MgCl2 than in LB medium (Fig 1B).”

Line 99, which is now Line 133: the sentence is corrected as following:

“The MIC for BLFX increased at higher concentrations of MgCl2 in ASWT”

Line 100, which is now Line 135: we have corrected Fig 1B to Fig. 1C.

(7) Line 101: text and Figure 1D are not consistent, as Figure 1D does not show this level of precision in added MgCl2 as indicated in the text (15.6 - 62.4 mM).  

We appreciate this comment! The sentence has been corrected as following: “At balofloxacin doses of 1.56, 3.125, 6.25, and 12.5 µg, the zone of inhibition decreased with increasing MgCl2 (Fig 1D)””.  

(8) MgCl2 clearly induces increasing levels of BLFX resistance, and to high levels, but not for every antibiotic. For example, the level of increased resistance to blactams is low (ceftriaxone) and plateaus (ceftazidime). As well, resistance to gentamicin plateaus at a lower level than the other aminoglycosides. These observations do not take away from the conclusion that Mg induces multi-drug resistance, but since the behaviour of the MICs for these drugs is different than the other drugs, they should be mentioned. Also, Figure 1F - tetracyclines (plural) is used for vertical axis label - does this refer to the tetracycline itself or the class itself, and if the class, which one was tested? 

We appreciate this comment! We revise the description as following: “Notably, magnesium had a reduced effect on ceftriaxone and gentamicin than other antibiotics.”

The tetracyclines is labeled as “Oxytetracycline” in the revised manuscript. 

- The magnesium chelation experiments presented in Figure 2 are not clear. The authors should briefly mention how this was done around line 128, and what data underlies the values in Figure 2C. Figure 2B is also not clear to me at all. Similarly, how the authors measured intracellular balofloxacin and Mg2+ is not clear and should be mentioned briefly around lines 130-132. 

We appreciate this comment! These have been rewritten following as  “To investigate whether magnesium binds to balofloxacin, balofloxacin was preincubated with magnesium, and zone of inhibition (ZOI) analysis was conducted. Six different concentrations of balofloxacin were separately incubated with six different concentrations of MgCl2, and then spotted on filter paper so that a defined amount of balofloxacin could be used for ZOI. While lower concentrations of MgCl2, (0.78, 3.125, or 12.5 mM) did not alter the ZOI, higher concentrations, including 50 and 200 mM MgCl2, decreased the ZOI (Suppl. Fig 2A), suggesting that even high doses of magnesium had only a partial effect on balofloxacin through direct binding. For example, at 200 mM MgCl2 and 5 or 10 μg/mL balofloxacin, the balofloxacin ZOI was 53.2 and 70.3% of the ZOI at 0 mM MgCl2, suggesting that  50% of the antibiotics were still functional. Intracellular BLFX also decreased with increasing MgCl2 (Suppl. Fig 2B), while exogenous Mg2+ increased intracellular Mg2+ levels in a dose-dependent manner. For example, exogenous 50 and 200 mM MgCl2 increased intracellular Mg2+ levels to 1.21 and 1.31 mM, respectively (Suppl. Fig 2C). The relationship between TolC, an efflux pump that transports quinolones from bacterial cells, and Mg2+ was also assessed (Kobylka et al., 2020; Song et al., 2020). The expression of TolC/tolC was unaffected by Mg2+ (Suppl. Fig 2D). Magnesium is critical for LPS stability. LPS levels increased at 200 mM Mg2+ (Suppl. Fig 2E), however, the loss of waaF, lpxA, and lpxC, three key genes involved in LPS biosynthesis, did not influence balofloxacin sensitivity/resistance in the presence of Mg2+ (Suppl. Fig 2F). These findings suggest that magnesium-induced LPS biosynthesis does not contribute directly to BLFX resistance and demonstrate that Mg2+ influx is involved in balofloxacin resistance.”

- Line 135: LPS cannot be "expressed", as the authors word it here. This should be corrected. Also, the inspection of Figure 2G actually shows the levels of LPS increase with increased Mg2+. The authors should re-evaluate these results and change their description around this area of the Results. 

We appreciate this comment! We have removed the whole Figure 2 to Supplementary Text and Supplementary Figure 2. We rewrite this part as following: “The relationship between TolC, an efflux pump that transports quinolones from bacterial cells, and Mg2+ was also assessed (Kobylka et al., 2020; Song et al., 2020). The expression of TolC/tolC was unaffected by Mg2+ (Suppl. Fig 2D). Magnesium is critical for LPS stability. LPS levels increased at 200 mM Mg2+ (Suppl. Fig 2E), however, the loss of waaF, lpxA, and lpxC, three key genes involved in LPS biosynthesis, did not influence balofloxacin sensitivity/resistance in the presence of Mg2+ (Suppl. Fig 2F). These findings suggest that magnesium-induced LPS biosynthesis does not contribute directly to BLFX resistance and demonstrate that Mg2+ influx is involved in balofloxacin resistance.”

- Section: MgCl2 affects bacterial metabolism. Authors switched to M9 medium - why? This contrasts with other sections using SWT and should be explained. Also, I cannot evaluate whether the statistical analysis of the data here was performed correctly and was appropriate for this type of experiment. I advise the authors to move the details in lines 166-169 to the Materials and Methods and replace this section instead with a more accessible description of the statistical analysis that a non-expert would be able to appreciate. Furthermore, analysis of Figure 3A indicates that the levels of asparagine, 4-hydroxybutyric acid, uracil, cystathionine, fumaric acid, and aminoethanol have significantly changed at high MgCl2, but these are not mentioned in the text. I suggest the authors mention these if they are relevant to the 12 enriched pathways, especially the biosynthesis of fatty acids. 

We appreciate this comment! 

We indicate the reason we use M9 medium as following:

“To better understand how magnesium affects bacterial metabolism” for explaining why the M9 medium was used.”

The information lines 166-169 indicated has been removed to M &M. 

We have carefully examined the abundance of the metabolites and the enriched pathway. Among the listed metabolites, only fumarate is within the enriched pathways. We mention this point in our revised manuscript as following:

“The increase in fatty acid biosynthesis could be partially explained by an imbalanced pyruvate cycle/TCA cycle, in which fumarate levels increased at higher Mg2+ while succinate levels increased at lower Mg2+ (Suppl. Fig 5B). These findings indicated that glycolysis fluxes into fatty acid biosynthesis rather than the pyruvate cycle/TCA cycle. The relevance of fatty acids and BLFX was demonstrated by the observation that exogenous palmitic acid increased bacterial resistance to balofloxacin (Fig 2F). These results suggest that fatty acid metabolism may be critical to magnesium-based phenotypic resistance.”

- Line 211 appears to refer to Figure 4F and should be checked. Similarly in line 216 - appears this should be Figure 4H, and line 218 should be Figure 4H. Line 226: add a reference to Fig 4I (after arcA was decreased). Line 227: what are genes N646_1004 and N646_1885? Based on Fig 4J these are crp - authors should add to line 227. Line 228 appears to refer to Figure 4J, not Figure 4I. Line 229 - should be Figure 4K, not Figure 4I. Line 231 - should be 4L, not 4K. Line 239 - should be 4M.

We appreciate this comment! The text and figure is now matched. 

- Line 312: the descriptions of "11 lipids, 32 lipids, and 53", and then "26 lipids, 52 lipids, and 107 lipids" are not clear at all and should be corrected. 

We appreciate this comment! The sentence is revised as following:

“The abundance of 11, 32, and 53 lipids was increased in 3.125, 50, and 200 mM MgCl2-treated bacteria, respectively, while the abundance of 26, 52, and 107 lipids was decreased in 3.125, 50, and 200 mM MgCl2-treated bacteria, respectively (Suppl. Fig 7C)”

- Line 340. What is the assay the authors are using to measure the levels of the PGS and PSS enzymes? This is not mentioned or clear in this part of the Results.  

We appreciate this comment!  We provide the information in the manuscript as following:

“Levels of PGS and PSS were quantified by ELISA kits according to manufacture’s instruction (Shanghai Fusheng Industrial Co., Ltd., China)”

- Line 372: What is the assay for measuring membrane depolarization? This is not mentioned and I suggest it should be. Line 374: Figure 7B does not show time dependence, only dose dependence, this should be corrected, it is assumed the authors are referring to Fig 7C for the time dependence data. 

We appreciate this comment! We provide the information in the result as following:  

“The voltage-sensitive dye, DiBAC4(3) showed that 12.5–200 mM MgCl2 promoted membrane depolarization in a dose-dependent manner (Fig 6A)”

We also explain how DiBAC4(3) can be used to measure membrane depolarization in the Materials and Methods section as following:

“DiBAC4(3) is a s voltage-sensitive probe that penetrates depolarized cells, binding intracellular proteins or membranes exhibiting enhanced fluorescence and red spectral shift.”

To make it clear the specific figure, we revise the sentence as following:

“Meanwhile, MgCl2 had a dose-dependent (Fig 6B) and time-dependent (Fig 6C) effect on proton motive force (PMF).”

- Line 384: mention how FM5-95 measures membrane permeability. The authors should also clarify how this reagent is used to measure membrane fluidity, and it is not clear if the data for this is presented in Figure 7 - please clarify. Regarding SYTO9 dye experiment: the authors should briefly explain the experimental design - how SYTO9 dye operates and why FACS was chosen. What is labeled with FITC?  

We appreciate this comment! We clarify the reason we use FM5-95 in the Methods and Materials section as following:

“Measurement of fluidity by fluorescence microscopy

Measurement of membrane fluidity is performed as previously described (Wen et al., 2022). Briefly, ATCC33787 were cultured in medium with indicated concentrations of MgCl2, collected and then adjusted to OD 0.6. Aliquot of 100 μL bacteria cells of each sample were diluted to 1 mL and 10 μL (10 mg/mL) FM5-95 (Thermo Fisher

Scientific, USA) was added. FM5-95 is a lipophilic styryl dye that insert into the outer leaflet of bacterial membrane and become fluorescence. This dye preferentially bind to the microdomains with high membrane fluidity(Wen et al., 2022). After incubated for 20 min at 30 ℃ at vibration without light, the sample was centrifuged for 10 min at 12,000 rpm. The pellets were resuspended with 20 μL of 3% NaCI. Aliquot of 2 μL sample was dropped on the agarose slide, and take photos under the inverted fluorescence microscope.”

This data is presented as micrographs in Fig. 6D, which shows the decreased FM5-95 staining with increasing concentrations of MgCl2. We make this description clear with the following revision:

“FM5-95 staining decreased with increasing concentrations of Mg2+, and no staining was observed in the presence of 200 mM Mg2+ (Fig 6D).”

We explain the reason why we use SYTO9 as following:

“SYTO9, a green fluorescent dye that binds to nucleic acid, enters and stains bacteria cells when there is an increase in membrane permeability (Lehtinen et al., 2004; McGoverin et al., 2020). Staining decreased with increasing MgCl2, indicating that bacterial membrane permeability declined in an Mg2+ dose-dependent manner (Fig 6E).”

We didn’t use FACS in this study, while we only analyze the fluorescence distribution with the equipment. To make it clear, we revise the sentence as following:

“After incubated for 15 min at 30 ℃ at vibration without light, the mixtures were filtered and measured by flow cytometry (BD FACSCalibur, USA).”

- Lines 391-397. The statement that palmitic acid shifts the peaks in Figure 7F is not supported by the data. There is essential no change in the major peak position within each MgCl2 concentration set with increasing palmitic acid. For the linolenic acid data, it is clear that linolenic acid increases permeability only at 50 mM MgCl2-this should be mentioned in the text. 

We appreciate this comment! We revise the sentence as following:

“Exogenous palmitic acid also shifted the fluorescence signal peaks to the left in an MgCl2-dependent manner while palmitic acid only slightly shifted the peaks (Fig 6F). In contrast, exogenous linolenic acid shifted the peak to the right in a dose-dependent manner at 50 mM MgCl2 (Fig 6G).” 

- Line 404-405 - as mentioned earlier, the assay for the update of BLFX should be mentioned (if it is done so earlier in the text, then it does not need to be here).  

We appreciate this comment! It has been mentioned in the introduction.  

- Discussion: CpxA/R-OmprF pathway is mentioned here for the first time. Is this one of the pathways modified by MgCl2 as determined during the course of the study? If so, this should be reworded to mention that. If not, the relevance of this particular pathway as it relates to light metals and phenotypic resistance should be discussed.

We appreciate this comment! Since it is not relevant to the discussion of Mg2+ and fatty acid biosynthesis, we delete this sentence in the revised manuscript.  

-The following grammatical errors should be corrected:

-line 55 change to: "genetic mutations; instead, this type of resistance is transient, and bacteria resume normal growth"

-line 57: change to "resistance types are biofilm" 

-line 61: change to "states that significantly" 

-line 63: change to "resistance share the common feature in they retard or even cease in the presence" 

-line 65: change to "resistance that allow bacteria to proliferate" 

-line 81: change "But whether" to "Whether" 

-line 178: change to "may be critical to the Mg-based phenotypic resistance"

-line 86: change to "Marine environments and agriculture are rich in magnesium, where..." 

-line 93: change in to vs

-line 154: insert space after metabolism 

-line 158: change 'identified" to "focused on the levels of" 

-line 160: change "The levels of forty-one metabolites" 

-line 198: change shared to share 

-line 310: increased is duplicated, delete one 

-line 451: add "the" before ratio 

-line 453: gram should be capitalized 

-line 462: "the regulation" should be reworded to "More importantly, the effect of exogenous MgCl targets the..." 

-line 469: add dash between Mg2+ and limited

-line 478: change "the crucial" to "a crucial" 

-there are numerous locations in the manuscript where the word "magnetism" is used when clearly the word is supposed to be magnesium - this should be corrected

We appreciate this comment! These have been corrected or revised. 

Editors comments:

Page 2 line 27; Page 25 line number 426; page 27 line number 481: In the abstract and discussion, only Vibrio alginolyticus was mentioned, even though two Vibrio species were used in the study. It would be helpful to understand the rationale behind the focus on this particular species.

We appreciate this comment! We have revised the introduction to provide additional information as following:

“Vibrios inhabit seawater, estuaries, bays, and coastal waters, regions full of metal ions such as magnesium (Kumarage et al., 2022). Magnesium is the second most dissolved element in seawater after sodium. At a salinity of 3.5% seawater, the magnesium concentration is about 54 mM (Potis, 1968), and in deep seawater, can be as high as 2,500 mM (Wang et al., 2024). Vibrio parahaemolyticus and V. alginilyticus are two representative Vibrio pathogens that infect humans and aquatic animals, resulting in illness and economic loss, respectively (Grimes, 2020). (Fluoro)quinolones such as balofloxacin are used to treat Vibrio infection, however, resistance has emerged due to overuse (Suyamud et al., 2024). Indeed, (fluoro)quinolones are one of China's two primary residual chemicals associated with aquaculture (Liu et al., 2017). Vibrio can develop quinolone resistance through mutations in the DNA gyrase gene or through plasmid-mediated mechanisms (Dutta et al., 2021). Thus, the use of V. parahaemolyticus and V. alginilyticus as bacterial representatives, and balofloxacin as a quinolone-based antibacterial representative, can help to define novel magnesium-dependent phenotypic resistance mechanisms of pathogenic Vibrio species.”

On Page 2, line 34: The abstract contains some undefined abbreviations, such as 'PE' and 'PG', which should be explained. 

We appreciate this comment! We explain the PE and PG in the revised abstract as following:

“phosphatidylethanolamine (PE) biosynthesis is reduced and phosphatidylglycerol (PG)”

On Page 2, line 31-32: For the statement "Exogenous supplementation of fatty acids confirm the role of fatty acids in antibiotic resistance…" it would be beneficial to specify whether the fatty acids were saturated or unsaturated. 

Response, We appreciate this comment! We revise the sentence as following:

“Exogenous supplementation of unsaturated and saturated fatty acids increased and decreased bacterial susceptibility to antibiotics, respectively, confirming the role of fatty acids in antibiotic resistance.”

The potential effects of the specific ions (SO4 and Cl2) present in the Mg2SO4 and MgCl2 compounds used in the study were not discussed. It would be useful to understand if these ions had any influence on the observed outcomes.

We appreciate this comment! We revise the sentence as following:

“However, the MIC for BLFX was higher in ASWT medium supplemented with Mg2SO4 or MgCl2 than in LB medium (Fig 1B). And Mg2SO4 or MgCl2 had no

difference on MIC, suggesting it is Mg2+ not other ions contribute to the MIC change.”

On Page 8, line 141: The heading of Figure 2, "Mg2+ elevates intracellular Mg2+," seems redundant and could be revised for clarity or modified. 

We appreciate this comment! Figure 2 is now moved to supplementary figure as Suppl. Fig 2. The title is revised as following:

“Figure 2. Mg2+ decreases balofloxacin uptake.”

On Page 4, line 91: some terms/abbreviations, such as 'LB' and 'M9,' require expansion or definition to ensure the reader's understanding.

We appreciate this comment! We include the expansion for LB and M9 in the  revised manuscript as following:

“Luria-Bertani medium (LB medium)” and “M9 minimal medium (M9 medium)”

Page 4, line 92: The real seawater composition used in the experiments should be supported by a reference.

We appreciate this comment! We provide the reference in the revised manuscript as following:

““artificial seawater” (ASWT) medium that included the major ion species in marine water (Wilson, 1975) (LB medium plus 210 mM NaCl, 35 mM Mg2SO4, 7 mM KCl, and 7 mM CaCl2)”

Page 4 line, number 93: the he full names of the bacterial strains (e.g., ATCC33787 and VP01) should be provided instead of just the strain numbers.

We appreciate this comment! We revised the sentence as following:

“To investigate whether this mineral impacts antibiotic activity, the minimal inhibitory concentration (MIC) of V. alginolyticus ATCC33787 and V. parahaemolyticus VP01, which we referred as ATCC33787 and VP01 afterwards,”

Finally, there appears to be a potential contradiction between the statements on page 12, lines 211-212 and 214-216, regarding the effects of Mg2+ on the synthesis of unsaturated fatty acids. Further explanation may be needed to reconcile these seemingly contradictory points.

We appreciate this comment! For line 221-226, which was previously line 211-212, is about the gene expression for fatty acid biosynthesis. While, Line 228 and 233, which was previously line 214-216 is about the gene expression for fatty acid degradation. We agree that the previous description is a little bit confuse. We revise the sentence to emphasize that we focus on fatty acid degradation so that the readers can tell them apart. 

In the text, we revised it as following:

“In addition, we also quantified gene expression during fatty acid degradation to determine whether Mg2+ affects this process”  In the figure legend, we also indicate that 

“H. qRT-PCR for the expression of genes encoding fatty acid degradation in the absence or presence of the indicated concentrations of MgCl2”

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper Homan et al used mouse models of Metabolic Dysfunction-Associated Steatotic Liver Disease and different specific target deletions in cells to rule out the role of Complement 3a Receptor 1 in the pathogenesis of disease. They provided limited evidence and only descriptive results that despite C3aR being relevant in different contexts of inflammation, however, these tenets did not hold true.

Weaknesses:

(1) The results are based on readouts showing that C3aR is not involved in the pathogenesis of liver metabolic disease.

(2) The description of the mouse models they used to validate their findings is not clear. Lysm-cre mice - which are claimed to delete C3aR in (?) macrophages are not specific for these cells, and the genetic strategy to delete C3aR in Kupffer cells is not clear.

(3) Taking this into account, it is very challenging to determine the validity of these data, also considering that they are merely descriptive and correlative.

We generated 2 different cohorts of mice using LysM-Cre (Jackson Strain #004781) to drive deletion in all macrophages and Clec4f-Cre (Jackson Strain #033296) to specifically ablate C3ar1 in Kupffer cells. These experimental models have been clearly defined in the revised manuscript on pages 5 and 7 and in the methods section (page 10). The reviewer’s point is well taken that the LysM-Cre transgene can also be active in granulocytes and some dendritic cells. Even so, despite deletion of C3ar1 in macrophages and other granulocytes, we do not see a major effect on hepatic steatosis and fibrosis in this GAN diet induced model of MASLD/MASH. This was a somewhat surprising finding. We do not agree that our findings are correlative. We specifically ablated C3aR1 in macrophages or Kupffer cells and found no significant differences in the major readouts of steatosis and fibrosis for MASLD/MASH between control and knockout mice. It is possible that in other models of liver injury that we did not test (e.g., short-term treatment with a hepatotoxin such as carbon tetrachloride), there may be differences in liver injury in mice lacking C3ar1 in macrophages, but the GAN diet model has been shown to better parallel the gene expression changes in human MAFLD/MASH. This has been added to the discussion (page 9).

Reviewer #2 (Public review):

Summary:

Homan et al. examined the effect of macrophage- or Kupffer cell-specific C3aR1 KO on MASLD/MASH-related metabolic or liver phenotypes.

Strengths:

Established macrophage- or Kupffer cell-specific C3aR1 KO mice.

Weaknesses:

Lack of in-depth study; flaws in comparisons between KC-specific C3aR1KO and WT in the context of MASLD/MASH, because MASLD/MASH WT mice likely have a low abundance of C3aR1 on KCs.

Homan et al. reported a set of observation data from macrophage or Kupffer cell-specific C3aR1KO mice. Several questions and concerns as follows could challenge the conclusions of this study:

(1) As C3aR1 is robustly repressed in MASLD or MASH liver, GAN feeding likely reduced C3aR1 abundance in the liver of WT mice. Thus, it is not surprising that there were no significant differences in liver phenotypes between WT vs. C3aR1KO mice after prolonged GAN diet feeding. It would give more significance to the study if restoring C3aR1 abundance in KCs in the context of MASLD/MASH.

GAN diet feeding resulted in higher liver C3ar1 compared to regular diet (Figure 1H). This thus became an impetus for studying the effects of C3ar1 deletion in macrophages or Kupffer cells, which are responsible for the majority of liver C3ar1 expression, in MASLD/MASH (Figures 2B and 3H). This point has been added to the text on page 5.

(2) Would C3aR1KO mice develop liver abnormalities after a short period of GAN diet feeding?

We did not assess if short term GAN diet feeding resulted in significant differences in liver abnormalities in the C3ar1 macrophage or Kupffer cell knockout mice. Perhaps the reviewer’s point is that perhaps with shorter periods of GAN diet feeding there may be a phenotype in the KO mice. We agree that this is entirely possible, though with shorter feeding timeframes what is typically seen is hepatic steatosis without fibrosis. Nevertheless, the most important element in our opinion for a disease preventing or modifying model lies with the longer-term GAN diet feeding. With long term GAN diet feeding that has been previously shown to model human MASLD/MASH, we did not observe significant differences in liver abnormalities with the KO mice. This has been added to the discussion (page 8).

(3) What would be the liver macrophage phenotypes in WT vs C3aR1KO mice after GAN feeding?

Similar to the above point, given the lack of a major MASLD/MASH phenotype in hepatic steatosis and fibrosis, we did not further profile the liver macrophage profiles of the macrophage or Kupffer cell C3ar1 KO mice with GAN feeding.

(4) In Fig 1D, >25wks GAN feeding had minimal effects on female body weight gain. These GAN-fed female mice also develop NASLD/MASH liver abnormalities?

We thank the reviewer for this question. In general, female GAN-fed mice develop milder MASLD/MASH abnormalities. We have included additional data in the revised manuscript in Figure S4. These results show no to minimal development of a MASLD/MASH gene signature.

(5) Would C3aR1KO result in differences in liver phenotypes, including macrophage population/activation, liver inflammation, lipogenesis, in lean mice?

We have provided additional data further characterizing liver inflammation, lipogenesis and macrophages in macrophage C3ar1 KO mice under lean/regular diet conditions in Figure 2K. These results show a potential trend but no substantial development of a MASLD/MASH gene signature.

(6) The authors should provide more information regarding the generation of KC-specific C3aR1KO. Which Cre mice were used to breed with C3aR1 flox mice?

Clec4f-Cre transgenic mice were used to generate Kupffer cell specific KO of C3ar1. This has been clarified and explicitly stated in the revised manuscript on page 7 and in the methods section.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

These data should be repeated using a more established model of Kupffer cell target deletion via Clec4-F mice.

Our data with Kupffer cell C3ar1 deletion is indeed done with Clec4f-Cre transgenic mice. This has been clarified in the revised manuscript on page 7 and in the methods section.

Reviewer #2 (Recommendations for the authors):

(1) Typo: "iver" in the abstract

(2) Line 97, "GAN diet I" should be "GAN diet"?

These points have been corrected in the revised manuscript.