Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In this study, the authors used a stopped-flow method to investigate the kinetics of substrate translocation through the channel in hexameric ClpB, an ATP-dependent bacterial protein disaggregase. They engineered a series of polypeptides with the N-terminal RepA ClpB-targeting sequence followed by a variable number of folded titin domains. The authors detected translocation of the substrate polypeptides by observing the enhancement of fluorescence from a probe located at the substrate's C-terminus. The total time of the substrates' translocation correlated with their lengths, which allowed the authors to determine the number of residues translocated by ClpB per unit time.

Strengths:

This study confirms a previously proposed model of processive translocation of polypeptides through the channel in ClpB. The novelty of this work is in the clever design of a series of kinetic experiments with an engineered substrate that includes stably folded domains. This approach produced a quantitative description of the reaction rates and kinetic step sizes. Another valuable aspect is that the method can be used for other translocases from the AAA+ family to characterize their mechanism of substrate processing.

Weaknesses:

The main limitation of the study is in using a single non-physiological substrate of ClpB, which does not replicate the physical properties of the aggregated cellular proteins and includes a non-physiological ClpB-targeting sequence. Another limitation is in the use of ATPgammaS to stimulate the substrate processing. It is not clear how relevant the results are to the ClpB function in living cells with ATP as the source of energy, a multitude of various aggregated substrates without targeting sequences that need ClpB's assistance, and in the presence of the co-chaperones.

Indeed, we agree that our RepA-Titinx substrates are not aggregates but are model, soluble, substrates used to reveal information about enzyme catalyzed protein unfolding and translocation.  Our substrates are similar to RepA-GFP and GFP-SsrA used by multiple labs including Wickner, Horwich, Sauer, Baker, Shorter, Bukua, to name only a few.  The fact that “this is what everyone does” does not make the substrates physiological or the most ideal. However, this is the technology we currently have until we and others develop something better. In the meantime, we contend that  the results presented here do advance our knowledge on enzyme catalyzed protein unfolding

Part of what this manuscript seeks to accomplish is presenting the development of a single-turnover experiment that reports on processive protein unfolding by AAA+ molecular motors, in this case, ClpB.  Importantly, we are treating translocation on an unfolded polypeptide chain and protein unfolding of stably folded proteins as two distinct reactions catalyzed by ClpB. If these functions are used to disrupt protein aggregates, in vivo, then this remains to be seen.

We contend that processive ClpB catalyzed protein unfolding has not been rigorously demonstrated prior to our results presented here.  Avellaneda et al mechanically unfolded their substrate before loading ClpB (Avellaneda, Franke, Sunderlikova et al. 2020).  Thus, their experiment represents valuable observations reflecting polypeptide translocation on a pre-unfolded protein.  Our previous work using single-turnover stopped-flow experiments employed unstructured synthetic polypeptides and therefore reflects polypeptide translocation and not protein unfolding (Li, Weaver, Lin et al. 2015).  Weibezahn et al used unstructured substrates in their study with ClpB (BAP/ClpP), and thus their results represent translocation of a pre-unfolded polypeptide and not enzyme catalyzed protein unfolding (Weibezahn, Tessarz, Schlieker et al. 2004). 

Many studies have reported the use of  GFP with tags or RepA-GFP and used the loss of GFP fluorescence to conclude protein unfolding.  However, such results do not reveal if ClpB processively and fully translocates the substrate through its axial channel.  One cannot rule out, even when trapping with “GroEL trap”, the possibility that ClpB only needs to disrupt some of the fold in GFP before cooperative unfolding occurs leading to loss of fluorescence.  Once the cooperative collapse of the structure occurs and fluorescence is lost it has not been shown that ClpB will continue to translocate on the newly unfolded chain or dissociate. In fact, the Bukau group showed that folded YFP remained intact after luciferase was unfolded (Haslberger, Zdanowicz, Brand et al. 2008).  Our approach, reported here, yields signal upon arrival of the motor at the c-terminus or within the PIFE distance thus we can be certain that the motor does arrive at the c-terminus after unfolding up to three tandem repeats of the Titin I27 domain.

ATPgS is a non-physiological nucleotide analog.  However, ClpB has been shown to exhibit curious behavior in its presence that we and others, as the reviewer acknowledges, do not fully understand (Doyle, Shorter, Zolkiewski et al. 2007).  Some of the experiments reported here are seeking to better understand that fact.  Here we have shown that ATPgS alone will support processive protein unfolding. With this assay in hand, we are now seeking to go forward and address many of the points raised by this reviewer. 

The authors do not attempt to correlate the kinetic step sizes detected during substrate translocation and unfolding with the substrate's structure, which should be possible, given how extensively the stability and unfolding of the titin I27 domain were studied before. Also, since the substrate contains up to three I27 domains separated with unstructured linkers, it is not clear why all the translocation steps are assumed to occur with the same rate constant.

We assume that all protein unfolding steps occur with the same rate constant, ku.  We conclude that we are not detecting the translocation rate constant, kt, as our results support a model where kt is much faster than ku.  We do think it makes sense that the same slow step occurs between each cycle of protein unfolding.

We have added a discussion relating our observations to mechanical unfolding of tandem repeats of Titin I27 from AFM experiments  (Oberhauser, Hansma, Carrion-Vazquez and Fernandez 2001). Most interestingly, they report unfolding of Titin I27 in 22 nm steps.  Using 0.34 nm per amino acids this yields ~65 amino acids per unfolding step, which is comparable to our kinetic step-size of 57 – 58 amino acids per step.

Some conclusions presented in the manuscript are speculative:

The notion that the emission from Alexa Fluor 555 is enhanced when ClpB approaches the substrate's C-terminus needs to be supported experimentally. Also, evidence that ATPgammaS without ATP can provide sufficient energy for substrate translocation and unfolding is missing in the paper.

In our previous work we have used fluorescently labeled 50 amino acid peptides as substrates to examine ClpB binding (Li, Lin and Lucius 2015, Li, Weaver, Lin et al. 2015).  In that work we have used fluorescein, which exhibits quenching upon ClpB binding.  We have added a control experiment where we have attached alexa fluor 555 to the 50 amino acid substrate so we can be assured the ClpB binds close to the fluorophore.  As seen in supplemental Fig. 1 A  upon titration with ClpB, in the presence of ATPγS, we observe an increase in fluorescence from AF555, consistent with PIFE.  Supplemental Fig. 1 B shows the relative fluorescence enhancement at the peak max increases up to ~ 0.2 or a 20 % increase in fluorescence, due to PIFE, upon ClpB binding.   

Further, peak time is our hypothesized measure of ClpB’s arrival at the dye. Our results indicate that the peak time linearly increases as a function of an increase in the number of folded TitinI27 repeats in the substrates which also supports the PIFE hypothesis. Finally, others have shown that AF555 exhibits PIFE and we have added those references.

The evidence that ATPγS alone can support translocation is shown in Fig. 2 and supplemental Figure 1.  Fig. 2 and supplemental Figure 1 are two different mixing strategies where we use only ATPgS and no ATP at all.  In both cases the time courses are consistent with processive protein unfolding by ClpB with only ATPγS.

Reviewer #2 (Public Review):

Summary:

The current work by Banwait et al. reports a fluorescence-based single turnover method based on protein-induced fluorescence enhancement (PIFE) to show that ClpB is a processive motor. The paper is a crucial finding as there has been ambiguity on whether ClpB is a processive or non-processive motor. Optical tweezers-based single-molecule studies have shown that ClpB is a processive motor, whereas previous studies from the same group hypothesized it to be a non-processive motor. As co-chaperones are needed for the motor activity of the ClpB, to isolate the activity of ClpB, they have used a 1:1 ratio ATP and ATPgS, where the enzyme is active even in the absence of its co-chaperones, as previously observed. A sequential mixing stop-flow protocol was developed, and the unfolding and translocation of RepA-TitinX, X = 1,2,3 repeats was monitored by measuring the fluorescence intensity with the time of Alexa F555 which was labelled at the C-terminal Cysteine. The observations were a lag time, followed by a gradual increase in fluorescence due to PIFE, and then a decrease in fluorescence plausibly due to the dissociation from the substrate allowing it to refold. The authors observed that the peak time depends on the substrate length, indicating the processive nature of ClpB. In addition, the lag and peak times depend on the pre-incubation time with ATPgS, indicating that the enzyme translocates on the substrates even with just ATPgS without the addition of ATP, which is plausible due to the slow hydrolysis of ATPgS. From the plot of substrate length vs peak time, the authors calculated the rate of unfolding and translocation to be ~0.1 aas-1 in the presence of ~1 mM ATPgS and increases to 1 aas-1 in the presence of 1:1 ATP and ATPgS. The authors have further performed experiments at 3:1 ATP and ATPgS concentrations and observed ~5 times increase in the translocation rates as expected due to faster hydrolysis of ATP by ClpB and reconfirming that processivity is majorly ATP driven. Further, the authors model their results to multiple sequential unfolding steps, determining the rate of unfolding and the number of amino acids unfolded during each step. Overall, the study uses a novel method to reconfirm the processive nature of ClpB.

Strengths:

(1) Previous studies on understanding the processivity of ClpB have primarily focused on unfolded or disordered proteins; this study paves new insights into our understanding of the processing of folded proteins by ClpB. They have cleverly used RepA as a recognition sequence to understand the unfolding of titin-I27 folded domains.

(2) The method developed can be applied to many disaggregating enzymes and has broader significance.

(3) The data from various experiments are consistent with each other, indicating the reproducibility of the data. For example, the rate of translocation in the presence of ATPgS, ~0.1 aas-1 from the single mixing experiment and double mixing experiment are very similar.

(4) The study convincingly shows that ClpB is a processive motor, which has long been debated, describing its activity in the presence of only ATPgS and a mixture of ATP and ATPgS.

(5) The discussion part has been written in a way that describes many previous experiments from various groups supporting the processive nature of the enzyme and supports their current study.

Weaknesses:

(1) The authors model that the enzyme unfolds the protein sequentially around 60 aa each time through multiple steps and translocates rapidly. This contradicts our knowledge of protein unfolding, which is generally cooperative, particularly for titinI27, which is reported to unfold cooperatively or utmost through one intermediate during enzymatic unfolding by ClpX and ClpA.

We do not think this represents a contradiction.  In fact, our observations are in good agreement with mechanical unfolding of tandem repeats of Titin I27 using AFM experiments (Oberhauser, Hansma, Carrion-Vazquez and Fernandez 2001).  They showed that tandem repeats of TitinI27 unfolded in steps of ~22 nm.  Dividing 22 nm by 0.34 nm/Amino Acid gives ~65 amino acids per unfolding event.  This implies that, under force, ~65 amino acids of folded structure unfolds in a single step.  This number is in excellent agreement with our kinetic step-size of 65 AA/step. 

Importantly, the experiments cited by the reviewer on ClpA and ClpX are actually with ClpAP and ClpXP.  We assert that this is an important distinction as we have shown that ClpA employs a different mechanism than ClpAP (Rajendar and Lucius 2010, Miller, Lin, Li and Lucius 2013, Miller and Lucius 2014).  Thus, ClpA and ClpAP should be treated as different enzymes but, without question, ClpB and ClpA are different enzymes.

(2) It is also important to note that the unfolding of titinI27 from the N-terminus (as done in this study) has been reported to be very fast and cannot be the rate-limiting step as reported earlier(Olivares et al, PNAS, 2017). This contradicts the current model where unfolding is the rate-limiting step, and the translocation is assumed to be many orders faster than unfolding.

Most importantly, the Olivares paper is examining ClpXP and ClpAP catalyzed protein unfolding and translocation and not ClpB.  These are different enzymes.  Additionally, we have shown that ClpAP and ClpA translocate unfolded polypeptides with different rates, rate constants, and kinetic step-sizes indicating that ClpP allosterically impacts the mechanism employed by ClpA to the extent that even ClpA and ClpAP should be considered different enzymes (Rajendar and Lucius 2010, Miller, Lin, Li and Lucius 2013).  We would further assert that there is no reason to assume ClpAP and ClpXP would catalyze protein unfolding using the same mechanism as ClpB as we do not think it should be assumed ClpA and ClpX use the same mechanism as ClpAP and ClpXP, respectively. 

The Olivares et al paper reports a dwell time preceding protein unfolding of ~0.9 and ~0.8 s for ClpXP and ClpAP, respectively.   The inverse of this can be taken as the rate constant for protein unfolding and would yield a rate constant of ~1.2 s-1, which is in good agreement with our observed rate constant of 0.9 – 4.3 s-1 depending on the ATP:ATPγS mixing ratio.  For ClpB, we propose that the slow unfolding is then followed by rapid translocation on the unfolded chain where translocation by ClpB must be much faster than for ClpAP and ClpXP.  We think this is a reasonable interpretation of our results and not a contradiction of the results in Olivares et al. Moreover, this is completely consistent with the mechanistic differences that we have reported, using the same single-turnover stopped flow approach on the same unfolded polypeptide chains with ClpB, ClpA, and ClpAP (Rajendar and Lucius 2010, Miller, Lin, Li and Lucius 2013, Miller and Lucius 2014, Li, Weaver, Lin et al. 2015).

(3) The model assumes the same time constant for all the unfolding steps irrespective of the secondary structural interactions.

Yes, we contend that this is a good assumption because it represents repetition of protein unfolding catalyzed by ClpB upon encountering the same repeating structural elements, i.e. Beta sheets. 

(4) Unlike other single-molecule optical tweezer-based assays, the study cannot distinguish the unfolding and translocation events and assumes that unfolding is the rate-limiting step.

Although we cannot, directly, distinguish between protein unfolding and translocation we have logically concluded that protein unfolding is likely rate limiting. This is because the large kinetic step-size represents the collapse of ~60 amino acids of structure between two rate-limiting steps, which we interpret to represent cooperative protein unfolding induced by ClpB.  It is not an assumption it is our current best interpretation of the observations that we are now seeking to further test. 

Reviewer #3 (Public Review):

Summary:

The authors have devised an elegant stopped-flow fluorescence approach to probe the mechanism of action of the Hsp100 protein unfoldase ClpB on an unfolded substrate (RepA) coupled to 1-3 repeats of a folded titin domain. They provide useful new insight into the kinetics of ClpB action. The results support their conclusions for the model setup used.

Strengths:

The stopped-flow fluorescence method with a variable delay after mixing the reactants is informative, as is the use of variable numbers of folded domains to probe the unfolding steps.

Weaknesses:

The setup does not reflect the physiological setting for ClpB action. A mixture of ATP and ATPgammaS is used to activate ClpB without the need for its co-chaperones, Hsp70. Hsp40 and an Hsp70 nucleotide exchange factor. This nucleotide strategy was discovered by Doyle et al (2007) but the mechanism of action is not fully understood. Other authors have used different approaches. As mentioned by the authors, Weibezahn et al used a construct coupled to the ClpA protease to demonstrate translocation. Avellaneda et al used a mutant (Y503D) in the coiled-coil regulatory domain to bypass the Hsp70 system. These differences complicate comparisons of rates and step sizes with previous work. It is unclear which results, if any, reflect the in vivo action of ClpB on the disassembly of aggregates.

We agree with the reviewer, there are several strategies that have been employed to bypass the need for Hsp70/40 or KJE to simplify in vitro experiments.  Here we have developed a first of its kind transient state kinetics approach that can be used to examine processive protein unfolding.  We now seek to go forward with examining the mechanisms of hyperactive mutants, like Y503D, and add the co-chaperones so that we can address the limitations articulated by the reviewer.   In fact we already began adding DnaK to the reaction and found that DnaK induced ClpB to release the polypeptide chain (Durie, Duran and Lucius 2018).  However, the sequential mixing strategy developed here was needed to go forward with examining the impact of co-chaperones. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Line 1: I recommend changing the title of the paper to remove the terms that are not clearly defined in the text: "robust" and "processive". What are the Authors' criteria for describing a molecular machine as "robust" vs. "not robust"? A definition of processivity is given in equation 2, but its value for ClpB is not reported in the text, and the criteria for classifying a machine as "processive" vs. "non-processive" are not included. Besides, the Authors have previously reported that ClpB is non-processive (Biochem. J., 2015), so it is now clear that a more nuanced terminology should be applied to this protein. Also, Escherichia coli should be fully spelled out in the title.

The title has been changed.  We have removed “robust” as we agree with the reviewer, there is no way to quantify “robust”.  However, we have kept “processive” and have added to the discussion a calculation of processivity since we can quantify processivity.  Importantly, the unstructured substrates used in our previous studies represent translocation and not protein unfolding.  here, on folded substrates, we detect rate-limiting protein unfolding followed by rapid translocation.  Thus, we report a lower bound on protein unfolding processivity of 362 amino acids. 

Line 20: The comment about mitochondrial SKD3 should be removed. SKD3, like ClpB, belongs to the AAA+ family, and it is simply a coincidence that the original study that discovered SKD3 termed it an Hsp100 homolog. The similarity between SKD3 and ClpB is limited to the AAA+ module, so there are many other metazoan ATPases, besides SKD3, that could be called homologs of ClpB, including mitochondrial ClpX, ER-localized torsins, p97, etc.

Removed.

Lines 133-139. Contrary to what the authors state, it is not clear that the "lag-phase" becomes significantly shorter for subsequent mixing experiments (Figure 1E) perhaps except for the last one (2070 s). It is clear, however, that the emission enhancement becomes stronger for later mixes. This effect should be discussed and explained, as it suggests that the pre-equilibrations shorter than ~2000 sec do not produce saturation of ClpB binding to the substrate.

We have added supplemental figure 2, which represents a zoom into the lag region.  This better illustrates what we were seeing but did not clearly show to the reader.  In addition, we address all three changes in the time courses, i.e. extend of lag, change in peak position, and the change in peak height. 

Line 175. The hydrolysis rate of ATPgammaS in the presence of ClpB should be measured and compared to the hydrolysis rate with ATP/ATPgammaS to check if the ratio of those rates agrees with the ratio of the translocation rates. These experiments should be performed with and without the RepA-titin substrate, which could reveal an important linkage between the ATPase engine and substrate translocation. These experiments are essential to support the claim of substrate translocation and unfolding with ATPgammaS as the sole energy source.

The time courses shown in figure 2 and supplemental Figure 1 are collected with only ATPgS and no ATP.  The time courses show a clear increase in lag and appearance of a peak with increasing number of tandem repeats of titin domains.  We do not see an alternate explanation for this observation other than ATPγS supports ClpB catalyzed protein unfolding and translocation.  What is the reviewers alternate explanation for these observations?

We agree with the reviewer that the linkage of ATP hydrolysis to protein unfolding and translocation is essential and we are seeking to acquire this knowledge.  However, a simple comparison of the ratio of rates is not adequate. We contend that a complete mechanistic study of ATP turnover by ClpB is required to properly address this linkage and such a study is too substantial to be included here but is currently underway. 

All that said, the statement on line 175 was removed since we do not report any ATPase measurements in this paper.

Line 199: It is an over-simplification to state that "1:1 mix of ATP to ATPgammaS replaces the need for co-chaperones". This sentence should be corrected or removed. The ClpB co-chaperones (DnaK, DnaJ, GrpE) play a major role in targeting ClpB to its aggregated substrates in cells and in regulating the ClpB activity through interactions with its middle domain. ATPgammaS does not replace the co-chaperones; it is a chemical probe that modifies the mechanism of ClpB in a way that is not entirely understood.

We agree with the reviewer.  The sentence has been modified to point out that the mix of ATP and ATPγS activates ClpB.

Figure 3B, Supplementary Figure 5A. The solid lines from the model fit cannot be distinguished from the data points. Please modify the figures' format to clearly show the fits and the data points.

Done.

Lines 326, 329. It is not clear why the authors mention a lack of covalent modification of substrates by ClpB. AAA+ ATPases do not produce covalent modifications of their substrates.

The issue of covalent modification was presented in the introduction lines 55 – 60 pointing out that much of what we have learned about protein unfolding and translocation catalyzed by ClpA and ClpX is from the observations of proteolytic degradation catalyzed by the associated protease ClpP.  However, this approach is not possible for ClpB/Hsp104 as these motors do not associate with a protease unless they have been artificially engineered to do so. 

Lines 396-399. I am puzzled why the authors try to correlate the size of the detected kinetic step with the length of the ClpB channel instead of the size characteristics of the substrate.

We are attempting to discuss/rationalize the observed large kinetic step-size which, in part, is defined by the structural properties of the enzyme as well as the size characteristics of the substrate.  We have attempted to clarify this and better discuss the properties of the substrate as well as ClpB.

As I mentioned in the Public Review, it is essential to demonstrate that the emission increase used as the only readout of the ClpB position along the substrate is indeed caused by the proximity of ClpB to the fluorophore. One way to accomplish that would be to place the fluorophore upstream from the first I27 domain and determine if the "lag phase" in the emission enhancement disappears.

Alexa Fluor 555 is well established to exhibit PIFE.  However, as in the response to the public review, we have included an appropriate control showing this in supplemental Fig. 1.

Finally, the authors repetitively place their results in opposition to the study of Weibezahn et al. published in 2004 which first demonstrated substrate translocation by engineering a peptidase-associated variant of ClpB. It should be noted that the field of protein disaggregases has moved since the time of that publication from the initial "from-start-to-end" translocation model to a more nuanced picture of partial translocation of polypeptide loops with possible substrate slipping through the ClpB channel and a dynamic assembly of ClpB hexamers with possible subunit exchange, all of which may affect the kinetics in a complex way. However, the present study confirmed the "start-to-end" translocation model, albeit for a non-physiological ClpB substrate, and that is the take-home message, which should be included in the text.

It is not clear to us that the field has “moved on” since Weibezahn et al 2004.  Their engineered construct that they term “BAP” with ClpP is still used in the field despite us reporting that proteolytic degradation is observed in the absence of ATP with that system  (Li, Weaver, Lin et al. 2015) and should, therefore, not be used to conclude processive energy driven translocation. The “partial translocation” by ClpB is also grounded in observations of partial degradation catalyzed by ClpP with BAP from the same group (Haslberger, Zdanowicz, Brand et al. 2008). It is not clear to us that the idea of subunit exchange leading to the possibility of assembly around internal sequences is being considered.  We do agree that this is an important mechanistic possibility that needs further interrogation. We agree with the reviewer, all these factors are confounding and lead to a more nuanced view of the mechanism.

All that said, we have removed some of the opposition in the discussion.

Reviewer #2 (Recommendations For The Authors):

(1) It is assumed that the lag phase will be much longer than the phase in which we see a gradual increase in fluorescence, as the effect of PIFE is significant only when the enzyme is very close to the fluorophore. Particularly for RepA-titin3, the enzyme has to translocate many tens of nm before it is closer to the C-terminus fluorophore. However, in all cases, the lag time is lower or similar to the gradual increase phase (for example, Figure 3B). Could the authors explain this?

The extent of the lag, or time zero until the signal starts to increase, is interpreted to indicate the time the motor moves from it’s initial binding site until it gets close enough to the fluorophore that PIFE starts to occur.  In our analysis we apply signal change to the last intermediate and dissociation or release of unfolded RepA-TitinX.  The increase in PIFE is not “all or nothing”.  Rather, it is starting to increase gradually.  Further, because these are ensemble measurements, and each molecule will exhibit variability in rate there is increased breadth of the peak due to ensemble averaging. 

(2) Although the reason for differences in the peak position (for example, Figure 1E, 2B) is apparent, the reason for variations in the relative intensities has to be given or speculated.

We have addressed the reason for the different peak heights in the revised manuscript.  It is the consequence of the fact that each substrate has slightly different fluorescent labeling efficiencies.  Thus, for each sample there is a mix of labeled and unlabeled substrates both of which will bind to ClpB but the unlabeled ClpB bound substrates do not contribute to the fluorescence signal, but will represent a binding competitor.  Thus, for low labeling efficiency there is a lower concentration of ClpB bound to fluorescent RepA-Titinx and for higher labeling efficiency there is higher concentration of ClpB bound to RepA-Titinx leading to an increased peak height.  RepA-Titin2 has the highest labeling efficiency and thus the largest peak height.

Reviewer #3 (Recommendations For The Authors):

The authors should make it clear that they and previous authors have used different constructs or conditions to bypass the physiological regulation of ClpB action by Hsp70 and its co-factors as mentioned above. In particular, the construct used by Avellaneda et al should be explained when they challenge the findings of those authors.

Minor points:

The lines fitting the experimental points are difficult or impossible to see in Figures 2B, 3B, and s5B.

Fixed

Typo bottom of p6 - "averge"

Fixed

Avellaneda, M. J., K. B. Franke, V. Sunderlikova, B. Bukau, A. Mogk and S. J. Tans (2020). "Processive extrusion of polypeptide loops by a Hsp100 disaggregase." Nature.

Doyle, S. M., J. Shorter, M. Zolkiewski, J. R. Hoskins, S. Lindquist and S. Wickner (2007). "Asymmetric deceleration of ClpB or Hsp104 ATPase activity unleashes protein-remodeling activity." Nature structural & molecular biology 14(2): 114-122.

Durie, C. L., E. C. Duran and A. L. Lucius (2018). "Escherichia coli DnaK Allosterically Modulates ClpB between High- and Low-Peptide Affinity States." Biochemistry 57(26): 3665-3675.

Haslberger, T., A. Zdanowicz, I. Brand, J. Kirstein, K. Turgay, A. Mogk and B. Bukau (2008). "Protein disaggregation by the AAA+ chaperone ClpB involves partial threading of looped polypeptide segments." Nat Struct Mol Biol 15(6): 641-650.

Li, T., J. Lin and A. L. Lucius (2015). "Examination of polypeptide substrate specificity for Escherichia coli ClpB." Proteins 83(1): 117-134.

Li, T., C. L. Weaver, J. Lin, E. C. Duran, J. M. Miller and A. L. Lucius (2015). "Escherichia coli ClpB is a non-processive polypeptide translocase." Biochem J 470(1): 39-52.

Miller, J. M., J. Lin, T. Li and A. L. Lucius (2013). "E. coli ClpA Catalyzed Polypeptide Translocation is Allosterically Controlled by the Protease ClpP." Journal of Molecular Biology 425(15): 2795-2812.

Miller, J. M. and A. L. Lucius (2014). "ATP-gamma-S Competes with ATP for Binding at Domain 1 but not Domain 2 during ClpA Catalyzed Polypeptide Translocation." Biophys Chem 185: 58-69.

Oberhauser, A. F., P. K. Hansma, M. Carrion-Vazquez and J. M. Fernandez (2001). "Stepwise unfolding of titin under force-clamp atomic force microscopy." Proc Natl Acad Sci U S A 98(2): 468-472.

Rajendar, B. and A. L. Lucius (2010). "Molecular mechanism of polypeptide translocation catalyzed by the Escherichia coli ClpA protein translocase." J Mol Biol 399(5): 665-679.

Weibezahn, J., P. Tessarz, C. Schlieker, R. Zahn, Z. Maglica, S. Lee, H. Zentgraf, E. U. Weber-Ban, D. A. Dougan, F. T. Tsai, A. Mogk and B. Bukau (2004). "Thermotolerance requires refolding of aggregated proteins by substrate translocation through the central pore of ClpB." Cell 119(5): 653-665.

Author response:

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

We would like to thank the reviewers and editor for their helpful comments. We have addressed their concerns as detailed below.

It would have been nice to have included a bona-fide SIRT2 target as a control throughout the study.

We agree that including a bona-fide SIRT2 target as a control is important for validating our results. Previous data from our work has shown that SIRT2 demyristoylates ARF6. Thus, we have included a blot in Figure S15 demonstrating that SIRT2 knockdown results in increased myristoylation of ARF6. This serves as a control to confirm the activity and role of SIRT2 in our study.

Did the authors also consider investigating SIRT1 in their assays? SIRT1 activates ACSS2 while SIRT2 leads to degradation of ACSS2. They should at least discuss these seemingly opposing roles of SIRT1 and SIRT2 in the regulation of ACSS2 and acetate metabolism in more depth particularly as it concerns situations (i.e., diseases, pathologies) where either SIRT1, SIRT2, or both sirtuins, are active. This would enhance the significance of the findings to the broader research community.

The study by Hallows et al. showed increased SIRT1 deacetylate K661 of ACSS2 and increase its catalytic activity. Subsequently, a follow-up investigation unveiled the role of the circadian clock in modulating intracellular acetyl-CoA levels through SIRT1-catalyzed K661 deacetylation of. Conversely, our research elucidates a contrasting mechanism wherein SIRT2 inhibits ACSS2 by deacetylating K271 under conditions of nutrient stress. The dual regulation of ACSS2 by SIRT1 through the circadian clock and SIRT2 under nutrient stress underscores the intricate and multifaceted nature of regulatory mechanisms involved in lipid metabolism. These findings underscore the versatility of lysine acetylation in modulating cellular metabolic pathways.

Collectively, these studies contribute to a better understanding of how SIRT1 and SIRT2 regulate ACSS2 activity in various metabolic contexts, thereby enhancing our knowledge of acetate metabolism and its implications in health and disease.

We have included such discussion of the manuscript.

In Figure 3, the authors should consider immunoblotting for endogenous ACSS2 throughout the differentiation and lipogenesis study since the total ACSS2 levels is the crucial aspect to affecting acetate-dependent promotion of lipogenesis in adipocytes, and to confirm TM-dependent stabilization of ACSS2 in that assay.

We have updated Figure 3 to include immunoblotting for endogenous ACSS2 levels. Additionally, we have confirmed the TM-dependent stabilization of ACSS2, which is now shown in Figure S12.

Do the authors have any data proving the K271 mutants of ACSS2 are still functional? Or that K271 ACSS2 protein is folded correctly?

To assess the functionality of the mutants, we isolated Flag-tagged wildtype, K271R, and K271Q ACSS2 proteins from SIRT2 knockdown HEK293T cells. Subsequently, we examined acetyl-CoA formation from acetate and CoA using high-performance liquid chromatography (HPLC). Our findings indicate that while the wildtype ACSS2 exhibits slightly higher activity compared to the K271R and K271Q mutants, but all variants remain functional (Figure S13).

Nearly all experiments are performed in a single cell line. Authors should test whether SIRT2 regulates ACSS2 acetylation in at least 1 or 2 more cell lines. Does SIRT2 regulate ACSS2 acetylation in 3T3-L1 preadipocytes?

Experiments showing that endogenous ACSS2 levels change in EBSS and nutrient-deprived media were repeated in A549 cells (Figure S5). However, due to the poor transfection efficiency of A549 cells, we were unable to obtain acetylation data. Similarly, conducting acetylation experiments in 3T3-L1 preadipocytes is challenging due to poor transfection efficiency.

The article does not explicitly address whether the absence of amino acids impacts the acetylation and subsequent degradation of ACSS2 by activating SIRT2. If so, one would expect the level of ACSS2 acetylation or ACSS2 expression under amino acid deprivation to be lower than that under normal conditions, as depicted in Fig. 1C and Fig. S3.

The experiments shown in Fig. 1C and Fig. S3 were using overexpressed Flag-tagged ACSS2 and we actually adjust the amount of DNA used to have similar Flag-ACSS2 levels.

To address the comment raised by the reviewer, we added Figure S14, which shows that endogenous ACSS2 acetylation is decreased under amino acid deprivation in SIRT2 control KD cells, indicating that the absence of amino acids impacts ACSS2 acetylation. The decreased expression of ACSS2 under amino acid deprivation is also addressed in Figure S6.

Several reviewers noted discrepancies between what is occurring to basal levels of ACSS2 vs in SIRT2 KD conditions. Fig. 2H shows higher basal level of acetylated ACSS2 in K271R mutant compared to wildtype (input may be an issue). If Fig. 2H is a critical piece of data, authors are recommended to show this using FLAP-IP & then Ac-K.

The increased stability of the K271R mutant compared to the wildtype (WT) results in higher protein levels, which results in the different input levels. However, this does not affect the conclusion that K271 is the acetylation site as the quantification result shows that K271R mutant has lower acetylation level and is not regulated by SIRT2 (Figure S16).

Regarding the basal levels of ACSS2 in control and SIRT2 KD conditions, it was because the experiments in question were using overexpressed Flag-tagged ACSS2 and we actually adjust the amount of DNA used to have similar Flag-ACSS2 levels. To address the concern, we monitored endogenous ACSS2 protein and acetylation levels and the results are shown in Figure S14.

Also, in Fig 2I there is no difference in basal ubiquitination between WT and K271R mutant. Related, based on model you would expect that overexpression of ACSS2-K271R mutant compared to wildtype would be at higher levels. In many figures authors do not see this (Fig. 2I, 3A, 3B). This needs to be explained.

This is related to some previous comments. In these experiments, we actually adjusted the DNA used in the transfection to obtain equal protein levels so that we can quantify other things (acetylation or ubiquitination levels). As stated in the manuscript regarding Figures 3A and 3B, "To ensure comparable expression levels at the beginning, we adjusted the amount of transfected DNA for both wild-type and the K271R mutant ACSS2." This approach allowed us to accurately compare the ubiquitination status between the wildtype and K271R mutant ACSS2 variants.

Data showing role of ACSS2-K271 mutant in lipid accumulation requires clarification. Based on model overexpression of ACSS2-K271 mutant should by itself cause increased lipid accumulation compared to wildtype.

This is indeed the case and we have added this in the revised manuscript “Consistent with our above observation that ACSS2 K271R mutant is more stable than the WT, expressing the K271R mutant lead to more lipid droplets than expressing the WT ACSS2 (Figure S12).”

Loading controls are notably absent at certain instances, such as IPs in Fig. 1A, 1C, and the IP in Fig. 2H. Such controls are required to interpret potential changes in acetylation.

For this experiment, we employed an approach where we overexpressed Flag-tagged wild-type (WT) and mutant forms of ACSS2. We conducted an immunoprecipitation (IP) targeting acetyl-lysine residues to enrich lysine-acetylated proteins, followed by immunoblotting for the Flag tag to specifically detect ACSS2 acetylation levels. To ensure the reliability of our results, we included a Flag blot to confirm equal expression levels of ectopically expressed ACSS2 across our samples before IP. Given the nature of our experimental design and the specific aim of investigating ACSS2 acetylation, we believe that additional loading controls beyond the input Flag blot are not required for the interpretation of our results. The inclusion of the input Flag blot serves as a control for protein expression levels, which is crucial for accurate assessment of ACSS2 acetylation status.

While CHX treatment is known to inhibit protein synthesis, it appears contradictory that CHX treatment in Fig. 2C seemingly leads to ACSS2 accumulation in SIRT2 knockdown HEK293T cells. This discrepancy requires clarification.

We conducted quantitative analysis of the immunoblot with replicates to ensure the reliability of our findings. Our analysis indicates that the protein level of ACSS2 remains relatively stable over the time course of CHX treatment. The observed slight increase at the 8-hour time point can be attributed to inherent experimental variability, as evidenced by the presence of large error bars in the graph. We have included a graph in Figure S7 to show that there is no significant change in the level of ACSS2 in the SIRT2 HEK293T cells.

In Fig. 2F-H, the authors argue that SIRT2 deacetylates ACSS2 to facilitate its ubiquitination and subsequent proteasomal degradation. However, these results are depicted under normal conditions, whereas findings in Fig. 1 suggest that SIRT2 deacetylates ACSS2 exclusively under nutrient stress. An explanation for this inconsistency is warranted.

These experiments were done in amino acid deprived (EBSS) media. We have corrected this in the manuscript.

Line 160 authors conclude "amino acid limitation..deacetylates K271"..but this was not directly demonstrated. Authors should add this data or change conclusion.

Addressed in response to some of the comments above.

Figures 1A and 1B, acetylation quantification, not clear if it is relative to the Flag tag or actin.

Acetylation quantification is relative to Flag tag. This is clarified in the figure legend.

Methods section lacking details & not well referenced (how did authors express wildtype & mutant in 3T3-L1 cells?) 

ACSS2 wildtype and K271R mutant Flag-tagged expression plasmids were transfected into ACSS2 knockdown 3T3-L1 cells using PEI transfection reagent following the manufacturer’s protocol. The pCMV-Tag4a empty vector was used as the negative control. Differentiation of 3T3L1 cell lines were done according to manufacturer’s protocol (DIF001-1KT, Sigma Aldrich) 24 hours after transfection. This has been included in the methods.

In Figure 3A, is the actin blot from the same immunoblots above it? Reviewers recommend the authors upload original immunoblot.

This experiment was repeated, and the blot has been replaced.

Author response:

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

eLife assessment

The manuscript reports useful findings by resolving the crystal structure of Sedoheptulose-1,7-Bisphosphatase (SBPase) from the green algae Chlamydomonas reinhardtii, which is involved in the Calvin cycle. The data presented are solid based on validated methodologies, which help in understanding the structure and function of this enzyme.

We thank the editors for this positive assessment.

Public Reviews:

Reviewer #1 (Public Review):

In this study, Le Moigne and coworkers shed light on the structural details of the Sedoheptulose-1,7-Bisphosphatase (SBPase) from the green algae Chlamydomonas reinhardtii. The SBPase is part of the Calvin cycle and catalyzes the dephosphorylation of sedoheptulose-1,7-bisphosphate (SBP), which is a crucial step in the regeneration of ribulose-1,5-bisphosphate (RuBP), the substrate for Rubisco. The authors determine the crystal structure of the CrSBPase in an oxidized state. Based on this structure, potential active site residues and sites of post-translational modifications are identified. Furthermore, the authors determine the CrSBPase structure in a reduced state revealing the disruption of a disulfide bond in close proximity to the dimer interface. The authors then use molecular dynamics (MD) to gain insights into the redox-controlled dynamics of the CrSBPase and investigate the oligomerization of the protein using small-angle X-ray scattering (SAXS) and size-exclusion chromatography. Despite the difference in oligomerization, disruption of this disulfide bond did not impact the activity of CrSBPase, suggesting additional thiol-dependent regulatory mechanisms modulating the activity of the CrSBPase.

We thank reviewer 1 for his/her careful reading of our manuscript.

The authors provide interesting new findings on a redox-mechanism that modulates the oligomeric behavior of the SBPase, however without investigating this potential mechanism in more detail. The conclusions of this manuscript are mostly supported by the data, but they should be more carefully evaluated in respect to what is known from other systems as e.g. the moss Physcomitrella patens. This is especially of interest, as SBPase was previously reported to be dimeric, whereas for FBPase a dimer/tetramer equilibrium has been observed.

We thank reviewer 1 for his/her comments on the novel or confirmatory character of our structure-function analysis onCrSBPase. We address the questions of oligomeric states later in this response.

(1) Given that PpSBPase has been already characterized in detail, the authors should provide a more rigorous comparison to the existing data on SBPases. This includes a more conclusive structural comparison but also the enzymatic assays should be compared to the findings from P. patens. Do the authors observe differences between the moss and the chlorophyte systems, maybe even in regard to the oligomerization of the SBPase?

Indeed, a previous study conducted by one of the authors of the current manuscript (Stéphane D. Lemaire) and collaborators determined the structure and regulatory properties of SBPase from the moss Physcomitrella patens (Gütle et al. 2018 https://doi.org/10.1073/pnas.1606241113). We added a clearer reference to this earlier work. The differences that we observed regarding the oligomeric states of SBPase from Chlamydomonas reinhardtii principally stem from our analytical method in vitro through size-exclusion chromatography, in comparison with crystal packing analysis in the reference study. We detailed PpSBPase/CrSBPase oligoimeric state comparison in the paragraph 'Oligomeric states of CrSBPase'. Besides, the asymmetric unit of our CrSBPase crystal structure is also a homodimer, similarly to PpSBPase, and we suggest that PpSBPase is also likely to adopt several oligomeric states in vitro. If this were confirmed by experiments, SBPase in several organisms would behave analogously to FBPase regarding the dimer/tetramer equilibrium.

In paragraph 'Crystal structure of CrSBPase' we added a comparison by alignment of our CrSBPase crystal structure to the previously reported _Pp_SBPase crystal structure, stating that with RMSD=0.478 Å the proteins are essentially identical.

In paragraph 'CrSBPase enzymatic activity' we compared the value we obtained for enzyme specific activity to those previously published on other SBPase from Chlamydomonas or the land plant Spinacia oleracea, highlighting the similarity of results in three different systems and teams (Seuter et al. 2002 https://doi.org/10.1023/A:1019297521424 and Tamoi et al. 2005 DOI: 10.1271/bbb.69.848).

(2) The authors should include the control experiments (untreated SBPase) and the assays performed with mutant versions of the SBPase, which are currently only mentioned in the text or not shown at all.

We add supplementary figure 14 in order to illustrate that since SBPase C115S or C120S mutants are still activated by reducing agent, the disulfide bridge between cysteines 115 and 120 is not the single control over SBPase activity but rather a control over the oligomeric exchange of the enzyme indirectly contributing to redox activation of the active site.

(3) The representation of the structure in figures (especially Figures 1 and 3) should be adjusted to match the author's statements. In Figure 1, the angle from which the structure is displayed changes over the entire figure making it difficult to follow especially as a non-structural biologist. Furthermore, important aspects of the structure mentioned in the text are not labeled and should be highlighted, by e.g. a close-up. Same holds true for Figure 3 that currently mostly shows redundant information.

We thank reviewer 1 for his/her advise on how to improve Figure 1. We drew new images for the complete figure, hopefully providing more consistent and clearer visual support to our text. For simplicity, protein is now always represented centered around its active site in the same orientation. We represent co-crystallized water in all projections as a guide to the eye.

Figure 3 and supplementary figure 3 were switched in order to better represent the experimental evidence provided by the resolution of SBPase structure under reducing conditions, i.e., the increase in local disorder around C115-C120 pair of cysteines in the 113-130 stretch forming a redox-conditionally dynamic loop and β-hairpin motif.

(4) The authors state that mutation of C115 and C120 to serine destabilize the dimer formation, while more tetramer and monomer is formed. As the tetramer is essentially a dimer of dimers, the authors should elaborate how this might work mechanistically. In my opinion, dimer formation is a prerequisite for tetramer formation and the two mutations rather stabilize the tetramer instead of destabilizing the dimer.

Time-dependent dynamic character of SBPase oligomer exchange is not resolved by the current study because we essentially combined size-exclusion chromatography (SEC) and X-ray crystallography to define quaternary structures at equilibrium. Overall, homodimer is the dominant state of wild-type SBPase by abundance in the purified recombinant form and by forming the constitutive asymmetric unit in all crystal packings. Dimer is indeed present in the tetramer state, a dimer of dimers, as pertinently stated by reviewer 1.

This being recognized, we tried to explain the systematic co-elution of the principal dimeric form with an additional species of smaller size on SEC (supplementary figure 1, right-side shoulder of the peak), at the apparent mass of a monomer. When solving the crystal structures of SBPase we realized that the dimer interface is contributed by residues 113-130 forming a loop and β-hairpin motif. Notably, in this loop cysteine 115 (C115) maps at bonding distance of 3.9 Å of side chain of arginine 220 (R220) from dimer partner subunit. In loop 113-120, cysteine pair C115 and C120 are subject to redox switching between disulfide (closed) and dithiol (open) conformations, as shown in our structures 7B2O and 7ZUV, respectively. Given that the reduction of C115-C120 disulfide bridge correlates with a higher flexibility of this motif that contributes to dimer interface (figure S3), we hypothesized that reduction of SBPase would destabilize dimer state to the benefit of transitory monomer state, and indeed point mutagenesis of C115S or C120S caused a large modification of oligomer equilibrium in favour of the monomer (figure S1C).

Mechanistically, we suggest two scenarios for the tetramer formation: either monomers first interact as in the crystallographic dimer before pairing such dimers into tetramers (as proposed by reviewer 1), or monomers start tetramerization by favoring the alternative subunit interface (figure 5B, between cyan and magenta chains) before stabilizing the crystallographic homodimer interface. In this latter case, monomerization would be necessary to efficiently re-arrange SBPase dimers into tetramers.

In physiological conditions the re-arrangement switch would be controlled by C115-C120 reduction through ferredoxin-thioredoxin redox cascade. Structural studies in dynamic conditions like native mass spectroscopy/photometry would be necessary to solve this speculation unambiguously although at this stage of our investigation there seem little doubt to us that C115-C120 disulfide-dithiol exchange is essential to control a dimer/monomer balance in first instance.

Reviewer #2 (Public Review):

The central theme of the manuscript is to report on the structure of SBPase - an enzyme central to the photosynthetic Calvin-Benson-Bassham cycle. The authors claim that the structure is first of its kind from a chlorophyte Chlamydomonas reinhardtii, a model unicellular green microalga. The authors use a number of methods like protein expression, purification, enzymatic assays, SAXS, molecular dynamics simulations and xray crystallography to resolve a 3.09 A crystal structure of the oxidized and partially reduced state. The results are supported by the claims made in the manuscript. One of the main weakness of the work is the lack of wider discussion presented in the manuscript. While the structure is the first from a chlorophyte, it is not unique. Several structures of SBPase are available. As the manuscript currently reads, the wider context of SBPase structures available and comparisons between them is missing from the manuscript. Another important point is that the reported structure of crSBPase is 0.453A away from the alphafold model. Though fleetingly mentioned in the methods section, it should be discussed to place it in the wider context.

We thank reviewer 2 for his/her assessment of our manuscript. In response to his/her suggestion to better compare our SBPase structure from the model microalga Chlamydomonas reinhardtii to that of the ortholog from Physcomitrium patens previously reported by an author of this manuscript (Stéphane D. Lemaire) and collaborators (Gütle et al. 2018), we wish to point out that paragraph 3 of the introduction was dedicated to this reference along with a mention to related Thermosynechococcus elongatus dual function fructose-1,6-bisphosphatase sedoheptulose-1,7-bisphosphatase (F/SBPase). We nevertheless follow his/her suggestion to better detail comparison between chloroplastic SBPase structures in the first result section 'Crystal structure of CrSBPase', consistently with response 1 to reviewer 1 (see above).

Regarding the integration of AlphaFold (AF) computational models in a general discussion about SBPase molecular structure, we wish to point out that our initial 7B2O crystallographic model of CrSBPase was deposited in PDB on 2020-11-27 before AlphaFold2 was available for the scientific community (Jumper et al. publication date is 15 July 2021).

AF2 entry AF-P46284-F1-model_v4 from AlphaFold Protein Structure Database aligns with our crystal structure 7B2O chain E with RMSD = 0.434 Å, showing excellent agreement between experiment and prediction at the level of protein main chain. It must still be pointed out that it is the AF2 model which is at 0.434 Å away from the experiment, and not the opposite. Exceptions of alignments are in local differences in several loops conformations and in the length of secondary structure elements. Many amino acid residues side chains adopt distinct orientations between the computational model and the experimental structure.

AF3 was recently communicated (Abramson et al. 2024) along with its online prediction server hosted at https://golgi.sandbox.google.com. CrSBPase model from AF3 align to our crystal structure 7B2O chain A with RMSD = 0.489 Å showing again their strong similarity and with a smaller discrepancy between AF2 and AF3 of RMSD = 0.216 Å. The only significant deviations between 7B2O and AF3 are in the orientation of several side chains and notably on the conformation of region 114-131 that contain the redox sensor motif.

We added the last two paragraphs to the revised version of the manuscript, after the results section presenting our crystallographic work.

Recommendations for the authors:

We made all recommended modifications as detail below.

Reviewer #1 (Recommendations For The Authors):

I have outlined a number of minor points below.

We addressed all minor points listed.

Line 220: The asymmetric unit only contains three dimers. The dimer of dimer or tetramer can only be reconstituted by displaying the symmetry mates.

We corrected our sentence for 'The asymmetric unit is composed of six polypeptide chains packing as three dimers'.

I also suggest that the authors separate the description of the asymmetric unit content from the modeled water molecules and rephrase e.g. „..and four water molecules could be modeled."

We rephrased as suggested.

I appreciate that the authors uploaded the structure in advance of this article, which allowed to evaluate the quality of the structure. Although this does not add valuable information, I have identified several unmodeled blobs, which possibly also account for waters.

Unmodeled blobs were tentatively assigned to water but had to be removed during later refinements. We used Coot Validate tools 'Unmodelled blobs' and 'Check/Delete water' to progress towards the current optimal refinement statistics. We admit that the resolution of the crystallographic dataset (3.09 Å) is limiting to reliably model mobile or less resolved elements like water molecules. Overall, we estimate that the functional elements of the structure are modeled to the best of our knowledge and with minimal subjectivity.

Line 222: Please write 309 instead of spelling the number.

We corrected for 309 instead of spelling the number.

Line 223: The structure representation in Figure 1A/B has to be improved. The authors might consider labeling the two domains & color them in two colors instead of the rainbow color coding. Furthermore, the 90{degree sign} rotation does not add much information. Here, turning the model in a different direction that allows to see the central b-sheet of domain 2 might be better suited. Furthermore, instead of describing b-strands first, followed by a-helices, I suggest describing which secondary structure elements form the two domains.

We improved Figure 1A as suggested while keeping Figure 2B with 90° rotation as rainbow color gradient in order to display with clarity the secondary structure content and connectivity. The orientation was tilted to better display the central β-sheet. This new version of Figure 1A/B should facilitate the text description of SBPase architecture that we amended as suggested.

Line 229: The information on A113-120 should be depicted in a closeup in Figure 1A.

We made a close-up view of sequence 113-120 as added figures 1C-D and modified the rest of the figure and legend accordingly.

Line 234: Please provide an r.m.s.d here.

We now provide r.m.s.d. for all structural alignments.

Line 242: Please introduce the domain labeling in Fig 1C to make it easier to track the exact region within SBP here. Is the residue numbering according to SBP or the human FBP?

Modified version of figure 1 now shows SBPase in the same orientation for panels A, E, F, G, H for simplicity. Domains labeling is indicated in panel A with NTD/CTD distinct colors as suggested. We explicited the position of W401 on all panels as a guide to the eye. We indicated in figure legend that residue numbering is according to Chlamydomonas SBPase Uniprot entry P46284.

Line 244: Is Figure 1D in the same orientation as C? I suggest making the surface transparent and showing the cartoon below, which will allow to easier see the solvent accessibility of the residues. Also, clearly label W401 (although it's the only water shown/modeled in this region).

We modified figure 1 to show all equivalent panels (ie. A-E-F-G-H) with the same orientation. In this new form we think that solvent accessibility and the relative position of significant residues is easier to interpret for the reader. W401 is consistently labeled throughout figure 1 panels.

Line 263: Please provide a close-up of the C222 and C231 including measured distance. It's clearly not visible from this view. It might even be helpful to provide close-ups of all cysteine residues that are mentioned in the text.

In the modified version of figure 1 we estimate that C222 and C231 are more easily visible. We added a close-up view of C22-C231 environment in a new supplementary figure 2. Since we do not explore further the functional relevance of this redox pair we chose not include C222-C231 close-up view in main figure 1. We added legends and modified supplementary figures numbering accordingly.

Line 276: As already mentioned earlier, none of the panels in Figure 1 provide a close-up of this loop. This should be added.

This loop is now displayed as a close-up view in panels C and D of main figure 1.

Line 284: It is difficult to follow the relative positions of the potential modification sites if the model is always depicted from a different angle in Figure 1. The authors might want to change this across Figure 1 or show the rotation angle.

This problem was addressed in the revised figure 1, panels A-E-F-G-H are in the same orientation now. Panel B was kept at a rotation of 90° with corresponding annotation.

Line 290: Please label W401. Also stick to one nomenclature (W or H20).

We labeled W401 and kept nomenclature consistent throughout the manuscript.

For comparative reasons, a full kinetic measurement (determination of Km and kcat) of the SBPase would also be helpful here.

We resolved to avoid a full kinetic measurement of CrSBPase because we could neither identify a reliable chemical provider nor synthesize ourselves the physiological substrate sedoheptulose-1,7-bisphosphate (SBP) and only characterized the reaction with fructose-1,6-bisphosphate. However, in the revised form of the manuscript we added in main text paragraph 'CrSBPase enzymatic activity' the kinetic constants from the previous reference study conducted on spinach SBPase (Cadet and Meunier, Biochem. J. 1988) with KMSBP\=0.05 mM and kcatSBP\=81 sec-1 of fully active enzyme with SBP as a substrate. For comparison, the authors of this study report that activity of SBPase on FBP is in the same range but lower, with KMFBP\=0.38 mM and kcatFBP\=21 sec-1. We also added a comparison of specific activities of our CrSBPase and spinach SBPase in the main text, showing that our enzyme behaves as previously reported ortholog from land plant.

Line 303: How much MgSO4 was used for the experiment shown in Figure 2A?

10 mM of MgS04 was used for experiment shown in Figure 2A. We added this information in the figure legend. We also added in the legend that 10 mM DTT is present in the experiment of Figure 2B and that 10 mM of MgSO4 and 1 mM of DTT are present in the experiment of Figure 2C.

Line 321: In my opinion it is not necessary to show the regions of all molecules here. I was rather expecting a superposition of the two structures (oxidized and reduced) with a close-up of the respective disulfide in the two states.

We agree that the initial version of Figure 3 panels showing side-by-side all conformational variants of the redox motif appear redundant. We switched initial Figure 3 to supplementary data and replaced it with the crystallographic b-factor mapping of the redox motif, in the variable conditions resolved by the crystals. We would like to stress that all these conformations were experimentally determined through X-ray crystallography, whether of the crystal of pure inactive enzyme that proved to be oxidized on the redox motif, or of the equivalent crystals submitted to activating treatment by the chemical reductant TCEP. As an attempt to clarification we added visual boxes to better appreciate this reduction-induced conformational plasticity that we interpreted as a local conditional disorder.

Line 331: Could the authors provide movies of the MD simulation? Otherwise, interpretation of the MD simulation results might be difficult for non-experts.

We added two movies of 20-µsec MD simulations as supplementary data to help non-expert readers.

Line 343: It might be helpful to label the structure elements in Figure 4 accordingly (e.g. residues, etc.)

We added secondary structure labeling in Figure 4.

Line 381: Should be changed to Figure 5A.

We changed reference to figure 6 that is a renumbering of figure 5 with changes included from suggestions below. Figure 6 now includes chromatograms of recombinant SBPase in panel A and chromatogram and western blot analysis of Chlamydomonas extracts in panel B.

Line 383: See above, figure 5B. Which structure is shown in the figure? 7zuv or 7b2o? Maybe include both structures in the figure in a side-by-side view. The authors might also want to include the SEC chromatograms in the main figure. Especially the purification from Chlamydomonas is helpful to estimate whether post-translational modifications have an impact on the oligomerization. This should also be mentioned in the text.

7b2o and 7zuv are illustrated side-by-side in panels A and B of figure 5. This was indicated in the figure legend, we now added the information on the figure. As suggested above we included chromatograms initially presented as supplementary material in a new main figure 6, panel A for recombinant proteins and panel B for proteins extracted from Chlamydomonas. Initial figures 5D-E, showing surface conservation of the dimeric SBPase, is moved to supplementary figure 5.

Line 385: I don't find the cultivation of Chlamydomonas in the method section. It should be added.

We added a methods paragraph dedicated to « Cultivation of Chlamydomonas for native SBPase analysis ».

Line 390-392: This information is not really helpful. Concentrated purified proteins might precipitate after a week storage without physiologically relevant effects being the reason.

We agree that the observation of a precipitate building up in vitro after a week of storage bears no particular physiological implications. We rather intended to report that an aggregated form of purified protein can be turned to droplets under the redox conditions that activate the enzyme. We reformulated these lines for clarification.

Line 397: I would appreciate having the SEC-chromatograms of the mutants also in the main figure.

Size-exclusion chromatograms that were initially in supplementary figures are now shown in main text figure 6 panel A, with the profiles WT and mutants aligned.

Line 402: Where are these data shown? They should be included in Figure 5.

We added a figure to present these data, not shown in the initial version of the manuscript. We preferred to place it as supplementary material because C115S and C120S mutant catalytic activity is essentially the same as WT and do not reveal a direct mechanistic effect of C115-C120 reduction over the catalytic pocket.

Line 427: Did the authors look into a possible cooperativity of their SBPase?

We did not observe direct positive cooperativity that could be ascribed to allostery in our enzymatic assays. It was previously reported for spinach SBPase that SBP saturation functions were hyperbolic with no evidence of homotropic interactions in the enzyme oligomer (Cadet and Meunier Biochem J. 1988 253, 249-254). The authors of this kinetic study however present a clear sigmoid response of SBPase to Mg2+ concentration, suggestive of an activating cross-talk between active sites in the oligomer. We consider this hypothesis of interest and wish we could further investigate allosteric conformational changes when SBP physiological substrate would be available.

Line 428-434: I don't really understand how the proteome mapping fits in here. Do the authors speculate that SBPase is recruited by some of the identified enzymes or directly interacts with them or that rather the spatial distribution optimizes the reaction kinetics?

We indeed want to correlate our in vitro observations of CrSBPase conditions of activity to those recently published by the group of Dr. Martin Jonikas in a physiological, in vivo setup of Chlamydomonas reinhardtii (Wang, Patena et al. Cell 2023 186, 3499–3518). We have no experimental evidence demonstrating the first suggestion that SBPase is recruited or directly interacts with partner enzymes but we privilege the second suggestion that local spatial distribution in the chloroplast stroma optimizes enzyme reaction kinetic thanks to Calvin-Benson-Bassham enzymes proximity. We rephrased these lines to clarify our hypothesis and express its speculative character.

Reviewer #2 (Recommendations For The Authors):

To make the manuscript stronger, the authors are recommended to do the following:

We followed given recommendations.

(1) include a wider discussion on the other SBPase structures that are available. A detailed comparison should be made between the oxidized and reduced structures present in the PDB with the structures that are being reported in the manuscript.

Consistently with reviewer #1 suggestion, and as detailed in response to public review above, we followed the recommendation to better report previous structural studies of SBPase in the results section. We also added comparisons with computational models from AlphaFold2 and AlphaFold3.

(2) The authors mention co-operativity between the subunits. With excellent sampling from molecular dynamics simulations, the authors should demonstrate co-operativity between the subunits.

Our molecular dynamic (MD) simulations span 20 µsec of SBPase in the dimeric state, starting from the experimental structures determined by XRC. In the considered time window, the only significant events that we observed are the local reorganization of the LBH motif that is a prerequisite for dimer rearrangement. We infer that local disorder contributes a separation of the pair of subunits in order to later allow for the building of the active homotetramer, at longer time scales that are outside the capacities used in this work. Moreover, demonstrating cooperativity with MD simulations would require more than a single event to ensure that results are significant, and performing series of 20µs-MD of SBPase is also outside the available capacities.

Author response:

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

eLife assessment

This study provides a useful strategy for treating mouse cutaneous squamous cell carcinoma (mCSCC) with serum derived from mCSCC-exposed mice. The exploration of serum-derived antibodies as a potential therapy for curing cancer is particularly promising but the study provides inadequate evidence for specific effects of mCSCC-binding serum antibodies. This study will be of interest to scientists seeking a novel immunotherapic strategy in cancer therapy.

Joint Public Review:

Summary:

This study presents an immunotherapeutic strategy for treating mouse cutaneous squamous cell carcinoma (mCSCC) using serum from mice inoculated with mCSCC. The author hypothesizes that antibodies in the generated serum could aid the immune system in tumor volume reduction. The study results showed a reduction in tumor volume and altered expression of several cancer markers (p53, Bcl-xL, NF-κB, Bax) suggesting the potential effectiveness of this approach.

Strengths:

The approach shows potential effect on preventing tumor progression, from both the tumor size and the cancer biomarker expression levels bringing attention to the potential role of antibodies and B cell responses in cancer therapy.

We greatly appreciate your positive feedback on our study.

Weaknesses:

These are some of the specific things that the author could consider to strengthen the evidence supporting the claims in their study.

(1) The study fails to provide evidence of the specific effect of mCSCC-antibodies on mCSCC. The study utilized serum which also contains many immune response factors like cytokines that could contribute to tumor reduction. There is no information on serum centrifugation conditions, which makes it unclear whether immune components like antigen-specific T cells, activated NK cells, or other immune cells were removed from the serum. The study does not provide evidence of neutralizing antibodies through isolation, analysis of B cell responses, or efficacy testing against specific cancer epitopes. To affirm the specific antibodies' role in the observed immune response, isolating antibodies rather than employing whole serum could provide more conclusive evidence. Purifying the serum to isolate mCSCC-binding antibodies, such as through protein A purification, and ELISA would have been more useful to quantify the immune response. It would be interesting to investigate the types of epitopes targeted following direct tumor cell injection. A more thorough characterization of the antibodies, including B cell isolation and/or hybridoma techniques, would strengthen the claim.

I am deeply appreciative of the reviewer's highly professional comments. Tumor development involves the coexistence of cancer cells at different developmental stages, each harboring a variety of known and unknown mutated proteins. These mutated proteins expose multiple known and unknown epitopes, each capable of stimulating the production of corresponding antibodies in healthy mice. Identifying all these antibodies presents a significant challenge. Current research methodologies, such as ELISA, WB, and ChIP, can only identify known antibodies based on existing antigens. A prerequisite for using these techniques is that both antigens and antibodies are identified. At present, there is no technology available to identify antibodies produced by an unknown mutated protein and epitope. However, I find the reviewer's comments insightful. Perhaps we can initially identify some known mCSCC-antibodies on mCSCC. However, studying the specific effect of these known mCSCC-antibodies on mCSCC is uncertain because we believe that tumor shrinkage results from the combined action of both known and unknown antibodies.

We concur with the reviewer's observations regarding the use of serum, which is rich in immune response factors such as cytokines that could potentially contribute to tumor reduction. In our future research, we plan to systematically analyze the individual roles of these antibodies and cytokines in tumor reduction. In 1973, Nature published a report indicating that serum demonstrated promising results in tumor treatment (Immunotherapy of Cancer with Antibody in Rats. Nature 243, 492 (1973). https://doi.org/10.1038/243492b0). Since then, there have been scarcely any reports on serum therapy for tumors. The primary focus of our study is to evaluate the efficacy of serum therapy in treating tumors. We hypothesize that antibodies and cytokines form a complex interactive network, working in synergy to reduce tumors. Consequently, we believe that studying these antibodies and cytokines in isolation may not yield effective results.

In this study, the methodology section outlines the process of serum preparation. It is important to note that serum is devoid of blood cells. I hypothesized that whole blood might have superior therapeutic effects compared to serum. This is because antibodies could potentially synergize with immune cells (including T cells, B cells, and NK cells), thereby enhancing the effectiveness of the treatment. As previously discussed, these antibodies, cytokines, and immune cells form a complex interactive network aimed at tumor reduction. Consequently, there are numerous factors that could influence the experimental outcomes, which presents a challenge for analyzing the results. Furthermore, the implementation of whole blood transfusion therapy introduces additional considerations, such as potential side effects and reactions associated with blood transfusions.

We thank the reviewers for their suggestion to purify the serum in order to isolate mCSCC-binding antibodies. As we previously mentioned, separating a large number of both known and unknown serum antibodies presents a significant technical challenge. We are eager to discuss and consider suggestions from the reviewers regarding methods to identify a large variety and number of unknown antibodies on cells. Perhaps, as the reviewer suggested, we could begin with known antibodies and employ Protein A purification technology to purify these antibodies and subsequently detect immune responses. We could also categorize the types of epitopes targeted, direct tumor cell injection, to study the epitopes of these types in further studies. The suggestion to study the response of B cells is valuable, and we plan to conduct comprehensive research on the response and status of B cells in our future studies.  

The purification of antibodies to enhance the specificity of their effectiveness against tumors is a critical aspect of our study. However, we would like to address some concerns raised. (1) The separation of all antibodies and cytokines presents a significant technical challenge. Particularly, there is a risk of overlooking antibodies that are present in low concentrations but play crucial roles. (2) What concerns us is that studying the composition separately would lose the overall effectiveness of the study. Our primary concern is that studying these components in isolation could compromise the holistic understanding of the study. This is akin to current research on traditional medicine, where the separation and individual study of compounds often result in a loss of overall therapeutic efficacy. For instance, consider a scenario where 100 antibodies collectively work to shrink a tumor. These antibodies interact with 20 cytokines, forming a complex network that enhances the cytokines' activity against tumor cells. Furthermore, many important antibodies and cytokines are currently unknown. Studying these antibodies in isolation could potentially result in the loss of this therapeutic effect. Therefore, in the discussion section, we have emphasized that our study considers a tumor mass, including tumor cells at various stages of development, as a single entity. As a practicing clinician, my primary focus is on the therapeutic outcomes in tumor treatments, despite the mechanisms of serum therapy remaining largely elusive, liking a black box.

(2) In the study design, the control group does not account for the potential immunostimulatory effects of serum injection itself. A better control would be tumor-bearing mice receiving serum from healthy non-mCSCC-exposed mice. Additionally, employing a completely random process for allocating the treatment groups would be preferable. Also, the study does not explain why intravenous injection of tumor cells would produce superior antibodies compared to those naturally generated in mCSCC-bearing mice.

I concur with the reviewer's perspective that using serum from healthy, non-mCSCC exposed mice as a control could potentially improve our study. Initially, our primary concern was to minimize harm to the mice and avoid excessive blood reactions, which led us to exclude the use of serum from healthy, non-mCSCC exposed mice in our control group. The main objective of our study was to investigate tumor shrinkage through serum treatment, specifically serum-derived antibodies. We anticipated that tumor-bearing mice receiving serum from healthy, non-mCSCC exposed mice would exhibit a response to the injected serum, which would manifest as a blood reaction. However, we did not expect this to result in a tumor treatment effect. If it turns out that normal serum (from healthy, non-mCSCC-exposed mice) possesses tumor-reducing properties, it would indeed be a novel discovery. We appreciate the reviewer's insightful suggestion and will consider incorporating it into our future research.

We concur with the reviewer's observations that the use of a completely random process for assigning treatment groups would be more desirable. Indeed, the complete randomization of the entire process further underscores the efficacy and universality of serum therapy. In this study, we utilized paired mice to mitigate the risk of cross-infection and adverse reactions associated with blood transfusions. We deeply value the reviewer's expert feedback.  

Lastly, the reason why tumor cells, when intravenously injected, produce antibodies superior to those naturally generated in mCSCC-bearing mice, is due to the following reasons. As tumor cells grow, they produce a variety of mutated proteins to adapt to the immune microenvironment and evade the immune system of mCSCC-bearing mice. However, these tumor cells with mutated proteins are exceptionally sensitive and recognizable to healthy mice. This recognition triggers an immune response in healthy mice, leading to the production of specific therapeutic antibodies. This simultaneous production of diverse and abundant antibodies is only achievable by living organisms.

(3) In Figure 2B, it would be more helpful if the author could provide raw data/figures of the tumor than just the bar graph. Similarly in Figure 3, the author should show individual data points in addition to the error bar to visualize the actual distribution.

Raw data (numerical values) have been incorporated into Figures 2B and 3, but the data is placed in the table below the graph. If placed above the error bar, it requires a small font and may not be clear.

(4) The author mentioned that different stages of tumor cells have different surface biomarkers. Therefore, experimenting with injecting tumor cells at various stages could reveal the most immunogenic stage. Such an approach would allow for a comparative analysis of immune responses elicited by tumor cells at different stages of development.

Yes, throughout the course of tumor development, tumor cells at various stages will exhibit distinct markers or possess different mutated proteins. The concept of segregating tumor cells from different stages and independently comparing their immune responses is indeed commendable. Future research could involve isolating cells that express identical biomarkers at each stage for a comparative analysis of the immune responses triggered by the tumor cells. However, this approach diverges from the original intent of this study.

Most tumor cells exist within the same developmental stage. However, this does not imply that all tumor cells within the tumor mass are at the same stage. For instance, a stage III liver cancer tumor may contain both stage I and stage IV tumor cells. Moreover, due to the complexity of tumor development, not all tumor cell surface markers are identical, even for tumors at the same stage. For instance, 20 major proteins and 100 minor proteins are implicated in tumor formation. In fact, random mutations in just 5 of these major proteins and 10 minor proteins can instigate the development of tumors. This implies that the protein pattern (tumor cell surface markers) associated with each individual's tumor is unique. While studying tumor cells at different stages separately allows for the observation of the immune response of tumor cells at each stage, it lacks a comprehensive research and treatment effect. For this reason, the design of this study treats a tumor mass as a whole, encompassing both the primary stage tumor cells and those not in that stage. These tumor cells are then injected to produce corresponding therapeutic antibodies. Furthermore, if tumor cells from only one stage are isolated and specific antibodies are produced against these cells, it could lead to immune escape of tumor cells at other stages, preventing the tumor from shrinking. Therefore, our approach aims to address this issue by considering the tumor mass as a whole.

(5) In the abstract the author mentioned that using mCSCC is a proof-of-concept for this potential cancer treatment strategy. The discussion session should extend to how this strategy might apply to other cancer types beyond carcinoma.

We have incorporated an additional paragraph in the discussion section where we delve into the concepts and experimental principles underpinning this study. This, we believe, addresses the reviewer's query regarding the applicability of our study's methodology to other types of tumors. The process for other tumors also involves isolating cells from the tumor, stimulating therapeutic antibody production in healthy mice using these cells, and ultimately reintroducing these antibodies into mice with tumors to facilitate tumor elimination

Recommendations For The Authors:

The author is encouraged to refine the study's design in future studies considering the weaknesses highlighted above, summarize the results more effectively, and seek opportunities to expand on this promising idea and enhance the research's impact and applicability.

We greatly appreciate the valuable suggestions provided by the editor and reviewers. These insights will certainly be addressed in our future research endeavors.

Suggestions for title modification:

Following the scope of the study, the term 'specific homologous neutralizing-antibodies' may be misleading as neutralizing antibodies typically refer to antibodies preventing viral cell entry. In cancer therapy, 'neutralization' is not a relevant concept, as cancer cells do not infect host cells. Using whole tumor cells as immunogens diverges from the specificity of traditional vaccination approaches that utilize well-defined proteins or antigens. Furthermore, the term "homologous" suggests a precision in targeting that is not demonstrated by reintroducing serum without isolating its specific components. Therapeutic effects should not be attributed to "neutralizing antibodies" without isolating or characterizing the antibody response or verifying their efficacy against specific cancer epitopes. Additionally, it is suggested that you indicate the biological system that your study utilised in the title. More so, this approach is not entirely novel, as seen with the use of adjuvants in some flu vaccines, or in Moderna's cancer vaccine mRNA-4157, which encodes up to 34 patient-specific tumor neoantigens. You can consider the title below or a variant of the same.

Suggested title: Generating serum-based antibodies from tumor-exposed mice: a potential strategy in cutaneous squamous cell carcinoma treatment

I concur with your suggestion and have modified the title to " Generating serum-based antibodies from tumor-exposed mice: a new potential strategy for cutaneous squamous cell carcinoma treatment ". I believe this research remains some new, hence the addition of the word "new". Furthermore, the term "novel" in the paper has been either removed or substituted.

Moreover, I propose that this study shares similarities with Moderna's cancer vaccine mRNA-415, albeit with certain differences. Moderna's cancer vaccine mRNA-415 encodes 34 recognized neoantigens to stimulate an immune response by eliciting specific T cell responses. This is similar to the strategy of some companies developing a protein set for diagnosing lung cancer, liver cancer, among others. Without a doubt, these methods have improved the effectiveness of tumor diagnosis and treatment. However, I think that these methods currently face challenges in completely eradicating tumors because they perceive tumors as a static process and cells that express certain mutated proteins in a fixed manner. I believe that small molecule antibodies, cytokines, and immune cells present in serum that are difficult to detect, have low concentrations, or are unknown are essential for maintaining the expression of important mutant proteins and the escape of tumor cells. This is also the primary reason why tumors are difficult to treat and prone to recurrence at present.

From my perspective, different tumors, as well as different stages of the same tumor, express varying mutated proteins or surface markers. Targeting some may result in others escaping or even creating a more conducive growth environment for those that do escape. Our study adopts a comprehensive view of a tumor block, encompassing tumor cells at different stages and tumor cells at the same stage but expressing different biomarkers. This approach generates a multitude of known and unknown antibodies that work in concert with cytokines and immune cells. While our method may not be capable of generating all mutated proteins and epitope antibodies due to the weakness of some antigens (epitopes of mutated proteins), it can still be effective. As long as the number of tumor cells is reduced below a certain threshold following multiple rounds of treatment with various antibodies produced at different stages, these cancer cells can be eradicated by the body's immune system. This is a process that is real-time and dynamic. Undoubtedly, if it becomes evident that alterations in a set of proteins can bolster the immune system and eradicate tumor cells, then the implications are significant. The immunotherapy proteins, which have demonstrated positive therapeutic effects, developed by certain companies are also predicated on this very principle.

Finally, I greatly appreciate your suggestions, which will be considered and gradually addressed in future research.

Author response:

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

Reviewer #1 (Public Review): 

In the manuscript "Mechanistic target of rapamycin (mTOR) pathway in Sertoli cells regulates age-dependent changes in sperm DNA methylation", the authors proposed to test if the balance of mTOR complexes in Sertoli cells may play a significant role in age-dependent changes in the sperm epigenome. The paper could be of interest and has a good scientific aim but there are too many drawbacks that hamper the initial enthusiasm. All sections need extensive revision. The paper is mostly descriptive without a mechanistic-orientated explanation for the observed results. 

Comments on revised version: 

I am not sure that the authors have made an attempt to clearly answer the reviewers comments that aimed to improve the quality of the manuscript. It stands as mostly descriptive and with limited interest as it is. 

We are thankful to the reviewer for agreeing to review our revised manuscript. Unfortunately, we completely disagree with the evaluation provided by the reviewer. Research on sperm DNA methylation experienced a significant rise of interest in the current century and by now more than 2000 papers have been published. Although it was demonstrated that the sperm DNA methylome may be affected by almost every factor analyzed, no study was published to identify molecular mechanisms that may link these factors with the sperm epigenome. Our study is the FIRST to identify such a mechanism (mTOR complexes balance in Sewrtoli cells). More so, we demonstrated experimentally that manipulations of this mechanism allow regulation of the rates of epigenetic aging of sperm in both directions (accelerate aging or rejuvenate). Thus, our study provides a mechanistic background for the development of therapeutic interventions that may target sperm epigenome.

We acknowledge that our study does not provide the full cascade of events linking the balance of mTOR complexes in Sertoli cells with the sperm DNA methylome. It suggests, however, the most plausible event next in a cascade (BTB permeability changes). Our group is working on this question now and we hope to provide the answer soon in a separate study. Even after that, we will be far from understanding the complete chain of molecular events that link mTOR and sperm methylome. It may take many years and significant effort of many research groups to dissect the whole cascade. It is worth mentioning that understanding of a complete cascade involved in pathology is not needed to develop efficient therapies if the critical nodes are known. For many common drugs (e.g. metformin) we do not know the full chain of molecular mechanisms but use them successfully.

Thus, we believe that our study is mechanistic as it identified a critical mechanism manipulation of which allows experimental aging and rejuvenation of the sperm methylome. Additionally, it generates new mechanistic questions and hypotheses to be answered in the future.

Reviewer #3 (Public Review): 

Summary and Strength: 

The manuscript by Amir et al. describes that Sertoli-specific inactivation of the mTORC1 and mTORC2 complex by KO of either Raptor or Rictor, respectively, resulted in progressive changes in blood-testis-barrier (BTB) function, testis weight, and sperm parameters, including counts, morphology, mtDNA content and sperm DNA methylation. 

The described studies are based on the hypothesis that a decline of BTB function with increasing chronological age of a male contributes to the DNA methylation changes that are known to occur in sperm DNA of old males when compared to sperm DNA from isogenic young males. In order to demonstrate the relevance of a functioning BTB for the maintenance of sperm methylation patterns, the authors generated mice with genetically disrupted mTORC2 complex or mTORC1 complex in Sertoli cells and determined sperm methylation patterns in comparison to isogenic wild-type males. In line with previously published scientific literature (e.g. Mok et al., 2013; Dong et al, 2015; and others), the manuscript corroborates that a Sertoli-cell specific deletion of mTORC2 caused a loss of BTB function and a progressive spermatogenic defect. The authors further show that sperm DNA is differentially methylated (DMRs) as a consequence of either a mTORC2 disruption (associated with a loss of BTB function) or following a mTORC1 disruption (BTB function either increased or not leaky) when compared to their isogenic age-matched wt controls. Those DMRs overlap partially with changes in sperm DNA methylation that were found when comparing sperm from 8-week males with sperm isolated from 22-week-old male mice. 

The authors interpret the observed changes as representative of the sperm DNA methylation changes that occur during normal chronological aging of the male. For an aged control group, the authors use sperm DNA of 22-week-old wild-type mates from the mTORC2 and mTORC2 KO breeding and compare the sperm methylation patterns found in sperm from those 22-week males to 8-week young males, that are intended to represent an old and a young cohort, respectively. DNA methylation analysis indicates that a disruption of mTORC2 (& decrease of BTB function) results in increased DNA methylation of sperm DNA, while a disruption of mTORC1 (and proposed increase of BTB tightness, not shown in the manuscript, though) resulted in increased hypomethylation. 

Weaknesses: 

While the hypothesis and experimental system are interesting and the data demonstrating the relevance of the mTORC2 complex for BTB function is convincing, several open questions limit the evidence that supports the hypothesis that the sperm DNA methylation changes seen in old males are caused by BTB failure following an imbalance of mTOR signaling complexes. The major critique points are the lack of a chronologically old group and the choice of 8 weeks & 22 weeks age of age: 

- Data illustrating the degree of BTB decline and sperm DNA methylation changes from chronologically "old" male mice is missing. 22-week-old mice are not considered old but are of good and mature breeding age, equivalent to humans in their mid-late twenties. (In the manuscript, the 22-week-old wildtype mice show no evidence of BTB breakdown (Figure 3), so why are their sperm used to represent "aged" sperm? 

- Adding a group of "old" wild-type mice of 12-14 months of age, which is closer to the end of effective reproduction in mice, more equivalent to 45-59 year-old humans) could be used to illustrate that (a) aging causes a marked decrease in BTB function at this time in mouse life, and that this BTB breakdown chronologically aligns with the age-associated DNA hypermethylation seen in old sperm. Age-matched "old" mTORC1 KO, with a (supposedly) tighter BTB barrier, could then be expected to have a sperm DMA methylation profile closer to that of younger wild-type animals. Such data are currently missing. While the progressive testicular decline observed in the mTORC1 KO (Fig.5) could make it difficult to obtain the appropriately aged mTORC1 KO tissues, it is completely feasible to obtain data from chronologically old wild-type males. (The progressive testicular decline further raises the question of what additional defects the KO causes, and how such additional defects would influence the sperm DNA methylation profile.) The addition of data from an old group to the currently included groups could strengthen the interpretation that the observations in the BTB-defective mTORC2 KO mice are modelling an age-related testicular decline, provided that the DMRs seen in the chronologically old group significantly overlap with the BTB-defective changes. 

- In the current form, the described differences in sperm DNA methylation are based on comparisons between pubertal mice (8 weeks) and mature but not old adult males (22 weeks), while a chronologically "old" group is missing from the data sets and comparisons. Thus, it appears that the described sperm methylation changes reflect developmental changes associated with normal maturation and not necessarily declining sperm quality due to aging. (Sperm obtained from 8-week-old mice likely were generated, at least in part, during the 1st wave of spermatogenesis, which is known to differ from the continuously proceeding spermatogenesis during the remained of the mature life. During the 1st wave of spermatogenesis, Sertoli cells are known to undergo gene expression changes which could contribute to varying degrees of BTB function, and thus have effects on the sperm DNA methylation profiles of such 1st wave sperm.) 

- It is unclear why the aging-related DMRs between the 8 and 22-week-old wild-type mice vary so dramatically between the two wild-type groups derived from the mTORC1 and the mTORC2 breeding (Fig. S4). If the main difference was due to mTORC1 or mTORC2 activity, both wildtype groups should behave very similarly. Changes seen in a truly "old" mouse (e.g. 20 weeks to 56 weeks), changes in "young mTORC1" and in "old mTORC2" are missing.

How do those numbers and profiles compare to the shown samples? 

Comments on latest version: 

The rebuttal letter and public response indicate the authors' reluctance to consider the limitations of their study, i.e. having chosen chronologically young animals to demonstrate a sperm aging effect and indicate that they are not willing to include adequate controls. 

Since there is no evidence that mice at this young age have a deteriorating blood-testis-barrier (indeed, normal intact BTB is clearly visible in the figures included in this study from animals of the relevant age group), the whole central hypothesis that the study is built upon (i.e. that increasing age causes deteriorating BTB integrity which in turn causes age-related changes in sperm DNA methylation), appears irrelevant or invalid. 

The authors' claim that age-related DNA methylation changes in sperm occur in linear fashion and that the changes are somewhat proportional with chronological age is in stark contrast of the claim that a decline of the BTB in old animals is causative for age-related sperm epigenetic changes, putting the relevance of the whole study in question. 

We are thankful to the reviewer for agreeing to review our revised manuscript. We disagree with the evaluation provided by the reviewer, however.

First, the reviewer misinterpreted the hypothesis of the study, although it is formulated in the last sentence of the Introduction:  “ … we hypothesized that the balance of mTOR complexes in Sertoli cells may also play a significant role in age-dependent changes in the sperm epigenome.” Instead, the reviewer assigned a different hypothesis to our study (that BTB integrity changes are responsible for age-dependent changes in sperm DNA methylation) and criticized us for not providing clear testing of this hypothesis.

To clarify, we believe that our study provides high-quality testing of OUR hypothesis as we demonstrated experimentally that manipulations of mTOR complexes balance in Sertoli allow acceleration and deceleration of epigenetic aging of sperm. Additionally, our study generated a hypothesis that BTB permeability may mediate the effects of the mTOR pathway on sperm methylome. This second hypothesis is to be tested in the future research.

We also disagree with the reviewer's interpretation of the aging process as an abrupt transition from a young, healthy, and undamaged state to an old, moribund, and damaged state. The whole body of biogerontological knowledge suggests instead steady accumulation of damage over lasting periods of time. For example, this understanding of steady change at the molecular level allowed the development and successful use of epigenetic clock and other molecular clock models, including several variants of sperm epigenetic clocks. These models clearly demonstrate linear or semi-linear accumulation in DNA-methylation changes in various tissues and biological species across the whole lifespan. It is reasonable to assume that BTB permeability decreases with age steadily as well and that in younger animals this decrease may be not easily detected by the existing analytical methods. Experimental data showing the dynamics of the BTB deterioration over age do not exist to our knowledge although it was demonstrated that older animals have loose BTB as compared with young. We agree with the reviewer that future studies testing the role of BTB deterioration for sperm methylome aging will need to provide such evidence. It was not the subject of the current study, however.

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

Reviewer #1 (Public Review):

In the manuscript "Mechanistic target of rapamycin (mTOR) pathway in Sertoli cells regulates age-dependent changes in sperm DNA methylation", the authors proposed to test if the balance of mTOR complexes in Sertoli cells may play a significant role in age-dependent changes in the sperm epigenome. The paper could be of interest and has a good scientific aim but there are too many drawbacks that hamper the initial enthusiasm. All sections need extensive revision. The paper is mostly descriptive without a mechanistic-orientated explanation for the observed results.

Specific comments:

(1) The abstract is poorly written. There is a lot of unnecessary introduction that does not provide a rationale for the work. It is not possible to understand the experimental approach or the major data just by reading the abstract. It does not clearly represent the work.

- We have added details of experimental design and results to the abstract and reduced the introductory part of the abstract.

(2) The introduction is somewhat vague and does not provide a clear rationale for the hypothesis. There should be more focus more on the role of mTOR in Sertoli cells that goes far beyond BTB. That will give more focus on mTOR. Then it is important to focus on BTB and mTOR: what is known? What is the gap and how can it be solved? Several relevant references are missed concerning mTOR and Sertoli cells.

- The goal of this study was not to explore all potential roles of mTOR pathway in Sertoli cells, but to test if shifts in the balance of mTOR complexes regulate (accelerate/decelerate) epigenetic aging of sperm. As such, we disagree with the reviewer and consider that the current Introduction provides a focused rational for the study.

(3) The Material and Methods section needs improvement. There is much important information missing. For instance: how many animals were used per group and how was the breeding done? At what age? Statistical analysis should be explained in detail.

- The number of animals was clearly stated in the original manuscript. We have added details of breeding and statistical analysis. 

(4) The results description could be improved. It is vague without highlighting how much difference was detected. The results should be numerically described when possible and the differences should be highlighted. A 10% difference may be significant but not biologically relevant. To correctly evaluate the differences it is important to describe them with some degree of detail.

- For all DNA methylation experiments we provide numerical characteristics of methylation changes, including numbers of DMRs, % change, significance, correlation coefficients. We believe that only age- and genotype-associated changes in reproductive parameters were not characterized in our manuscript in detail. We have added Table 1 to provide these numbers.

(5) There is no discussion of the data. The authors just summarize their findings without a comprehensive analysis of the literature and how the effects can be mediated. mTOR interacts with different pathways (mTORC1 and mTORC2 are even mediators of distinct pathways). This would be very relevant to discuss. In addition, there are many study limitations not discussed. There is no clear mechanistic explanation of the way by which the mTOR pathway in Sertoli cells regulates age-dependent changes in sperm DNA methylation. The paper seems preliminary.

- We have added an additional paragraph to the discussion to highlight a potential molecular mechanism that links mTOR pathway with the sperm epigenome.

(6) Figure 1 is too simple and does not provide any schematic support for the text.

- We disagree with the reviewer and believe that the figure represents a good visualization of our hypothesis useful for the perception of the study.

(7) Figure 2 lacks some detail. For instance, how many animals were used for each step?

- Numbers of animals are provided in the text of the paper.

(8) Taking into consideration the roles of mTOR on sperm, particularly mTORC1, it is not clear whether there were any differences in sperm motility.

- We did not assess sperm motility in this study. 

Reviewer #2 (Public Review):

In this study, the authors hypothesized that the balance of mTOR complexes in Sertoli cells may also play a significant role in age-dependent changes in the sperm epigenome. To test this hypothesis, the authors use transgenic mice with manipulated activity of mTOR complexes in Sertoli cells. These results suggest that the mTOR pathway in Sertoli cells may be used as a novel target of therapeutic interventions to rejuvenate the sperm epigenome in advanced-age fathers.

The authors attempt to demonstrate that the balance of mTOR complexes in Sertoli cells regulates the rate of sperm epigenetic aging. The authors have effectively met their research objectives, and their conclusions are supported by the data presented.

- We are very thankful for the positive evaluation of our study.

Reviewer #3 (Public Review):

Summary and Strength:

The manuscript by Amir et al. describes that Sertoli-specific inactivation of the mTORC1 and mTORC2 complex by KO of either Raptor or Rictor, respectively, resulted in progressive changes in blood-testis-barrier (BTB) function, testis weight, and sperm parameters, including counts, morphology, mtDNA content and sperm DNA methylation.

The described studies are based on the hypothesis that a decline of BTB function with increasing chronological age of a male contributes to the DNA methylation changes that are known to occur in sperm DNA of old males when compared to sperm DNA from isogenic young males. In order to demonstrate the relevance of a functioning BTB for the maintenance of sperm methylation patterns, the authors generated mice with genetically disrupted mTORC2 complex or mTORC1 complex in Sertoli cells and determined sperm methylation patterns in comparison to isogenic wild-type males. In line with previously published scientific literature (e.g. Mok et al., 2013; Dong et al, 2015; and others), the manuscript corroborates that a Sertoli-cell specific deletion of mTORC2 caused a loss of BTB function and a progressive spermatogenic defect. The authors further show that sperm DNA is differentially methylated (DMRs) as a consequence of either a mTORC2 disruption (associated with a loss of BTB function) or following a mTORC1 disruption (BTB function either increased or not leaky) when compared to their isogenic age-matched wt controls. Those DMRs overlap partially with changes in sperm DNA methylation that were found when comparing sperm from 8-week males with sperm isolated from 22-week-old male mice.

The authors interpret the observed changes as representative of the sperm DNA methylation changes that occur during normal chronological aging of the male. For an aged control group, the authors use sperm DNA of 22-week-old wild-type mates from the mTORC2 and mTORC2 KO breeding and compare the sperm methylation patterns found in sperm from those 22-week males to 8-week young males, that are intended to represent an old and a young cohort, respectively. DNA methylation analysis indicates that a disruption of mTORC2 (& decrease of BTB function) results in increased DNA methylation of sperm DNA, while a disruption of mTORC1 (and proposed increase of BTB tightness, not shown in the manuscript, though) resulted in increased hypomethylation.

Weaknesses:

While the hypothesis and experimental system are interesting and the data demonstrating the relevance of the mTORC2 complex for BTB function is convincing, several open questions limit the evidence that supports the hypothesis that the sperm DNA methylation changes seen in old males are caused by BTB failure following an imbalance of mTOR signaling complexes. The major critique points are the lack of a chronologically old group and the choice of 8 weeks & 22 weeks age of age:

- Data illustrating the degree of BTB decline and sperm DNA methylation changes from chronologically "old" male mice is missing. 22-week-old mice are not considered old but are of good and mature breeding age, equivalent to humans in their mid-late twenties. (In the manuscript, the 22-week-old wildtype mice show no evidence of BTB breakdown (Figure 3), so why are their sperm used to represent "aged" sperm?

- Adding a group of "old" wild-type mice of 12-14 months of age, which is closer to the end of effective reproduction in mice, more equivalent to 45-59 year-old humans) could be used to illustrate that (a) aging causes a marked decrease in BTB function at this time in mouse life, and that this BTB breakdown chronologically aligns with the age-associated

DNA hypermethylation seen in old sperm. Age-matched "old" mTORC1 KO, with a (supposedly) tighter BTB barrier, could then be expected to have a sperm DMA methylation profile closer to that of younger wild-type animals. Such data are currently missing. While the progressive testicular decline observed in the mTORC1 KO (Fig.5) could make it difficult to obtain the appropriately aged mTORC1 KO tissues, it is completely feasible to obtain data from chronologically old wild-type males. (The progressive testicular decline further raises the question of what additional defects the KO causes, and how such additional defects would influence the sperm DNA methylation profile.) The addition of data from an old group to the currently included groups could strengthen the interpretation that the observations in the BTB-defective mTORC2 KO mice are modelling an age-related testicular decline, provided that the DMRs seen in the chronologically old group significantly overlap with the BTB-defective changes.

- In the current form, the described differences in sperm DNA methylation are based on comparisons between pubertal mice (8 weeks) and mature but not old adult males (22 weeks), while a chronologically "old" group is missing from the data sets and comparisons. Thus, it appears that the described sperm methylation changes reflect developmental changes associated with normal maturation and not necessarily declining sperm quality due to aging. (Sperm obtained from 8-week-old mice likely were generated, at least in part, during the 1st wave of spermatogenesis, which is known to differ from the continuously proceeding spermatogenesis during the remained of the mature life. During the 1st wave of spermatogenesis, Sertoli cells are known to undergo gene expression changes which could contribute to varying degrees of BTB function, and thus have effects on the sperm DNA methylation profiles of such 1st wave sperm.)

- It is unclear why the aging-related DMRs between the 8 and 22-week-old wild-type mice vary so dramatically between the two wild-type groups derived from the mTORC1 and the mTORC2 breeding (Fig. S4). If the main difference was due to mTORC1 or mTORC2 activity, both wildtype groups should behave very similarly. Changes seen in a truly "old" mouse (e.g. 20 weeks to 56 weeks), changes in "young mTORC1" and in "old mTORC2" are missing. How do those numbers and profiles compare to the shown samples?

Some general comments regarding the chosen age of animals:

- As mentioned, sperm from 8-week-old mice represent many sperm that were produced in the 1st wave of spermatogenesis; 22-week-old mice are not considered chronologically old mice, but mature and "relatively" young animals. 18-24 month-old mice are considered to be equivalent to 56-69 year-old humans, and might be more suitable to detect aging effects. "Old mice" for study purposes should be at least 12-14 months of age, ideally >18 months of age. 22 weeks (5 months of age) are mice at good breeding age, but still considered mature adults, not old males, and therefore are not expected to show typical aging health problems (like declining fertility).

Even the cited reference (Flurkey et al. 2007) defines that "... mice used a reference group for "young mice" should be at least 3 months of age (~ 13 weeks), i.e. fully sexually mature. The authors specifically state: " The young adult group should be at least 3 months old because, although mice are sexually mature by 35 days, relatively rapid maturational growth continues for most biologic processes and structures until about 3 months. The upper age range for the young adult group is typically about 6 months. ... For the middleaged group, 10 months is typically the lower limit.... The upper age limit for the middleaged group is typically 14-15 months, because at this age, most biomarkers still have not changed to their full extent, and some have not yet started changing. For the old group, the lower age limit is 18 months because age-related change for almost all biomarkers of aging can be detected by then. The upper limit is 22-26 months, depending on the genotype." According to this reference, mice up to 6 months of age are generally considered "mature adults" (equivalent to humans 20-30 yrs), mice of 10-14 month are "middle-aged adults" (equivalent to ~38-47 human years) and 18-24 month mice are "old" (equivalent to human of 56-69 yrs.).

Going on these commonly used age ranges, it is unclear why the authors used 8-week-old mice (generally considered pubertal to late adolescent age) as young mice and 5-month-old mice as "old mice".

Differences seen between these cohorts most likely do not reflect aging, but more likely reflect changes associated with normal developmental maturation, since testis and epididymides continue to grow until about 10-11 weeks of age.

- The DMRs identified between 8 and 22-week-old animals could represent DMRs that are dependent on developmental maturation more than being changed in an "age-dependent" manner (in the sense of increased chronological age). This interpretation is congruent with the fact that those DMRs are enriched for developmental categories.

- We are thankful to the reviewer for a detailed explanation of their disagreement with the ages of mice used in this study. In short, the reviewer suggests that our older group (22 weeks) is not old enough to represent aged animals and our young group (8 weeks) may still have spermatozoa from the first wave of spermatogenesis, and as such the observed differences between the 2 ages cannot be considered as aging-related but rather may represent different stages of maturation of the reproductive system. At the first glance this criticism looks valid. 

However, to design our experiments we used our data that was not included to this manuscript initially. These data demonstrated that age dependent changes in sperm DNA are linearly or semi linearly associated with age in the age range from 56 to 334 days. Thus, within this interval any 2 ages, distant enough to register the difference in DNA methylation, can be used to assess age dependent changes in DNA methylation and changes in the rates of epigenetic aging of sperm in response to genetic manipulations. We have added these results now, - see “Identification of agedependent patterns in sperm DNA methylation” section in Material and Methods and “Patterns of age-dependent changes in sperm DNA methylation” in Results. We also consider that the reviewer’s suggestion that sperm from 8-week-old mice represents the first wave of spermatogenesis does not have ground. Indeed, C57BL/6 mice first have fertile sperm in cauda epididymis at 37 days of age [1], 19 days earlier than the age of 56 days (8 weeks) at which sperm was collected in our study in the youngest group of mice. Given that young C57BL/6 mice ejaculate spontaneously around 3 times per 5 days [2], 8 weeks old mice have ejaculated > 10 times since the first wave of spermatogenesis before the sperm was collected for our study, making negligibly small the chances of survival of any first wave sperm in their cauda epididymides to the age of 8 weeks. We have added this information to the text.

(1) Mochida, K.; Hasegawa, A.; Ogonuki, N.; Inoue, K.; Ogura, A. Early Production of Offspring by in Vitro Fertilization Using First-Wave Spermatozoa from Prepubertal Male Mice. J. Reprod. Dev. 2019, 65, 467–473, doi:10.1262/jrd.2019-042.

(2) Huber, M.H.; Bronson, F.H.; Desjardins, C. Sexual Activity of Aged Male Mice: Correlation with Level of Arousal, Physical Endurance, Pathological Status, and Ejaculatory Capacity. Biol. Reprod. 1980, 23, 305–316, doi:10.1095/biolreprod23.2.305.

Author response:

We thank the editors and reviewers for their enthusiasm for this work and helpful suggestions. In summary, the reviewers provided suggestions for additional discussion items and clarifications for the text and figures, especially in relation to the cryo-EM structures and suppressor screen sections of the manuscript. We will consider each of these and make edits as needed. In particular, reviewers asked for further details about the structural model in addition to analysis of our new structure with respect to previously reported intron lariat spliceosome (ILS) complexes. For the latter point, we present additional evidence for the correct assignment of Yju2 in the S. cerevisiae ILS structure and note that docking of the 3’ splice site is not observed in any ILS structure from yeast, worms, or humans. This is consistent with our proposed mechanism. We will clarify these points in the text as well highlight some caveats of prior studies of the ILS complex. We feel that these changes will add additional nuance to the manuscript as well as clarify the findings and their context and significance for the reader.

Author response:

We would like to thank all reviewers for their valuable comments that help us to improve our manuscript. We will make the following modifications in the revised manuscript:

(1) To reduce the complexity of the experiments we carried out, we will summarize trimeric G proteins in Ciona in the first paragraph of the Result section and explain how we focused on Gas and Gaq in the initial phase of this study.

(2) As the reviewer 1 suggested, the polymodal roles of papilla neurons are interesting. We will add a discussion regarding this aspect. The sentences will be like the following:

“The recent study (Hoyer et al., 2024) provided several lines of evidence suggesting that papilla neurons can serve as the sensors of several chemicals in addition to the mechanical stimuli. This finding and our model seem mutually related because these chemicals could modify Ca2+ and cAMP signaling. The use of G protein signaling may allow Ciona to reflect various environmental stimuli to initiate metamorphosis in the appropriate situation, both mechanically and chemically.”

(3) As both reviewers suggested, imaging cAMP on the backgrounds of some G protein knockdowns and pharmacological treatments is important, and we will carry out some of these experiments.

(4) According to reviewer 2's comment, we will carefully modify the text about interpreting the results so that the descriptions suitably reflect the results.

Author response:

Response to reviewers (Public review):

We thank all the three reviewers for their opinion on our work on Candida albicans β-1,6-glucan, which highlights the importance of this cell wall component in the biology of fungi. Here are our responses to their comments for public reviews:

(1) Indeed, the data presented for immunological studies is preliminary. It has been acknowledged by the reviewers that our analysis providing insights into the biosynthetic pathways involved in comprehensive in dealing with organization and dynamics of the β-1,6-glucan polymer in relation with other cell wall components and environmental conditions (temperature, stress, nutrient availability, etc.). However, we anticipated that there would be immediate curiosity as to what the immunological contribution of β-1,6 glucan and we therefore felt we needed to initiative these studies and include them. We therefore performed immunological studies to assess whether β-1,6-glucans act as a pathogen-associated molecular pattern (PAMP), and if so, what its immunostimulatory potential is. Our data clearly suggest that β-1,6-glucan is a PAMP, and consequently lead to several questions: (a) what are the host immune receptors involved in the recognition of this polysaccharide, and thereby the downstream signaling pathways, (b) how is β-1,6-glucan differentially recognized by the host when C. albicans switches from a commensal to an opportunistic pathogen, and (c) how does the host environment impact the exposure of this polysaccharide on the fungal surface. We believe addressing these questions is beyond the scope of the present manuscript and aim to present new data in future manuscript. Nonetheless, in the revised manuscript, suggest approaches that we can take to identify the receptor that could be involved in the recognition of β-1,6-glucan. Moreover, we have modified the discussion presenting it based on the data rather than being descriptive.    

(2) It will be interesting to assess the organization of β-1,6-glucan and other cell wall components in the opaque cells. It is documented that the opaque cells are induced at acidic pH and in the presence of N-acetylglucosamine and CO2. Our data shows that pH has an impact on β-1,6-glucan, which suggests that there will be differential organization of this polysaccharide in the cell wall of opaque cells. As suggested by the reviewer, we will include analysis of opaque cells (and other C. albicans cell types) in future studies.

With the exception of these major new avenues for this research, our revision can address each of the comments provided by the reviewers.

Author response:

Reviewer #1 (Public Review): 

Summary: 

In this study, Masroor Ahmad Paddar and his/her colleagues explore the noncanonical roles of ATG5 and membrane ATG8ylation in regulating retromer assembly and function. They begin by examining the interactomes of ATG5 and expand the scope of these effects to include homeostatic responses to membrane stress and damage. 

Strengths: 

This study provides novel insights into the noncanonical function of ATG8ylation in endosomal cargo sorting process. 

Weaknesses: 

The direct mechanism by which ATG8ylation regulates the retromer remains unsolved. 

We agree with the reviewer.  We do however show how at least one aspect of ATG8ylation contributes to the proper retromer function, which occurs via lysosomal membrane maintenance and repair. Understanding the more direct effects on retromer will require a separate study. We will emphasize this in the revised manuscript and point out the limitations of the present work.

Reviewer #2 (Public Review): 

Summary:

Padder et al. demonstrate that ATG5 mediates lysosomal repair via the recruitment of the retromer components during LLOMe-induced lysosomal damage and that mAtg8-ylation contributes to retromer-dependent cargo sorting of GLUT1. Although previous studies have suggested that during glucose withdrawal, classical autophagy contributes to retromer-dependent GLUT1 surface trafficking via interactions between LC3A and TBC1D5, the experiments here demonstrate that during basal conditions or lysosomal damage, ATGs that are not involved in mATG8ylation, such as FIP200, are not functionally required for retromer-dependent sorting of GLUT1. Overall, these studies suggest a unique role for ATG5 in the control of retromer function, and that conjugation of ATG8 to single membranes (CASM) is a partial contributor to these phenotypes. 

Strengths: 

(1) Overall, these studies suggest a unique non-autophagic role for ATG5 in the control of retromer function. They also demonstrate that conjugation of ATG8 to single membranes (CASM) is a partial contributor to these phenotypes. Overall, these data point to a new role for ATG5 and CASM-dependent mATG8ylation in lysosomal membrane repair and trafficking. 

(2) Although the studies are overall supportive of the proposed model that the retromer is controlled by CASM-dependent mATG8-ylaytion, it is noteworthy that previous studies of GLUT1 trafficking during glucose withdrawal (Roy et al. Mol Cell, PMID: 28602638) were predominantly conducted in cells lacking ATG5 or ATG7, which would not be able to discriminate between a CASM-dependent vs. canonical autophagy-dependent pathway in the control of GLUT1 sorting. Is the lack of GLUT1 mis-sorting to lysosomes observed in FIP200 and ATG13KO cells also observed during glucose withdrawal? Notably, deficiencies in glycolysis and glucose-dependent growth have been reported in FIP200 deficient fibroblasts (Wei et al. G&D, PMID: 21764854) so there may be differences in regulation dependent on the stress imposed on a cell. 

We thank the reviewer on the overall assessment of the strengths of the study.

We have discussed in the manuscript the elegant study by Roy et al., PMID 28602683. To accommodate reviewer’s comment, we will additionally emphasize in the text that our study is focused on basal conditions and conditions that perturb endolysosomal compartments. We agree with the reviewer that under metabolic stress conditions (such as glucose limitation) more complex pathways may be engaged and will acknowledge that in the discussion.

Weaknesses: 

(1) Additional controls are needed to clarify the role of CASM in the control of retromer function. Because the manuscript proposes both CASM-dependent and independent pathways in the ATG5 mediated regulation of the retromer, it is important to provide robust evidence that CASM is required for retromer-dependent GLUT1 sorting to the plasma membrane vs. lysosome. The experiments with monsensin in Fig. 7C-E are consistent with but not unequivocally corroborative of a role for CASM.

We fully agree with the reviewer. In fact, our data with bafilomycin A1 treatment causing GLUT1 miss-sorting (manuscript line 317) show that it is the perturbance of lysosomes  and not CASM per se that leads to mis-sorting of GLUT1 (Fig. 7D,E). Note that it has been shown (PMIDs: 28296541, 25484071 and 37796195) that although bafilomycin A1 deacidifies lysosomes it does not induce but instead inhibits CASM. This is because bafilomycin A1 cases dissociation of V1 and V0 sectors of V-ATPase, unlike other CASM-inducing agents which promote V1 V0 association. Complementing this, our data with ATG2AB DKO and ESCRT VPS37A KO (Fig. 8A-F) indicate that the repair of lysosomes is important to keep the retromer machinery functional (as illustrated in Fig. 8G). This may be one of the effector mechanisms downstream of membrane atg8ylation in general and hence also downstream of CASM. We will revise Fig. 7 title to read “Lysosomal damage causes GLUT1 mis-sorting” and will explain these relationships in the text.

Based on the results shown with ATG16KO in Fig 4A-D, rescue experiments of these 16KO cells with WT vs. C-terminal WD40 mutant versions of ATG16 will specifically assess the requirement for CASM and potentially provide more rigorous support for the conclusions drawn. 

We will carry out the experiment proposed by the reviewer for the planned revision.

(2) Also, the role of TBC1D5 should be further clarified. In Fig S7, are there any changes in the interactions between TBC1D5 and VPS35 in response to LLOMe or other agents utilized to induce CASM?

We thank the reviewer for pointing this out. We do have data with VPS35 in co-IPs shown in Fig. S7.  There is no change in the amounts of VPS35 or TBC1D5 in GFP-LC3A co-IPs. We will include a graph with quantification in the revised manuscript and emphasize this point.

Does TBC1D5 loss-of-function modulate the numbers of GLUT1 and Gal3 puncta observed in ATG5 deficient cells in response to LLOMe? 

We agree that TBC1D5 is an interesting aspect. However, because TBC1D5 does not change its interactions in the experiments in our study, we consider this topic (i.e. whether TBC1D5 phenocopies VPS35 and ATG5 KOs in its effects on Gal3) to be beyond the scope of the present work. We underscore that LLOMe (lysosomal damage) mis-sorts GLUT1 even without any genetic intervention (e.g., in WT cells in the absence of ATG5 KO; Fig. 7). Thus, in our opinion the effects of TBC1D5 inactivation may be a moot point.

(3) Finally, the studies here are motivated by experiments in Fig. S1 (as well as other studies from the Deretic and Stallings labs) suggesting unique autophagy-independent functions for ATG5 in myeloid cells and neutrophils in susceptibility to Mycobacterium tuberculosis infection. However, it is curious that no attempt is made to relate the mechanistic data regarding the retromer or GLUT1 receptor mis-sorting back to the infectious models. Do myeloid cells or neutrophils lacking ATG5 have deficiencies in glucose uptake or GLUT1 cell surface levels? 

Reviewer’s point is well taken. Glucose uptake, its metabolism, and diabetes underly resurgence in TB in certain populations and are important factors in a range of other diseases. This was alluded to in our discussion (lines 461-469). However, these are complex topics for future studies. We will expand this section of the discussion.

Reviewer #3 (Public Review): 

In this manuscript, Padder et al. used APEX2 proximity labeling to find an interaction between ATG5 and the core components of the Retromer complex, VPS26, VPS29, and VPS35. Further studies revealed that ATG5 KO inhibited the trafficking of GLUT1 to the plasma membrane. They also found that other autophagy genes involved in membrane atg8ylation affected GLUT1 sorting. However, knocking out other essential autophagy genes such as ATG13 and FIP200 did not affect GLUT1 sorting. These findings suggest that ATG5 participates in the function of the Retromer in a noncanonical autophagy manner. Overall, the methods and techniques employed by the authors largely support their conclusions. These findings are intriguing and significant, enriching our understanding of the non-autophagic functions of autophagy proteins and the sorting of GLUT1. Nevertheless, there are several issues that the authors need to address to further clarify their conclusions. 

(1) The authors confirmed the interaction between Atg5 and the Retromer complex through Co-IP experiments. Is the interaction between Atg5 and the Retromer direct? If it is direct, which Retromer complex protein regulates the interaction with Atg5? Additionally, does ATG5 K130R mutant enhance its interaction with the Retromer? 

AlphaFold modeling in the initial submission of our study to eLife (absent from the current version) suggested the possibility of a direct interaction between ATG5 and VPS35 with ATG12—ATG5 complex facing outwards, in which case K130R would not matter. However, mutational experiments in putative contact residues did not alter association in co-IPs. So either ATG5 interacts with other retromer subunits or more likely is in a larger protein complex containing retromer. It will take a separate study to dissect associations and find direct interaction partners. We can provide our data on the currently available modeling and mutational analyses in a full point-for-point rebuttal but believe that since they are inconclusive, they should not be included in the study.

(2) To more directly elucidate how ATG5 regulates Retromer function by interacting with the Retromer and participates in the trafficking of GLUT1 to the plasma membrane, the authors should identify which region or crucial amino acid residues of ATG5 regulate its interaction with the Retromer. Additionally, they should test whether mutations in ATG5 that disrupt its interaction with the Retromer affect Retromer function (such as participating in the trafficking of GLUT1 to the plasma membrane) and whether they affect Atg8ylation. They also need to assess whether these mutations influence canonical autophagy and lysosomal sensitivity to damage. 

Please see the response to point 1.

We thank the editors and reviewers for their assessment, constructive criticisms and recommendations.

Author response:

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

Reviewer #1 (Public Review):

We thank the reviewer for his careful reading, which enabled us to improve the quality of this manuscript. We have addressed some major criticisms, and in particular, we have now included the characterization of the impact of BMP2 on other lines as well as the study of the impact of reversion of the H3.3K27M mutation (Figure 3 - figure supplement 1C-D). This control, judiciously proposed by the reviewer, seems more relevant than using mutant H3.1K27M / ACVR1 lines, given the possibility of BMP2 action via other receptors.

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

Reviewer #1

Summary:

Mutational analysis of diffuse midline glioma (DMG) found that ACVR1 mutations, which up-regulate the BMP signaling pathway are found in most H3.1K27M, but not H3.3K27M DMG cases. In this manuscript, Huchede et al attempted to determine whether the BMP signaling pathway has any role in H3.3K27M DMG tumors. They found that the BMP signaling is activated to a similar level in H3.3K27M DMG cells with wild-type ACVR1 compared to ACVR1 DMG cells, likely due to the expression of BMP7 or BMP2. They went on to test whether cells treated with BMP7 or BMP2 treatments affected the gene expression and cell fitness of tumor cells with H3.3K27M mutation. They concluded that BMP2/7 synergizes with H3.3K27M to induce a transcriptomic rewiring associated with a quiescent but invasive cell state. The major issue for this conclusion is that the authors did not use the right models/controls to obtain results to support this conclusion as detailed below. Therefore, in order to strengthen the conclusion, the authors need to address the major concerns below.

Strength:

This paper addresses an important question in the DMG field.

Major concerns/weakness:

(1) All the results in Fig. 2 utilized two glioma lines SF188 and Res259. The authors should repeat all these experiments in a couple of H3.3K27M DMG lines by deleting the H3.3K27M mutation first.

We thank the referee for his/her comments that have helped us to strengthen our conclusions. Although we were rather interested in studying how the BMP pathway can participate in installing a particular cell state at the time of expression of the K27M mutation, we have now included the characterization of the native H3.3K27M BT245 and SU-DIPGXIII cell lines, and their counterparts in which the mutation was reverted by CRISPRCas9 (Harutyunyan et al., 2019). As shown in Figure 3-figure supplement D, the growth arrest induced by BMP2 seems indeed to be specific of the K27M epigenetic context, which could also be required to settle a positive regulation loop to activate the BMP pathway, as mentioned in the Discussion.

(2) Fig. 3. The experiments of BMP2 treatment should be repeated in other H3.3K27M DMG lines using H3.1K27M ACVR1 mutant tumor lines as controls.

The use of mutant ACVR1 lines is interesting, but their control status seems questionable, as the addition of BMPs could have a cumulative effect on the effect of the mutation, notably by activating other receptors in the pathway. But we have now included 3 different cell lines (HSJD-DIPG-014, BT245 and SU-DIPGXIII), and observed similar impact of BMP2 with growth arrest as a readout (Figure 3-figure supplement C-D)

Minor concerns

Fig.2A. BMP2 expression increased in H3.3K27M SF188 cells. Therefore, the statement "whereas BMP2 and BMP4 expressions are not significantly modified (Figure 2A and Figure 2-figure supplement A-B)" is not accurate.

The referee is absolutely right, and we have corrected this statement.

Reviewer #2 (Public Review):

The manuscript by Huchede et al investigates the BMP pathway in H3K27M-mutant gliomas carrying or not activating mutations in ALK2 (ACVR1). Their results in cell lines and in datasets acquired from the literature on patient tumors indicate that the BMP signaling pathway is activated at similar levels between ACVR1 wild-type and mutant tumors. The group further identifies BMP2 and BMP7 as possibly the main activators of the pathway in cells. They then show that BMP2 and 7 crosstalk with the H3 mutation and synergize to induce transcriptomic rewiring leading to an invasive cell state.

The paper is well-written and easy to follow with a robust experimental plan and datasets supporting the claims. While previous work (acknowledged by the authors) indicated activation of BMP in H3K27M tumors, wild type for the ACVR1 mutation this paper is a nice addition and provides further mechanistic cues as to the importance of the BMP pathway and specific members in these deadly brain cancers. The effect of these BMPs in quiescence and invasion is of particular interest.

We thank the referee for his/her supportive comments.

A few suggestions to clarify the message are provided below 1- In thalamic diffuse midline gliomas, the BMP pathway should not be activated as it is in the pons. The authors should identify thalamic tumors in the datasets they explored and patients-derived cell lines from thalamic tumors available to investigate whether this pathway is active across all H3.3K27M mutants in the brain midline or specifically in tumors from the pons.

The inter-patient variability observed in the level of activation of the BMP pathway may indeed be due, at least in part, to different tumor locations. However, we failed to find this information in the publicly available datasets that we used. We however included this element in the Discussion part.

(2) There are ~20% H3.3K27M tumors that carry an ACVR1 mutation and similar numbers of H3.1K27M that are wild type for this gene. Can the authors identify these outliers in their datasets and assess the activation of BMP2 and 7 or other BMP pathway members in this context?

We have now included the outliers present in our datasets in the legends of Figure 1B and Figure 1-figure supplement B and F. From the few samples available to document these outliers in the cohorts that we used, we have not observed major differences regarding the expression levels of BMP2/7 or BMP pathway members and have discussed the fact that it may result from the establishment in all cases of a feedback loop of activation.

In all this is an interesting paper that provides meaningful data to pursue clinical targeting of the BMP pathway, which would be a nice addition to the field.

We thank the reviewer for his/her supportive comments.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The study by Vengayil et al. presented a role for Ubp3 for mediating inorganic phosphate (Pi) compartmentalization in cytosol and mitochondria, which regulates metabolic flux between cytosolic glycolysis and mitochondrial processes. Although the exact function of increased Pi in mitochondria is not investigated, findings have valuable implications for understanding the metabolic interplay between glycolysis and respiration under glucose-rich conditions. They showed that UBP3 KO cells regulated decreased glycolytic flux by reducing the key Pi-dependent-glycolytic enzyme abundances, consequently increasing Pi compartmentalization to mitochondria. Increased mitochondria Pi increases oxygen consumption and mitochondrial membrane potential, indicative of increased oxidative phosphorylation. In conclusion, the authors reported that the Pi utilization by cytosolic glycolytic enzymes is a key process for mitochondrial repression under glucose conditions.

Comments on revised version:

This reviewer appreciates the author's responses addressing some of the concerns.

(1) However, the concern of reproducibility and experimental methods applied to the study is still valid, particularly considering that many conclusions were drawn from western blot analysis. The authors used separate gel loading controls for western blot analysis, which is not a valid method. Considering loading and other errors/discrepancies during the transfer phase of the assay, the direct control should be analyzing the membrane after transfer or using an internal control antibody on the same membrane. None of the western blots are indicated with marker sizes, and it isn't very clear how many repeats there are and whether those repeats are biological or technical repeats.

We thank the reviewer for raising this concern. This point requires detailed clarification regarding two key points: the first one regarding the use of Coomassie stained gels over internal ‘housekeeping gene’ antibodies, and the second one regarding the challenges in performing controls for western blots In case of high abundance proteins such as glycolytic enzymes.

(1) In our western blots, we have used Coomassie stained gel as a loading control for all our western blots. This is performed by cutting one half of the gel and using it for transfer followed by blotting and using the other half for Coomassie staining. I.e. This is not two separate gels that are loaded, but the same gel. Practically, this is no different from cutting a membrane to blot with different antibodies. This method is of course valid method for normalizing western blot data, and is used by multiple studies, for the reasons mentioned below. The historical use of a ‘house-keeping’ gene as a loading control for western blotting assumes that the protein levels of these does not change under different conditions. However, this approach has multiple, severe limitations (since a ‘housekeeping gene’ is entirely contextual, and indeed), and therefore it is correct to use total protein as a loading control. This is indeed recommended for use by multiple studies (Collins et al., 2015). Coomassie staining for total protein is far more reliable than using house-keeping genes as a loading control in western blots (Welinder and Ekblad, 2011). A notable example would be GAPDH itself, which is widely used as a loading control in many studies. As is clear from our data in this manuscript, GAPDH levels itself decrease in ubp3Δ cells. Had we used GAPDH as a loading control, we wouldn’t have identified the decrease in glycolytic enzymes in ubp3Δ cells, and this story would have met with a tragic fate very early on in its inception. We have in fact be very careful with these quantitations, and even before loading samples on gels, they are first normalized using a standard protein estimation assay (Bradford), followed by normalized loading, followed by cutting the gel into two parts - one for coomassie staining and protein normalization, and the other for the western blot for the respective proteins. However, in point (2) below, we clarify on why sometimes we have to load a separate gel with normalized protein, which should resolve this point.

(2) Glycolytic enzymes are highly abundant proteins and to achieve a signal in the linear range of western blot, the protein extracts have to be diluted (up to 25 or 50 times). As discussed under point 1, an internal control ‘housekeeping gene’ antibody is not a reliable method to use as loading control. Even if we want to use an antibody for an internal protein as a control, there are not many proteins that are as abundant as metabolic enzymes and because of this simple reason, the sample dilution results in these proteins not getting detected in the western blot since the signal will be below the limit of detection. This leaves using a separate gel loading control as the only easy to perform, reliable option.

We would like to further highlight the fact that the changes in metabolic enzymes and ETC proteins that we observe in the ubp3 mutant by western blot, were also independently observed by large scale untargeted quantitative proteomics study by  (Isasa et al., 2015), which we cite extensively in this manuscript. Since an entirelyindependent study, using a completely different (untargeted) method has also shown very similar  changes in proteins that we observe (mitochondrial, and glycolytic enzymes), there should be no room for doubt regarding the altered glycolytic enzyme and ETC protein  levels that we discover in this study.

None of the western blots are indicated with marker sizes

We have clearly indicated the marker sizes in all our western blots. Separately, raw images of the blots and Coomassie stained gels have been provided with the manuscript raw data, and is therefore easily available for any interested reader.

It isn't very clear how many repeats there are and whether those repeats are biological or technical repeats.

We have already clearly indicated the details of each blot in the figure legends. For example “A representative blot (out of three biological replicates, n=3) and their quantifications are shown. Data represent mean ± SD.” We kindly request the reviewer to thoroughly go through the figure legends for details regarding the western blots, or any other data. We hope this addresses all the reviewer concerns regarding the credibility of our western blot results and the method of using Coomassie stained gels as loading controls in this study.

(2) Concern regarding citing the Ouyang et al. paper is still valid. This paper is an essential implication in phosphate metabolism and is directly related to some of the findings associated with mitochondrial function, along with conflicting results, which should be discussed in the discussion section. As a reviewer, I do not request citing any paper from the authors in general; however, considering some of the conflicting results here, citing and discussing paper from Ouyang et al. will improve the interoperation/value of their findings.

As mentioned in detail in our previous response  letter, we do not believe that the study from Ouyang et al., present ‘conflicting results’ of any kind. Nevertheless, in response to the reviewer's suggestion, we have revised the discussion section of our manuscript and added a few points that  incorporate the insights from Ouyang et al. These are in the discussion section (“It is important to highlight that our experiments, whether involving Pi supplementation or Pi limitations, maintain the cellular Pi concentration within the millimolar range and are conducted within a short timeframe (~ 1 hour). This differs significantly from Pi starvation studies, where cells are subjected to prolonged and complete Pi deprivation, triggering extensive metabolic adjustments to sustain available Pi pools, such as an increase in mitochondrial membrane potential, independent of respiration”). We trust that this modification will enhance the interested readers' understanding of our study's overarching conclusions.

Reviewer #2 (Public Review):

Summary:

Cells cultured in high glucose tend to repress mitochondrial biogenesis and activity, a prevailing phenotype type called Crabree effect that observed in different cell types and cancer. Many signaling pathways have been put forward to explain this effect. Vengayil et al proposed a new mechanism involved in Ubp3/Ubp10 and phosphate that controls the glucose repression of mitochondria. The central hypothesis is that ∆ubp3 shift the glycolysis to trehalose synthesis, therefore lead to the increase of Pi availability in the cytosol, then mitochondrial received more Pi and therefore the glucose repression is reduced.

Strengths:

The strength is that the authors used an array of different assays to test their hypothesis. Most assays were well designed and controlled.

Weaknesses:

I think the main conclusions are not strongly supported by the current dataset. Here are my comments on authors' response and model.

(1) The authors addressed some of my concerns related to ∆ubp3. But based on the results they observed and discussed, the ∆ubp3 redirect some glycolytic flux to gluconeogenesis while the 0.1% glucose in WT does not. Similarly, the shift of glycolysis to trehalose synthesis is also not relevant to the WT cells cultured in low glucose situation. This should be discussed in the manuscript to make sure readers are not misled to think ∆ubp3 mimic low glucose. It is likely that ∆ubp3 induce proteostasis stress, which is known to activate respiration and trehalose synthesis.

But based on the results they observed and discussed, the ∆ubp3 redirect some glycolytic flux to gluconeogenesis while the 0.1% glucose in WT does not. Similarly, the shift of glycolysis to trehalose synthesis is also not relevant to the WT cells cultured in low glucose situation.

We would like to clarify that we do not observe a redirection of glycolytic flux to gluconeogenesis in ubp3 mutant. What we observe is a rewiring of glycolytic flux into increased trehalose synthesis and PPP, and decreased glycolysis. Also, the shift of glycolysis to trehalose synthesis is relevant to WT cells cultured in low glucose. It is a well-known fact that the trehalose synthesis increases with decrease in media glucose. In case of 0.1% glucose, this increase in trehalose is not due to an increase in gluconeogenesis (since the pathways utilizing alternate carbon sources still remain repressed  in 0.1% glucose (Yin et al., 2003)), but by the increase in glycolytic flux towards trehalose. This is also supported by increase in Tps2 protein levels upon decreasing glucose concentration (Shen et al., 2023). We will also note that there are very few studies that actually estimate gluconeogenic flux in cess (and they only rely on steady state measurements). Estimating gluconeogenic flux appropriately is challenging in itself (eg. see Niphadkar et al 2024). 

In case of glucose concentrations lower than 0.1%, the shift to trehalose synthesis might not be as relevant. We observe that the glycolysis defective mutant tdh2tdh3 cells does not show an increase in trehalose synthesis (Figure 3-figure supplement 1E). However, in this context, the decrease in the rate of GAPDH catalyzed reaction alone appears to be sufficient to increase the Pi levels (Figure 3F) even without an increase in trehalose. Therefore, there might be differences in the relative contributions of these two arms towards Pi balance, based on whether it is low glucose in the environment, or a mutant such as ubp3Δ that modulates glycolytic flux. In ubp3Δ cells, the combination of low rate of GAPDH catalyzed reaction and high trehalose will happen (based on how glycolytic flux is modulated), vs only the low rate of the GAPDH catalyzed reaction in tdh2tdh3 cells. As an end point the increase in Pi happens in both cases, but this happens via slightly differing outcomes. Also note: in terms of free Pi sources a low-glucose condition (with low glycolytic rate) is very different from a no-glucose, respiratory condition (where cells perform very high gluconeogenesis, at a rate that is an order of magnitude higher than in low glucose). In respiration-reliant conditions such as in ethanol, cells switch to high gluconeogenesis, where there is a large increase in trehalose synthesis as a default (eg see Varahan et al 2019). In this condition, trehalose synthesis could become a major source for Pi (eg see Gupta 2021). This could also support the increased mitochondrial respiration. In an ethanol-only medium, the directionality of the GAPDH reaction is itself reversed (i.e. G-1,3-BP → G-3-P). Therefore, this reaction now becomes an added source of Pi, instead of a net consumer of Pi (see illustration in Figure 3G). Therefore, a very reasonable inference is that a combination of increased trehalose and increased 1,3 BPG to G3P conversion can become a Pi source, supporting increased mitochondrial respiration in a non-glucose, respiratory medium.

We have now clarified these points in the discussion section in the updated version of our manuscript. Lines xxx. We hope that this updated discussion section satisfies the reviewer’s concern regarding how relevant the increase in trehalose synthesis is for altered Pi balance and increased mitochondrial respiration in WT cells.

It is likely that ∆ubp3 induce proteostasis stress, which is known to activate respiration and trehalose synthesis.

Apart from some general changes in metabolism, there are no reports whatsoever that suggest that general proteostasis stress can results in an extensive, precise metabolic rewiring - where there is an increased in respiration, mitochondrial de-repression, precise decrease in two limiting glycolytic enzyme levels, and a precise reduction in glycolytic flux, as observed in the ubp3 mutant. If this was the case, deletion of any deubiquitinase should result in an increase in trehalose and respiration which clearly does not happen (as is already clear from the large screen shown in Figure 1)

However, in response to this query, we performed experiments to assess the extent of proteostasis stress in ubp3 mutants. For this, we have now estimated the changes in global ubiquitination in WT vs ubp3 mutant, and compared this with conditions of moderate proteostasis stress (mild heat shock at 42C/~1hr). These data are now included in the revised manuscript as Figure 1- figure supplement 1J. Notably, our analysis reveals only very minor  alteration in global ubiquitination levels in ubp3 mutants compared to WT cells. This is in very stark contrast to  limited heat stress, where a clear increase in global ubiquitination can be easily observed. Given these data, we can conclude that there is no significant general proteostatic stress in ubp3 mutants, that could induce substantial metabolic rewiring of such precise nature.

(2) Pi flux: it is known that vacuole can compensate the reduction of Pi in the cytosol. The paper they cited in the response, especially the Van Heerden et al., 2014 showed that the pulse addition of glucose caused transient Pi reduction and then it came back to normal level after 10min or so. If the authors mean the transient change of glycolysis and respiration, they should point that out clearly in the abstract and introduction. If the authors are trying to put out a general model, then the model must be reconsidered.

In Van Heerden et al., the pulse addition of glucose causes transient Pi reduction due to rapid Pi consumption in glycolysis. The phosphate levels came back to normal level because of the glucose flux into trehalose synthesis releasing free Pi. This is the entire crux of the study and this is the reason why tps2 mutants which cannot synthesize trehalose exhibit a growth defect and have decreased Pi levels. As explained in detail in our early response, the cellular Pi levels are maintained by a relative balance of reactions that consume and release Pi and therefore a change in this balance can change Pi as well. Indeed, if this were not the case, the tps2 mutants would simply maintain the Pi levels similar to WT cells by increasing Pi transport from the medium, which is clearly not the case (eg see Gupta 2021).

The cytosol has ~50mM Pi (van Eunen et al., 2010 FEBSJ), while only 1-2mM of glycolysis metabolites, not sure why partial reduction of several glycolysis enzymes will cause significant changes in cytosolic Pi level and make Pi the limiting factor for mitochondrial respiration. In response to this comment, the authors explained the metabolic flux that the rapid, continuous glycolysis will drain the Pi pool even each glycolytic metabolite is only 1-2mM. However, the metabolic flux both consume and release Pi, that's why there is such measurement of overall free Pi concentration amid the active metabolism. One possibility is that the observed cytosolic Pi level changes was caused by the measurement fluctuation.

The measurement fluctuations that we mentioned in our previous response letter was in case of cells grown in high and low glucose, where there are multiple factors such as mitochondrial amount which complicates the Pi measurements. In case of ubp3 mutants which have a similar amount of total mitochondria as that of WT cells, there is minimal fluctuation for Pi measurement. We have done extensive standardization of mitochondrial isolation and Pi measurement in the isolated mitochondria (as explained in detail in the manuscript) to minimize any such fluctuations. 

However, the metabolic flux both consume and release Pi, that's why there is such measurement of overall free Pi concentration amid the active metabolism

The reviewer is correct in pointing out that metabolic flux consume and release Pi. However, in glucose grown yeast cells, the rate of glycolysis which is a Pi consuming reaction is higher than any other metabolic pathway. In fact, the glycolytic rate in glucose-grown S. cerevisiae is one of the highest ever observed in any living system. A decrease in glycolysis and an increase in trehalose therefore shifts the balance in Pi utilization and results in increased free Pi in ubp3 cells. For a more detailed theoretical reasoning on the consumption and production of Pi, see Gupta 2021.

Importantly, the authors measured Pi inside mito for ethanol and glucose, but not the cytosolic Pi, which is the key hypothesis in their model. The model here is that the glycolysis competes with mito for free cytosolic Pi, so it needs to inhibit glycolysis to free up cytosolic Pi for mitochondrial import to increase respiration. I don't see measurement of cytosolic Pi upon different conditions, only the total Pi or mito Pi. The fact is that in Fig.3C they saw WT+Pi in the medium increase total free Pi more than the ∆ubc3, while WT decrease mito Pi compared to WT control and ∆ubc3 and therefore decrease basal OCR upon Pi supplement. A simple math of Pitotal = Pi cyto + Pi mito tells us that if WT has more Pitotal (Fig.3C) but less Pi mito (fig.5 supp 1C), then it has higher Pi cyto. This is contradictory to what the authors tried to rationalize. Furthermore, as I pointed out previously, the isolated mitochondria can import more Pi when supplemented, so if there is indeed higher Picyto, then the mito in WT should import more Pi. So, to address these contradictory points, the authors must measure Pi in the cytosol, which is a critical experiment not done for their model. For example, they hypothesized that adding 2-DG, or ∆ubp3, suppress glycolysis and thus increase the supply of cytosolic Pi for mito to import, but no cytosolic Pi was measured (need absolute value, not the relative fold changes). It is also important to specific how the experiments are done, was the measurement done shortly after adding 2-DG. Given that the cells response to glucose changes/pulses differently in transient vs stable state, the authors are encouraged to specify that.

(1) Importantly, the authors measured Pi inside mito for ethanol and glucose, but not the cytosolic Pi, which is the key hypothesis in their model. The model here is that the glycolysis competes with mito for free cytosolic Pi, so it needs to inhibit glycolysis to free up cytosolic Pi for mitochondrial import to increase respiration. I don't see measurement of cytosolic Pi upon different conditions, only the total Pi or mito Pi.

As clearly described in the manuscript, the key hypothesis that emerges is the role of the availability/accessibility of Pi for the mitochondria, in the context of activity. As discussed in detail in the discussion section, this can come from a combination of available Pi pools in the cytosol and increased transport of this Pi to the mitochondria. While it is true that the decreased glycolysis in ubp3 mutants frees up available Pi pools in the cytosol, measurement of cytosolic Pi in these mutants growing in log phase might not necessarily show an increased cytosolic Pi, if the Pi is being actively transported the the mitochondria at a rate higher that the WT, as indicated by the ~6 fold increase in mitochondrial Pi in ubp3 cells. This would require tools such as intracellular fluorescence based-Pi sensors that could accurately capture temporal changes in cytosolic and mitochondrial Pi following glycolytic inhibition. However, these tools are not available till date for use in yeast and measuring cytosolic Pi following glycolytic inhibition over time using colorimetric Pi assays are extremely difficult.  

However, the reviewer does correctly state that we had not included measurement of cytosolic Pi. Since the mitochondrial Pi estimate was itself a very challenging (and critical) experiment we had originally thought that data was sufficient. We have therefore now performed a series of new experiments, where we first enrich the cytosolic fraction (without mitochondrial contamination), and estimated cytosolic Pi amounts in WT and ubp3 cells. Our Pi measurements indicate a cytosolic Pi concentration in the range of ~35 mM, which is similar to the earlier reported values in yeast. We further observe that the cytosolic Pi is about ~25% lower in ubp3 mutants (~25-27 mM) compared to WT cells (Figure 4B). As mentioned earlier, this would be consistent with higher transport of Pi from the cytosol to the mitochondria in these cells. Effectively, ubp3 cells have a total increase in cellular Pi, and with a Pi pool distribution such that there is increased Pi availability in mitochondria (Figure 4B). This further substantiates this hypothesis of an increased Pi allocation to mitochondria in ubp3 mutants. The reason for increased rate of Pi transport to mitochondria is not immediately clear, but could also come from changes in cytosolic pH - a possibility that we suggest in our discussion, and is discussed in a later section of this response letter as well.   

(2) The fact is that in Fig.3C they saw WT+Pi in the medium increase total free Pi more than the ∆ubc3, while WT decrease mito Pi compared to WT control and ∆ubc3 and therefore decrease basal OCR upon Pi supplement. A simple math of Pitotal = Pi cyto + Pi mito tells us that if WT has more Pitotal (Fig.3C) but less Pi mito (fig.5 supp 1C), then it has higher Pi cyto. This is contradictory to what the authors tried to rationalize. Furthermore, as I pointed out previously, the isolated mitochondria can import more Pi when supplemented, so if there is indeed higher Picyto, then the mito in WT should import more Pi.

a) “The fact is that in Fig.3C they saw WT+Pi in the medium increase total free Pi more than the ∆ubc3, while WT decrease mito Pi compared to WT control and ∆ubc3 and therefore decrease basal OCR upon Pi supplement. A simple math of Pitotal = Pi cyto + Pi mito tells us that if WT has more Pitotal (Fig.3C) but less Pi mito (fig.5 supp 1C), then it has higher Pi cyto.”

In WT cells supplemented with external Pi (WT+Pi), there is an increased total Pi, but a decreased mitochondrial Pi. As discussed in the discussion section in the manuscript, this could be due to the supplemented Pi not being transported to mitochondria. The reviewer is correct in pointing out that as per simple math this should mean that the cytosolic Pi in WT+Pi should be high. We have now assessed cytosolic Pi upon external Pi supplementation, and this is exactly what we observe in our cytosolic Pi measurements now included in the revised manuscript (Figure 5-figure supplement 5C). There is a higher cytosolic Pi in WT+Pi (~52 mM) compared to WT cells (~35 mM) and ubp3 cells (~27 mM). We have now pointed this out in the discussion section in the revised manuscript “Notably, this increased respiration does not happen upon direct Pi supplementation to highly glycolytic WT cells, where the Pi accumulates in cytosol, without increasing mitochondrial Pi (Figure 5-figure supplement 1C).” We hope that these new data completely addresses the reviewer’s concern regarding the Pi allocations in case of WT+Pi cells.

b) This is contradictory to what the authors tried to rationalize. Furthermore, as I pointed out previously, the isolated mitochondria can import more Pi when supplemented, so if there is indeed higher Picyto, then the mito in WT should import more Pi.

We would like to clarify that the Pi measurements in WT+Pi absolutely do not contradict our hypothesis. Furthermore, nowhere do we claim that an increase in cytosolic Pi will increase mitochondrial Pi!! On the contrary, we explain in detail that supplementing Pi to WT cells (which increases cytosolic Pi) will not increase respiration if the increased Pi is not being transported to mitochondria. This is exactly what happens in WT+Pi, where Pi accumulates in the cytosol but does not result in increased mitochondrial Pi. The reviewer argues that if there is higher cyto Pi, mitochondria should import more Pi. This is true in case of transport via diffusion where the external concentration dictates the direction of metabolite transport, but is fundamentally wrong in case of transport of metabolites where active transporters and additional regulators are involved. This is the entire basis of the idea of metabolic compartmentalisation where  cells maintain pools of metabolites in different organelles which regulate the cellular metabolic state. A well-studied example is pyruvate, whose cytosolic concentration is high in glycolytic cells, but it's transport to mitochondria is reduced in glycolysis to maintain cytosolic fermentation. As discussed in the manuscript, a logical explanation for Pi supplementation not increasing respiration and mitochondria Pi is that there might be mechanisms in highly glycolytic cells that restrict the transport of Pi to mitochondria, thereby compartmentalizing Pi in the cytosol. One such possible mechanism is pH (discussed in a later section) and it is possible that there are other mechanisms involved. 

In case of isolated mitochondria, Pi supplementation results in an increased respiration simply because it is an in vitro set up where we supplement metabolites such as pyruvate, malate and ADP along with phosphate to ensure that mitochondria is actively respiring and in this case Pi will be consumed since it is being used for ATP synthesis. This is entirely different from an in vivo scenario where cells are glycolytic, and mechanisms to prevent mitochondrial transport of metabolites such as pyruvate and phosphate are active. 

c) It is also important to specific how the experiments are done, was the measurement done shortly after adding 2-DG?

Cells were treated with 2-DG for one hour and respiration was measured. We have mentioned these details clearly in the figure legends and methods.  

d) The most likely model to me is that, which is also the consensus in the field, is that no matter 2-DG or ∆ubp3, the cells re-wiring metabolism in both cytosol and mitochondria, and it is the total network shift that cause the mitochondrial respiration increase, which requires the increase of mito import of Pi, ADP, O2, and substrates, but not caused/controlled by the Pi that singled out by the authors in their model.

The aim of our study is only to highlight the importance of mitochondrial Pi availability as a critical factor in controlling mitochondrial respiration. Of course this would require sufficient other factors such as ADP, substrates and oxygen. It cannot be otherwise. However, as we point out in the discussion, a major limiting factor might be Pi availability. While the altered glycolysis in ubp3 mutants might control availability of other factors such as pyruvate and ADP, this is not the focus of our study. We would also like to point out that prior studies show that even though cytosolic ADP decreases in the presence of glucose, this does  not limit mitochondrial ADP uptake, or decrease respiration, due to the very high affinity of the mitochondrial ADP transporter. This is discussed in our discussion section as well. Further we show that the levels of ETC proteins can be altered by changing Pi levels, which places Pi as a major regulator of respiration. We would like to point out once again that studies in other systems have also highlighted a major role of mitochondrial Pi availability in controlling respiration. These references are included in our manuscript (Scheibye-Knudsen et al., 2009, Seifer et al., 2015). This includes a recent study in T cells that clearly shows increased mitochondrial respiration upon overexpressing mitochondrial Pi transporter SLC25A3 alone (Wu et al., 2023). Our manuscript now in fact provides a contextual explanation of these diverse observations from other cellular systems where mitochondrial Pi transport appears to regulate respiration.

(3) The explanation that cytosolic pH reduction upon glucose depletion/2DG is a mistake. There are a lot of data in the literature showing the opposite. If the authors do think this is true, then need to show the data. Again, it is important to distinguish transient vs stable state for pH changes.

We observe that directly supplementing Pi to WT cells growing in high glucose does not result in higher mitochondrial Pi or increased respiration. However, supplementing Pi to WT cells increases mitochondrial respiration in the presence of glycolytic inhibitor 2-DG. We therefore merely suggest that cytosolic pH could be an additional regulator of mitochondrial Pi transport, since this will be consistent with the differences in mitochondrial Pi transport in highly glycolytic cells, and cells with decreased glycolysis ( such as 2-DG addition and ubp3 mutant). This is because in mitochondria, Pi is co-transported along with protons. Therefore, changes in cytosolic pH (which changes the proton gradient) will control the mitochondrial Pi transport (Hamel et al., 2004).  The glycolytic rate is itself a major factor that controls cytosolic pH. The cytosolic pH in highly glycolytic cells is maintained ~7, and decreasing glycolysis results in cytosolic acidification (Orij et al., 2011). Therefore, under conditions of decreased glycolysis (such as loss of Ubp3), cytosolic pH becomes acidic. Since mitochondrial Pi transport depends on the proton gradient, a low cytosolic pH would favour mitochondrial Pi transport. Therefore, under conditions of decreased glycolysis (2DG treatment, or loss of Ubp3), where cytosolic pH would be acidic, increasing cytosolic Pi might indirectly increase mitochondria Pi transport, thereby leading to increased respiration. But we certainly do leave alternate interpretations to the imagination of any reader, and are indeed open to them. These are all exciting future directions this study will enable a contextual interpretation of.

The explanation that cytosolic pH reduction upon glucose depletion/2DG is a mistake.

We have cited two independent studies which suggest that cytosolic pH decreases upon a decrease in glycolysis (Orij et al.,2011 ,Dechant et al., 2010). This control of cytosolic pH by the glycolytic rate has been extensively shown using glycolytic mutants, cells in low glucose and cells grown in the presence of glycolytic inhibitors. According to the reviewer, this is a mistake and

there are a lot of data in the literature showing the opposite.

In our literature review we did not come across any relevant studies that actually show the opposite. If the  reviewer still thinks this is a mistake, the reviewer is welcome to include some of the relevant literature that clearly shows the opposite in the comments, with actual measurements of cytosolic pH. Additionally,  the possible role of cytosolic pH in this context does not affect the conclusions of our study, and we only include this as a possibility in the discussion. Therefore, this is obviously well beyond the scope of experiments in our current study, and considering the extensive data from multiple studies that shows that cytosolic pH decreases under low glycolysis, there is no relevance  to including experiments to address the same in this study. We leave this as a point for an interested reader to think about, and it certainly can nucleate new directions of future study.

Author response:

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

Summary of the changes

Changes in the manuscript were made to clarify some ambiguities raised by the reviewers and to improve the report following their recommendations. A summary of the main changes is listed below:

- The title was changed to better reflect the results of this study - Re-training the model on log transformed FACS scores.

- Testing the specificity of the FEPS to facial expression of pain within this experimental setup by comparing it to the activation maps obtained from the Warm stimulation condition.

- Testing for sensitization/habituation of the behavioral measures (FACS scores and pain ratings).

- Adding a section in the discussion to better address the limitations of this study and provide potential directions for future studies.

Other changes target areas where the original manuscript may have been ambiguous or lacked precision. To address these concerns, additional details have been incorporated, and certain terms have been revised to ensure a more precise and transparent presentation of the information.

Public Reviews:

Reviewer #1 (Public Review):

Picard et al. report a novel neural signature of facial expressions of pain. In other words, they provide evidence that a specific set of brain activations, as measured by means of functional magnetic resonance imaging (fMRI), can tell us when someone is expressing pain via a concerted activation of distinctive facial muscles. They demonstrate that this signature provides a better characterization of this pain behaviour when compared with other signatures of pain reported by past research. The Facial Expression of Pain Signature (FEPS) thus enriches this collection and, if further validated, may allow scientists to identify the neural structures subserving important non-verbal pain behaviour. I have, however, some reservations about the strength of the evidence, relating to insufficient characterization of the underlying processes involved.

We are thankful for the summary of our work. We are hopeful that the modifications made in the latest version effectively address these concerns. The changes are outlined in the summary above, and detailed in the following point-by-point response.

Strengths:

The study relies on a robust machine-learning approach, able to capitalise on the multivariate nature of the fMRI data, an approach pioneered in the field of pain by one of the authors (Dr. Tor Wager). This paper extends Wager's and other colleagues' work attempting to identify specific combinations of brain structures subserving different aspects of the pain experience while examining the extent of similarity/dissimilarity with the other signatures. In doing so, the study provides further methodological insight into fine-grained network characterization that may inspire future work beyond this specific field.

We are thankful for the positive comments.

Weaknesses:

The main weakness concerns the lack of a targeted experimental design aimed to dissect the shared variance explained by activations both specific to facial expressions and to pain reports. In particular, I believe that two elements would have significantly increased the robustness of the findings:

(1) Control conditions for both the facial expressions and the sensory input. An efficient signature should not be predictive of neutral and emotional facial expressions (e.g., disgust) other than pain expressions, as well as it should not be predictive of sensations originating from innocuous warm stimulation or other unpleasant but non-painful stimulation.

We do recognize the lack of specificity testing for the FEPS, especially towards negative emotional facial expressions. This would be relevant to test given the behavioural overlap between the facial expressions of pain and disgust, fear, anger, and sadness (Kunz et al., 2013; Williams, 2003). The experimental design used in this study did not include other negative states. However, we fully support the necessity of collecting data throughout those conditions, and we believe that the present study highlights the importance of such a demonstration. Future research should involve recording facial expressions while exposing participants to stimuli that elicit a range of negative emotions but, to our knowledge, such combination of fMRI and behavioural data is currently unavailable. As raised by the reviewer, this approach would allow us to assess the specificity of the FEPS to the facial expression evoked by pain compared to different affective states. We would like to emphasise that specificity and generalizability testing is a massive amount of work, requiring multiple studies to address comprehensively. A Limitations paragraph addressing this research direction has been added to the Discussion. A conclusion was added to the abstract as follows: “Future studies should explore other pain-relevant manifestations and assess the specificity of the FEPS against other types of aversive or emotional states.”

(2) Graded intensity of the sensory stimulation: different intensities of the thermal stimulation would have caused a graded facial expression (from neutral to pain) and graded verbal reports (from no pain to strong pain), thus offering a sensitive characterisation of the signal associated with this condition (and the warm control condition).

However, these conditions are missing from the current design, and therefore we cannot make a strong conclusion about the generalisability of the signature (regardless of whether it can predict better than other signatures - which may/may not suffer from similar or other methodological issues - another potential interesting scientific question!). The authors seem to work on the assumption that the trials where warm stimulation was delivered are of no use. I beg to disagree. As per my previous comment, warm trials (and associated neutral expressions) could be incorporated into the statistical model to increase the classification sensitivity and precision of the FEPS decoding.

The experience of pain can fluctuate for a fixed intensity or after controlling statistically for the intensity of the stimulation (Woo et al., 2017). Consistent with this, the current study focused on spontaneous facial expression in response to noxious thermal stimuli delivered at a constant intensity that produced moderate to strong pain in every participant. As the reviewer points out, this does not allow us to characterise and compare the stimulus-response function of facial expression and pain ratings. The advantage of the approach adopted is to maximise the number of trials where facial expression is more likely to occur, while ensuring that changes in facial expression and pain ratings are not confounded with changes in stimulus intensity. The manuscript has been revised to clarify that point. However, we do agree that it would be interesting to conduct more studies focusing on facial expression in response to a range of stimulus intensities. This discussion has been added to the Limitations paragraph.

Furthermore, following the reviewer’s suggestion, we performed complementary analyses on the warm trials in the proposed revisions. The dot product (FEPS scores) between the FEPS and the activation maps associated with the warm condition was computed. A linear mixed model was conducted to investigate the association between FEPS scores and the experimental condition (warm vs pain). The trials in the pain condition were divided into two conditions: null FACS scores (painful trials with no facial response; FACS scores = 0) and non-null FACS scores (painful trials with a facial response; FACS > 0). The details of this analysis have been added to the manuscript (see Response of the FEPS to pain and warm section in the Methods; lines 427 to 439) as well as the corresponding results (see Results and Discussion; lines 138 to 158). The FEPS scores were larger in the pain condition where a facial response was expressed, compared to both the pain condition without facial expression and the warm condition. These results confirmed the sensitivity of the FEPS to facial expression of pain.

Reviewer #2 (Public Review):

Summary:

The objective of this study was to further our understanding of the brain mechanisms associated with facial expressions of pain. To achieve this, participants' facial expressions and brain activity were recorded while they received noxious heat stimulation. The authors then used a decoding approach to predict facial expressions from functional magnetic resonance imaging (fMRI) data. They found a distinctive brain signature for pain facial expressions. This signature had minimal overlap with brain signatures reflecting other components of pain phenomenology, such as signatures reflecting subjective pain intensity or negative effects.

We appreciate this concise and accurate summary of our study.

Strength:

The manuscript is clearly written. The authors used a rigorous approach involving multivariate brain decoding to predict the occurrence and intensity of pain facial expressions during noxious heat stimulation. The analyses seem solid and well-conducted. I think that this is an important study of fundamental and clinical relevance.

Weaknesses:

Despite those major strengths, I felt that the authors did not suffciently explain their own interpretation of the significance of the findings. What does it mean, according to them, that the brain signature associated with facial expressions of pain shows a minimal overlap with other pain-related brain signatures?

We express our sincere gratitude for the valuable insights and constructive comments on the strengths and weaknesses of the current study. We thank reviewer 2 for the encouragement to reinforce our interpretation of the significance of the findings, while acknowledging the limitations raised by the three reviewers.

A few questions also arose during my reading.

Question 1: Is the FEPS really specific to pain expressions? Is it possible that the signature includes a facial expression signal that would be shared with facial expressions of other emotions, especially since it involves socio-affective regulation processes? Perhaps this question should be discussed as a limit of the study?

We acknowledge this limitation as outlined in response to Reviewer #1. We have incorporated a Limitations paragraph to provide a more in-depth discussion of this limitation and to explore potential future avenues (lines 225 to 268). Again, please note that the demonstration of specificity is an incremental process that requires a systematic comparison with other conditions where facial expressions are produced without pain. A concluding sentence was added to the abstract to encourage specificity testing in future studies. as indicated above.

Question 2: All AUs are combined together in a composite score for the regression. Given that the authors have other work showing that different AUs may be associated with different components of pain (affective vs. sensory), is it possible that combining all AUs together has decreased the correlation with other pain signatures? Or that the FEPS actually reflects multiple independent signatures?

The question raised is consistent with the work of Kunz, Lautenbacher, LeBlanc and Rainville (2012), and Kunz, Chen and Rainville (2020). In the current study, the pain-relevant action units were combined in order to increase the number of trials where a facial response to pain was expressed, thus enhancing the robustness of our analyses. Given the limited sample size, our current dataset is unfortunately insufficient to perform such analysis as there would not be enough trials to look at the action units separately or in subgroups. While the approach of combining the different AUs has proven to be valid and useful, we recognize the value of investigating potential independent signatures associated with the different AUs within the FEPS, and examining whether those signatures can lead to more similar patterns compared to previously developed pain signatures. This discussion has been included in the Limitations paragraph in the Discussion (lines 225 to 268).

Question 3: Is facial expressivity constant throughout the experiment? Is it possible that the expressivity changes between the beginning and the end of the experiment? For instance, if there is a habituation, or if the participant is less surprised by the pain, or in contrast if they get tired by the end of the experiment and do not inhibit their expression as much as they did at the beginning. If facial expressivity changes, this could perhaps affect the correlation with the pain ratings and/or with the brain signatures; perhaps time (trial number) could be added as one of the variables in the model to address this question.

The concern raised by the reviewer is legitimate. We conducted a mixed-effects model to assess the impact of successive trials and runs on facial expressivity. Results indicate that the FACS scores did not change significantly throughout the experiment, suggesting no notable effect of habituation or sensitization on the facial expressivity in our study. Details about the analysis and the results have been added to the Facial Expression section in the Methods (lines 335 to 346).

Reviewer #3 (Public Review):

In this manuscript, Picard et al. propose a Facial Expression Pain Signature (FEPS) as a distinctive marker of pain processing in the brain. Specifically, they attempt to use functional magnetic resonance imaging (fMRI) data to predict facial expressions associated with painful heat stimulation. The main strengths of the manuscript are that it is built on an extensive foundation of work from the research group, and that experience can be observed in the analysis of fMRI data and the development of the machine learning model. Additionally, it provides a comparative account of the similarities of the FEPS with other proposed pain signatures. The main weaknesses of the manuscript are the absence of a proper control condition to assess the specificity of the facial pain expressions, a few relevant omissions in the methodology regarding the original analysis of the data and its purpose, and a biased interpretation of the results.

I believe that the authors partially succeed in their aims, as described in the introduction, which are to assess the association between pain facial expression and existing pain-relevant brain signatures, and to develop a predictive brain activation model of the facial responses to painful thermal stimulation. However, I believe that there is a clear difference between those aims and the claim of the title, and that the interpretation of the results needs to be more rigorous.

We wish to express our appreciation for the insightful and constructive critique provided. The limitation pertaining to the absence of specificity testing had been addressed in response to Reviewer #1, and it has been incorporated into the manuscript (lines 251 to 258).

The commentary made by Reviewer #3 has drawn our attention to a critical concern, namely the potential misalignment between the study findings and our original title. Consequently, we have changed the title to “A distributed brain response predicting the facial expression of acute nociceptive pain”. We also revised the interpretation of the results in the discussion section and we have added a section on limitations.

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

I hope the following comments will be useful to improve the manuscript.

Abstract

I felt the abstract could be more clear in terms of experimental or scientific questions, hypotheses/expectations, and findings. I also feel the abstract should briefly support the conclusive claim ("is better than...": how better? Or according to what criterion? This may be more relevant than the final conclusive general sentence that does not specifically address the significance of the findings).

The abstract was revised to reinforce the functional perspective adopted to interpret brain activity produced by noxious stimuli and predicting various pain-relevant manifestations. We also mention explicitly the other pain-relevant signatures against which the FEPS is compared in this report, and we added a concluding sentence highlighting the importance of assessing the specificity of the FEPS in future studies.

Introduction - background and rationale

I would postpone the discussion around pain signature and anticipate the one about the brain mechanisms of facial expressions of pain. This will allow you to reinforce the logical flow of rationale, literature gap/question, why the problem is important, and study aims. Only then go for a review of relevant literature on signatures before providing a more specific final paragraph about the study-specific questions, expectations, and implementation. At the moment this is limited to a single very descriptive short paragraph at the end of the intro.

The introduction was structured to guide the readers through a comprehensive understanding of different pain neurosignatures. The introduction aimed to establish a robust rationale for the subsequent analyses detailed in the results section. Indeed, the presentation of that literature ensured that the discussion around pain signatures is contextualised within a broader continuous framework. We acknowledge the reviewer’s comment on the limited description of the brain mechanisms of facial expression of pain. However, this was addressed in several previous reports of our laboratory (Kunz et al. 2011; Vachon-Presseau et al. 2016; Kunz, Chen, and Rainville 2020). We have added some more details about the brain mechanisms of facial expression, and highlighted those references in the first paragraph of the introduction.

Methods and Results

(1) Was there any indication of power based on the previous work or the other signature papers? If yes, how that would inform the present analysis?

The NPS was trained on 20 participants that experienced 12 trials at each of four different intensities. The assessment of the effect sizes was performed on the Neurological Pain Signature in Han et al. (2022). That study revealed a moderate effect size for predicting between-subject pain reports, and a large one for predicting within-subject pain reports. We trained our model on 34 participants that underwent 16 trials. We expected our results to show a smaller effect size as the current experimental design only allowed us to examine spontaneous changes in the facial expression, as noted in the comments made by Reviewer #1. However, the best way to calculate the unbiased effect size of the results presented in the current study would be to test the unchanged model on new independent datasets (see Reddan, Lindquist, and Wager, 2017). Unfortunately, such datasets do not currently exist.

(2) I would clarify to the reader what is meant by normal range of thermal pain and why is this relevant. Also, I did not find data about this assessment nor about the assessment of facial expressiveness (or reference to where it can be found).

We changed this formulation to “All participants included in this study had normal thermal pain sensitivity” and we added a few references. By targeting a healthy population with normal thermal pain sensitivity, our study sought to identify a predictive brain pattern related to facial expression evoked by typical responses to pain that could eventually be generalised to other individuals from the same population. Details about the assessment of facial expressiveness have been added in the appropriate section in the Methods.

(3) That pain ratings are only weakly associated with facial responses is, in its own right, an interesting finding, as a naïve reader would expect the two to be highly positively correlated. I'd suggest discussing this aspect (in reference to previous research) as it is interesting on both theoretical and empirical grounds.

The likelihood and the strength of pain facial expression generally increase with pain ratings in response to acute noxious stimuli of increasing physical intensities, thereby leading to a positive association between the two responses that is driven by the stimulus. However, the poor correlation or the dissociation between facial pain expression and pain rating is a very well known phenomenon that can be demonstrated easily using experimental methods where the stimulus intensity is held constant and spontaneous fluctuations are observed in both facial expression and pain ratings. This result was not discussed in the current manuscript as it was already addressed in the work of Kunz et al. (2011) and Kunz, Karos and Vervoot (2018). We added the references to these studies in the revised manuscript (lines 330 to 334).

(4) It may be worth having CIs throughout the whole set of analyses.

Thanks for the suggestions, this was an oversight. The confidence intervals have been added in the manuscript where applicable.

(5) I would clarify if there are two measures of the brain signature: dot-product and activation map. Relatedly, I cannot find where the authors explained what "FEPS pattern expression scores". Can the authors please clarify?

The clarification has been added in the manuscript (lines 413 to 414).

(6) There seems to be the assumption that the relationship between pain-relevant brain signatures and facial expressions of pain would be parametric and linear. However, this might not hold true. Did the authors test these assumptions?

We indeed decided to use a linear regression technique (i.e. LASSO regression) to model the association between the brain activity and the facial expression of pain. The algorithm choice was mainly based on the simplicity and the interpretability of that approach, and our limited number of observations. The choice was also coherent with previous studies in the domain (e.g. Wager et al., 2011; Wager et al., 2013; Krishnan et al. 2016; Woo et al., 2017). Using a linear model, we were able to predict above chance level the facial expression evoked by pain using the fMRI activation. However, it is legitimate to think that more complex non linear models can better capture the brain patterns predictive of that behavioural manifestation of pain.

(7) Did the authors assess whether the FACS were better to be transformed/normalised? More generally, I would report any data assessment/transformation that has not been reported.

Thank you for this highly relevant suggestion. FACS scores were indeed not normally distributed and the analyses were conducted again to predict the log transformed FACS scores. This transformation was effective to normalize the distribution (skewness = 0.75, kurtosis = -0.84). The predictive model was confirmed on transformed data.

(8) Page 12: I am not clear on whether all the signatures are included in the same model (like a multiple regression) or if separate regressions are calculated per signature. The authors seem to imply that several regressions have been computed (possibly one per comparison with each signature?).

The correlation between the FACS scores and the pain-related signatures was computed separately for each signature. This information has been clarified.

(9) MVPA: See my main comment about warm trials and experimental/statistical design. For example, the LASSO regression model for the pain trials could be compared with a model using warm trials besides (or instead of) the unfitted model. Otherwise, add the warm trials as another predictor or within the subject level in a dummy fixed factor comprising pain and warm trials.

The inclusion of warm trials in the model training would be inconsistent with the goal of the main analysis to predict the facial expression of pain when a noxious pain stimulus is presented. Secondary analyses were conducted to compare the response of the FEPS to the warm trials compared to noxious pain trials. The dot product between the FEPS and the activation maps (FEPS scores) associated with the warm condition was computed. A linear mixed model was conducted to investigate the association between FEPS scores and the experimental condition (warm vs pain). Additional contrasts compared the warm trials with the pain trials with and without pain facial expression. The details of this analysis have been added to the manuscript (see Response of the FEPS to pain and warm in the Methods) as well as the corresponding results (see Results and Discussion).

(10) I would clarify for the reader why the separate M1 analysis has been run. Although obvious, I feel the reader would benefit from the specific hypothesis about this control analysis being spelled out together with the other statistical hypotheses within the statistical design in a more streamlined manner.

We extended the discussion on the rationale of that analysis and its interpretation taking into account the most recent results using the log transformed FACS scores (lines 125 to 133).

(11) The mixed model aimed to assess the relationship between pain ratings FEPS scores and facial scores is a crucial finding. I believe it speaks to the importance of a more complete design, which I already highlighted. I have a couple of technical questions: did the authors assess random slopes too? And, what was the strategy used to determine the random effects structure?

The linear mixed model considered the participants as a random effect, with random intercepts, considering the grouping structure in our data (i.e., each participant completed multiple trials). The reported results in the original manuscript were considering fixed slopes. However, following the reviewer’s comment, we re-computed the mixed linear models allowing the slopes to vary according to the intensity ratings. The results were changed in the manuscript to represent the output of those models.

(12) The text from lines 63 to 67 could go in the methods.

We decided to include those lines within the Result and Discussion section to give the reader more specification about the FACS scores, as this term is subsequently referenced in the following part of the Results and Discussion section. We are concerned that putting this information only in the Methods section would disrupt the reading.

Reviewer #2 (Recommendations For The Authors):

p. 4-5. When you report the positive weight clusters, you follow up with a sentence specifying which cognitive processes those brain regions are typically associated with. However, when you report the negative weight clusters, you do not specify the cognitive processes typically associated with those brain areas. I think that providing that information would be helpful to the readers.

Thanks for noticing this omission. The information has been added in the most recent version of the manuscript (lines 119 to 121).

p. 9. You specify that the degree of expressiveness of participants was evaluated. How did you evaluate expressiveness? Did you use this variable in your analyses? Were participants excluded based on their degree of expressiveness?

Details about the assessment of facial expressiveness have been added in the appropriate section in the Methods (lines 285 to 289).

p. 10. You explain that two certified FACS-coders evaluated the video recordings to rate the frequency of AUs. Could you please provide more details about the frequency measure? I think that there are different ways in which this could have been done. For instance, were the videos decomposed into frames, and then the frequency measured by summing the number of frames in which the AU occurred? Or was it "expression-based", so one occurrence of an AU (frequency of 1) would correspond to the whole period between its activation onset and offset? Both ways have pros and cons. For example, if the frequency represents the number of frames, then it controls for the total duration of the AU activation within a trial (pro); but if there were multiple activations/deactivations of the AU within one trial, this will not be controlled for (con). And vice-versa with the second way of calculating frequency.

Details about the frequency scores have been added to the manuscript (lines 315 to 319).

p. 11. When you explained how you calculated the association between the facial expression of pain and pain-related brain signatures, I felt that there was some information missing. Did you use the thresholded maps (available in the published articles), or did you somehow have access to the complete, voxel-by-voxel, raw regression coefficient maps?

The unthresholded maps were used. The information has been clarified in the latest version of the manuscript, as well as the details about the availability of the maps (see Data Availability section at the end of the manuscript).

Reviewer #3 (Recommendations For The Authors):

Format

The authors will notice that many observations about the manuscript are related to missing information and a lack of graphical representations. I believe the topic and the content of the manuscript are too complex to condense into a short report.

Title

The claim of the title is simply not substantiated by the content of the manuscript. Demonstrating that the FEPS is a distinctive (i.e., specific) marker of pain processing requires a substantially different experimental design, with more rigorous controls and a broader set of painful stimulations. The manuscript would benefit from a more accurate title.

We agree that the title could better align with our findings. We modified the title accordingly : “A distributed brain response predicting the facial expression of acute nociceptive pain”.

Abstract

I find it puzzling that the authors claim that there is limited knowledge of the neural correlates of facial expression of pain given what they describe in the first paragraph of the introduction. Besides, they propose to reanalyze a dataset that has been extensively described in Kunz et al. (2011), which is unlikely to provide any new significant information.

We respectfully disagree with that comment. We considered that three articles (i.e., Kunz et al., 2011; Vachon-presseau et al., 2016; Kunz, Chen and Rainville, 2020) on the topic do constitute limited knowledge, especially if we compare it to the very large body of literature on the neural correlates associated with pain ratings. Except for these three studies, all the other citations pertain to behavioral studies on facial expression of pain, and do not examine the brain activity related to it. Furthermore, we believe that the complementary nature of the analyses performed in Kunz et al. (2011) and in this manuscript offers new insights into our understanding of facial expression in the context of pain. Indeed, the multivariate approach used in this study addresses some limitations present in Kunz et al. (2011) univariate analyses, mainly that it provides a quantifiable way to compare the similarity between different predictive patterns (Reddan and Wager, 2017). We submit that the assessment of the FEPS against several other pain-relevant signatures provides new and important information.

Furthermore, the abstract does not clearly state the aim, and the first line of the results does not match what the authors claim in the preceding line. The take-home message (last sentence) introduces the concept of a biomarker, which, as stated before, cannot be validated with the current data/experimental design. To put it in plain words, a given facial expression (or a composite score derived from a combination of expressions) cannot be a specific biomarker for pain, because a person can always mimic the same expression without feeling pain. Whether a given facial expression can be predicted from brain activity is a different issue, and whether that prediction can differentiate between painful and non-painful origins of the facial expression is another different issue. Unfortunately, neither of those issues can be tested with the current data/experimental design. The abstract would improve if the authors would circumscribe to what they actually tested, which is accurately described in the last sentence of the Introduction.

The abstract was revised accordingly. The term ‘biomarker’ was used in accordance with preceding studies in the field (see Reddan and Wager, 2017; Lee et al., 2021). Please note that we applied the same reasoning to fluctuations in pain expression as previous studies have applied to pain ratings. Of course, we can not dismiss the possibility of someone mimicking facial expressions. Similar reasoning applies to subjective reports, as individuals can intentionally overestimate their pain experience conveyed through verbal reports. This is another case of specificity testing that cannot be addressed in the present study (see new conclusion of the abstract and discussion of limitations). The challenge of pain assessment is a classical problem within both the scientific and the clinical literature. Here, we suggest that the consideration of multiple manifestations of pain is necessary to address this challenge and will provide a more comprehensive portrait of pain-related brain function.

Introduction

I believe that the Introduction would benefit from a strict definition of what is a marker/biomarker/neuromarkers (all those terms are used in the manuscript) and what are its desirable features (validity, reliability, specificity, etc.). I also believe that the Introduction (and the rest of the text) would benefit from a critical assessment of the term "signature". The Introduction describes four existing "signatures", all of them differing in the experimental condition in which acute nociceptive pain is studied, and proposes a fifth one. Keeping with the analogy, I'm wondering whether they should be called (pain) "signatures" if there is a different one for each experimental acute pain condition, and they are so dissimilar between them when they are tested on the same condition (this dataset).

The last part of that comment raises fundamental methodological potential limitations that should be addressed in more depth in another article. That point goes beyond the scope of a research article. Regarding the stability aspect of the signatures, most of the signatures have not been studied extensively. It is thus difficult to currently assess their reliability. However, Han et al. (2022) showed high within-individual test-retest reliability for the NPS across eight different studies. Given that pain is a multidimensional experience, it is not surprising to find different patterns of activation predictive of different aspects or dimensions of the pain experience (see Čeko et al., 2022 for a similar discussion applied to negative affect).

The authors state that "As an automatic behavioral manifestation, pain facial expression might be an indicator of activity in nociceptive systems, perceptual and evaluative processes, or general negative affect." Doesn't it reflect all three of them? (and instead of or?) Why "might"?

The original sentence has been modified as follows: “As an automatic behavioral manifestation, pain facial expression is considered to be an indicator of activity in nociceptive systems, and to reflect perceptual and affective-evaluative processes” (lines 65 to 67).

Methods

The pain scale should be described. Kunz et al. used a 0-100 scale, where 50 was the pain threshold. This is crucial to interpret the 75-80/100 score for the painful thermal intensity.

The description of the pain scale has been added to the manuscript (lines 299 to 300).

Ratings for warm and painful temperatures should be reported (ideally plotted with individual-trial/subject data). In the same line of reasoning, FACS scores should be reported as well (ideally plotted with individual-trial/subject data). It would be interesting to explore the across-trial variability of pain ratings and FACS scores. That is, do people keep giving the same ratings and making the same facial expression after 16 trials? How much variability is between trials and between subjects?

The point raised in that comment was already addressed in response to a comment made by Reviewer #1 (also see the new Figures S2 and S4; see also lines 335 to 346).

How come only painful trials are analyzed? What if the FEPS signature was the same for warm and painful stimulation, thus reflecting the settings (fMRI experiment, stimulation, etc.) rather than the brain response to the stimuli?

The point raised in that comment was already addressed in response to a comment made by Reviewer #1. There was no pain expression in the warm trials and the FEPS shows no response to warm trials. This is now illustrated in the new Figure S4B (see also lines 138 to 158).

The authors propose to predict the trial-by-trial FACS composite score from the pain ratings using a LMM. However, it is interesting that they aim for an almost constant within- and between-subject pain score (75-80/100) as stated in the Methods. This should theoretically render the linear model invalid since its first (and main) assumption would be that FACS should vary linearly with the pain score. Even if patients were not aware that the temperatures were constant across trials, the variation in pain scores should be explained by random noise for a constant stimulation intensity.

Reviewer #3 raises an important point that we need to clarify. Contrary to the expectation that FACS responses should be strongly correlated to pain ratings, we posited that these response channels depend at least in part on separate brain networks that may be differentially sensitive to a variety of modulatory mechanisms (attention, emotion, expectancy, motor priming, social context, etc.). This implies that part of the variance in FACS is independent from pain ratings. We, therefore, consider what Reviewer #3 refers to as random noise to be relevant and meaningful fluctuations reflecting endogenous processes influencing one’s experience of pain and differentially affecting various output responses.

I noticed that fMRI data was analyzed with SPM5 in the original paper (Kunz et al., 2011) and with SPM8 in this manuscript. Was fMRI data re-processed for this manuscript? Were there any differences between the original analysis and this one that might induce changes in the interpretation of results?

The data were indeed re-processed using SPM8, which was the most recent version available when we started the analyses reported here. We used trial-by-trial activation maps for MVPA, which differs from what was used in the previous study (contrast maps at the level of the conditions, not the trials). We have no reason to believe that the different versions will change the message of this manuscript since those versions do not differ significantly in terms of the fMRI preprocessing pipeline (see SPM8 release notes; https://www.fil.ion.ucl.ac.uk/spm/software/spm8/). Furthermore, the aim of this present study is not to compare the different analysis parameters implemented in SPM5 vs SPM8.

What is the rationale for including PVP in the comparison among signatures? The experimental settings in which it was devised are distant from those described here.

The inclusion of the PVP was aimed at enhancing our comparative analysis with the FEPS, as we sought to investigate the potential functional meaning of the FEPS. The PVP was developed to capture the aversive value of pain, a dimension that is conceptually proximal to the interpretation of the facial expression as a manifestation of the affective response to nociceptive pain.

The LASSO-PCR approach is, in my opinion, not a procedure for (brain) decoding in this context. It is accurately described in the section title as a method for multivariate pattern analysis, or as a variable selection and regularization method for a prediction model. Here, brain activity in specific areas related to pain processing can hardly be described as "encoded", and the method just helps select those activations relevant for explaining a certain outcome (in this case, facial expressions).

We understand the point made by reviewer #3. The term brain decoding was changed for multivariate pattern analysis in the latest version of the manuscript.

Details are missing with regards to the dataset split into training, validation, and testing.

Details about the training and testing procedure were added in the manuscript (lines 383 to 385).

This might just be ignorance from me, so I apologize in advance, but what are "contrast" fMRI images? They are mentioned three times in the text but not really described. Are they the "Pain > Warm" contrasts from the original paper?

We apologize for any confusion caused by the use of the term “contrast images” which suggests a direct comparison between two experimental conditions. We have replaced “contrast images” with “activation maps” to provide a more accurate description of the nature of the data used in the multivariate pattern analysis (lines 388 to 389).

In the "Facial expression" section, the authors run an LMM to test the association between pain ratings (response variable) and facial responses (explanatory variable). If I understand correctly, in the "Multivariate pattern analysis" section they test the association between facial composite scores (response variable) and pain ratings (explanatory variable), but they obtain different results.

The analyses were recomputed on the log transformed data, as mentioned previously in the response to reviewers 1-2. The first model (in the “Facial expression” section) used the log transformed FACS scores as a dependent variable, the pain ratings as the fixed effect, and the participants as the random effect. The results of that analysis suggested that the transformed facial expression scores were not significantly associated with the pain ratings (p = .07). The second model uses both the FEPS pattern expression scores and pain ratings as fixed effects to predict facial responses. This analysis showed the significant contribution of the FEPS to the prediction of FACS scores (p < .001) and no significant effect of the pain ratings. However, a significant interaction was found (p = .03) suggesting that the prediction of the pain facial expression by the FEPS may vary with pain ratings (i.e. moderator effect). Those results have been clarified in the “Multivariate pattern analysis” section in the Methods (lines 416 to 426).

In this same section, what are "FEPS pattern expression scores"? They are used three times in the text, but I could not find their description.

The FEPS pattern expression scores correspond to the dot product between the trial-by-trial activation maps and the unthresholded FEPS signature. This information has been added to the manuscript (lines 413 to 414).

It would not be far-fetched to hypothesize that FACS scores could be predicted using solely activity from the motor cortex. The authors attempted to do this, but only with information from M1. Why did they not use the entire motor cortex, or better, regions of the motor cortex directly linked with the AUs described in the manuscript?

The selection of the primary motor area (M1) was based on the results found in Kunz et al. (2011). In this study, M1 showed the strongest correlation with facial expression of pain. There are numerous possibilities of combinations of multiple brain regions considering a variety of criteria based on distributed networks involved in motor, affective, or pain-related processes. We limited our exploration to the region with the strongest hypothesis due to practical feasibility concerns.

Results and Discussion

As a general recommendation, results should present individual data whenever possible. For example, the association between signatures and facial expression should be plotted using scatterplots.

We have added figures showing individual data when it was applicable (Figure S2; Figure S4).

The authors state that the LASSO-PCR model accounts for the facial responses to pain. I believe this is an overstatement, considering:

- A Pearson's r of 0.49 is usually considered low/weak correlation (moderate at best). In the same line, an R2 of 0.17 means that only 17% of the variance is explained by the model.

More nuanced interpretation of the results has been added to the discussion. A section has been added to highlight the limitations of the study.

- Figure 1 needs to display individual subject data and the ideal regression line.

The model was trained using a k-fold cross-validation procedure. The regression lines thus represent the model’s prediction for each one of the 10 folds (i.e. each fold is trained and tested on a different subset of the data). A scatter plot including the ideal regression line computed across all trials and subjects was added in supplementary material to illustrate the relation between the FACS scores and the FEPS pattern expression scores (Figure S4).

- Looking at Figure 1, it is clear that the model has an intercept different from zero. This means that when the FACS score was zero (i.e., volunteers did not make any distinguishable facial expression), the model predicted a score larger than zero. This is not discussed in the manuscript, and in simple terms, it means that there are brain activation patterns when no discernible facial expression is being made by the volunteers. In the original paper by Kunz et al., two groups of subjects were categorized, and one of them was a facially low- or non-expressive group (n=13). This fact is not even mentioned in the manuscript.

The categorization in the previous report (Kunz et al., 2012) was based on a pre-experimental session. All subjects were included in the current analysis. This is now indicated in the Methods (lines 287 to 289).

- On the other end of the range in Figure 1, differences between the FACS scores near the maximum range (40) are underestimated by 23 to 33 points! I guess that the RMSE is smaller (6-7 points), because many FACS scores are concentrated on the low end of the scale.

This is a very interesting comment. A section discussing the limits of the model to predict the lower and higher FACS scores has been added in the manuscript (lines 232 to 250).

It is of course acceptable to interpret the low similarity between signatures as a sign that each signature describes a different mechanism related to pain processing. However, I believe that a complete discussion should contemplate other competing hypotheses. Considering that all signatures were developed using a similar painful thermal stimulation protocol, it is reasonable to expect larger similarities between signatures. The fact that they are so dissimilar could be a reflection of model overfit, i.e., all these signatures are just fitted to these particular experimental protocols and data, and do not generalize to brain mechanisms of pain processing.

We appreciate the pertinent observation. We have included a limitations section in which we discussed, among other considerations, the possible overfitting of models and the necessity of pursuing generalizability studies (lines 225 to 268).

Author response:

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

eLife assessment

This is an important study on the regulation of chlorophyll biosynthesis in rice embryos. It provides insights into the genetic and molecular interactions that underlie chlorophyll accumulation, highlighting the inhibition of OsGLK1 by OsNF-YB7 and the broader implications for understanding chloroplast development and seed maturation in angiosperms. The results presented, including mutation analysis, gene expression profiles, and protein interaction studies, provide convincing evidence for the function of OsNF-YB7 as a repressor in the chlorophyll biosynthesis pathway.

Thank you very much for your positive assessment of our manuscript. We have carefully revised the manuscript according to the reviewers’ valuable suggestions and comments. For more details, please see the point-to-point response to the reviewers below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript investigates the regulation of chlorophyll biosynthesis in rice embryos, focusing on the role of OsNF-YB7. The rigorous experimental approach, combining genetic, biochemical, and molecular analyses, provides a robust foundation for these findings. The research achieves its objectives, offering new insights into chlorophyll biosynthesis regulation, with the results convincingly supporting the authors' conclusions.

Strengths:

The major strengths include the detailed experimental design and the findings regarding OsNF-YB7's inhibitory role.

Weaknesses:

However, the manuscript's discussion on the practical implications for agriculture and the evolutionary analysis of regulatory mechanisms could be expanded.

Thank you for your insightful comments and suggestions. In the revised manuscript, we discussed the potential application of the chlorophyllous embryo (please see line 270-274). The presence of chlorophyll in the embryo facilitates photosynthesis at early developmental stages, potentially leading to improved seedling growth and vigor (Smolikova and Medvedev, 2016). In crops such as soybean and canola, green embryo is considered as a valuable trait due to its association with enhanced photosynthetic capacity, which consequently promotes fatty acid biosynthesis (Ruuska et al., 2004). However, chlorophyll degradation must be carefully managed during seed maturation to avoid negative effects on seed viability and meal quality (Chung et al., 2006). Interestingly, the green embryo of lotus (Nelumbo nucifera) is widely used as a food ingredient in Asian, Australia, and North America. It is employed in herbal medicine to treat nervous disorders, insomnia, and other conditions (Zhu et al., 2017; Ha et al., 2022), highlighting the significant potential value of the green embryo.

In many chloroembryophytes, such as Arabidopsis, the embryo occupies a large proportion of the seed. From an evolutionary perspective, the presence of chlorophyll in the embryo may promote adaptation in such chloroembryophytes because more reserves can be accumulated in the seed through active photosynthesis, better supporting the embryo development and subsequent seedling growth (Sela et al., 2020). On the other hand, some leucoembryophytes, such as rice, have persistent endosperm rich in storage reserves to nourish embryo development (Liu et al., 2022). Gaining the ability to accumulate chlorophyll in the embryo is unnecessary for such species. In agreement with this hypothesis, cholorophyllous embryos are more prevalent in non-endospermous seeds (Dahlgren, 1980). However, we would like to emphasize that the evolutionary force driving the divergence of chloroembryophytes and leucoembryophytes is currently almost completely unknown and deserves in-depth investigation in the future. We discussed the possible evolution of the ability to accumulate chlorophyll in the embryo, please find the details in Line 276-295.

Reviewer #2 (Public Review):

Summary:

The authors set out to establish the role of the rice LEC1 homolog OsNF-YB7 in embryo development, especially as it pertains to the development of photosynthetic capacity, with chlorophyll production as a primary focus.

Strengths:

The results are well-supported and each approach used complements each other. There are no major questions left unanswered and the central hypothesis is addressed in every figure.

Weaknesses:

There are a handful of sections that could use clarifying for readers, but overall this is a solidly composed manuscript.

The authors clearly achieved their aims; the results compellingly establish a disparity between how this system operates in rice and Arabidopsis. Conclusions are thoroughly supported by the provided data and interpretations. This work will force a reconsideration of the value of Arabidopsis as a model organism for embryo chlorophyll biosynthesis and possibly photosynthesis during embryo maturation more broadly, as rice is a major crop organism and it very clearly does not follow the Arabidopsis model. It will thus be useful to carry out similar tests in other organisms rather than relying on Arabidopsis and attempting to more fully establish the regulatory mechanism in rice.

Thank you very much for your positive comments. We have carefully revised the manuscript according to your and the other reviewers’ comments and suggestions. Particularly, we emphasized the necessary to carry out similar tests in other organisms rather than relying on Arabidopsis to better understand the regulatory mechanism in rice.

Reviewer #3 (Public Review):

Summary:

In this study, the authors set out to understand the mechanisms behind chlorophyll biosynthesis in rice, focusing in particular on the role of OsNF-YB7, an ortholog of Arabidopsis LEC1, which is a positive regulator of chlorophyll (Chl) biosynthesis in Arabidopsis. They showed that OsNF-YB7 loss-of-function mutants in rice have chlorophyll-rich embryos, in contrast to Arabidopsis LEC1 loss-of-function mutants. This contrasting phenotype led the authors to carry out extensive molecular studies on OsNF-YB7, including in vitro and in vivo protein interaction studies, gene expression profiling, and protein-DNA interaction assays. The evidence provided well supported the core arguments of the authors, emphasising that OsNF-YB7 is a negative regulator of Chl biosynthesis in rice embryos by mediating the expression of OsGLK1, a transcription factor that regulates downstream Chl biosynthesis genes. In addition, they showed that OsNF-YB7 interacts with OsGLK1 to negatively regulate the expression of OsGLK1, demonstrating the broad involvement of OsNF-YB7 in rice Chl biosynthetic pathways.

Strengths:

This study clearly demonstrated how OsNF-YB7 regulates its downstream pathways using several in vitro and in vivo approaches. For example, gene expression analysis of OsNF-YB7 loss-of-function and gain-of-function mutants revealed the expression of selected downstream chl biosynthetic genes. This was further validated by EMSA on the gel. The authors also confirmed this using luciferase assays in rice protoplasts. These approaches were used again to show how the interaction of OsNF-YB7 and OsGLK1 regulates downstream genes. The main idea of this study is very well supported by the results and data.

Weaknesses:

From an evolutionary perspective, it is interesting to see how two similar genes have come to play opposite roles in Arabidopsis and rice. It would have been more interesting if the authors had carried out a cross-species analysis of AtLEC1 and OsNF-YB7. For example, overexpressing AtLEC1 in an osnf-yb7 mutant to see if the phenotype is restored or enhanced. Such an approach would help us understand how two similar proteins can play opposite roles in the same mechanism within their respective plant species.

We appreciate your insightful comments and suggestions. It is a very interesting question whether AtLEC1 can fully restore osnf-yb7, given the possible functional divergence between the genes in terms of regulation of chlorophyll biosynthesis in the embryo. We have previously expressed OsNF-YB7 in the lec1-1 background in Arabidopsis, driven by the native promoter of LEC1 (Niu et al., 2021). We found that OsNF-YB7 could almost completely rescue the embryo defects in Arabidopsis, indicating that OsNF-YB7 plays a resemble role in rice as the LEC1 does in Arabidopsis (Niu et al., 2021). We sought to determine whether AtLEC1 can complement the chlorophyll defect in osnf-yb7. However, given the fact that osnf-yb7 shows severe callus induction defect, which is not surprising, because many studies have shown that LEC1 is indispensable for somatic embryo development in various plant species, we are struggling to obtain the genetic materials for analysis. We have to transform OsNF-YB7pro::AtLEC1 into the WT background first, and then cross the transformant with the osnf-yb7 mutant. This is a time-consuming process in rice, but hopefully we will able to isolate a line expressing OsNF-YB7pro::AtLEC1 in the osnf-yb7 background from the resulting segregating population.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

A minor comment regarding the chlorophyll contents quantification in the study. Line 87: "The results showed that WT had an achlorophyllous embryo throughout embryonic development,...." In the TEM result, chloroplast was not observed in the WT embryo sections, indicating a lack of chlorophyll-containing structures, contrary to what was found in the osnf-yb7 embryos where chloroplasts were observed.

The authors stated that the embryo morphologies and Chl autofluorescence data showed that WT had an achlorophyllous embryo throughout embryonic development. However, the quantification of Chl levels in Figure 1D and Figure 4C showed that WT does produce some chlorophylls, albeit at lower levels than osnf-yb7 or OSGLK-OX embryos (WT values in the two figures are slightly different). This discrepancy warrants clarification to ensure consistency and accuracy in the manuscript's findings.

We re-evaluated the Chl content in the embryos of WT and OsGLK1-OX mature seeds. The result confirmed our previous finding that WT embryos produce a small amount of chlorophyll (please see the updated Fig. 4C). Notably, we observed that the dark-grown etiolated plants still have measurable chlorophyll content as reported in many studies (for example, Wang et al., 2017; Yoo et al., 2019), suggesting that there is potential bias in measuring chlorophyll content using an absorbance-based approach. We assume this possibly explains the concern you have raised.

Reviewer #2 (Recommendations For The Authors):

Mild editing for grammar is needed throughout, e.g. line 73, "It is still a mysterious why plant species".

We have carefully edited the grammar.

As a minor point, the placement of figure panels, such as in Figure 1, is not always intuitive.

Thank you for your suggestion. This figure has been revised as suggested. Please see the updated Fig. 1.

What is the significance of the two GFP mutants in Figures 2C and 2D? Is one of those the mislabeled Flag mutant?

The lines showed in Fig. 2C and D were not mislabeled. They were two independent transgenic events, both of which showed that OsNF-YB7 inhibited the expression of OsPORA and OsLHCB4 in rice. The transgenic lines overexpressing OsNF-YB7 tagging with the 3× Flag (NF-YB7-Flag) were also used for this experiment. In agreement, OsPORA and OsLHCB4 were significantly downregulated in the three independent NF-YB7-Flag lines (Fig. S4C), confirming the results showed in Fig. 2C and D.

In Figures 2G and 2H, what is that enormous band at the bottom of the gel?

The bands at the bottom of the gel were free probes. We indicated this in the revised figure.

Not until the Materials and Methods section did I realize that any of this study was being done in tobacco; the Introduction implies it's rice vs. Arabidopsis and it might be a good idea to mention the organism of study somewhere before Figure 6.

We apologize for any confusion caused by our previous writing. While the majority of this study was performed with rice plants or protoplasts, the split complementary LUC assays and BiFC assays were performed with tobacco. We have specified these in the revised manuscript as suggested.

Reviewer #3 (Recommendations For The Authors):

It would be nice if the author could show what the phenotype is in AtLEC1 OX in osnf-yb7 and also OsNF-YB7 OX in atlec1 mutants.

Thank you for your suggestion. We have previously expressed OsNF-YB7 in the lec1-1 background of Arabidopsis, driven by the native promoter of Arabidopsis LEC1 (Niu et al., 2021). Since OsNF-YB7 could rescue the embryo morphogenesis defects in Arabidopsis (Niu et al., 2021), we assumed that OsNF-YB7 plays a similar role in rice as the LEC1 does in Arabidopsis. However, it remains unknown whether expression of LEC1 in osnf-yb7 may restore the chlorophyllous embryo phenotype in rice. As the generation of genetic material is time-consuming, and especially given the fact that osnf-yb7 has a severe callus induction defect, we are struggling to obtain the complementary line for analysis. We have to transform OsNF-YB7pro::AtLEC1 in a WT background first, and then cross the transformant with the osnf-yb7 mutant. Hopefully, we will be able to isolate a line expressing OsNF-YB7pro::AtLEC1 in osnf-yb7 background, from the derived segregating population. We discussed the reviewer’s concern in the revised manuscript, please see Line 369-376.

Line 46, I think it is vague to mention that 'Like most plant species'. Some species might have different copy numbers, for example, a single GLK in liverwort M. polymorpha.

The statement has been revised. Please see Line 46.

Figures 2F and 5B, why was only one promoter region used for OsLHCB4? It would be better to have more regions like OsPORA.

Thank you for your comments. Here, we have examined more promoter regions (P1, P2 and P3) in the revised manuscript as suggested, among which, the previously selected promoter region (P3) contains both the G-box and CCAATC motifs that can be potentially recognized by GLK1. Consistent to our previous report, the results showed that OsNF-YB7 (left) and OsGLK1 (right) were associated with the P3 region, but showed no significant differences in the other probes. Please see the results in Fig. 2F and Fig. 5B of the revised manuscript.

Legend of Figures 2G, H, OsPORA (I), and OsLHCB (J) should be (G) and (H) respectively.

Corrected.

References

Chung, D.W., Pruzinska, A., Hortensteiner, S., and Ort, D.R. (2006). The role of pheophorbide a oxygenase expression and activity in the canola green seed problem. Plant Physiol 142, 88-97.

Ha, T., Kim, M.S., Kang, B., Kim, K., Hong, S.S., Kang, T., Woo, J., Han, K., Oh, U., Choi, C.W., and Hong, G.S. (2022). Lotus Seed Green Embryo Extract and a Purified Glycosyloxyflavone Constituent, Narcissoside, Activate TRPV1 Channels in Dorsal Root Ganglion Sensory Neurons. J Agric Food Chem 70, 3969-3978.

Liu, J., Wu, M.W., and Liu, C.M. (2022). Cereal Endosperms: Development and Storage Product Accumulation. Annu Rev Plant Biol 73, 255-291.

Niu, B., Zhang, Z., Zhang, J., Zhou, Y., and Chen, C. (2021). The rice LEC1-like transcription factor OsNF-YB9 interacts with SPK, an endosperm-specific sucrose synthase protein kinase, and functions in seed development. Plant J 106, 1233-1246.

Ruuska, S.A., Schwender, J., and Ohlrogge, J.B. (2004). The capacity of green oilseeds to utilize photosynthesis to drive biosynthetic processes. Plant Physiol 136, 2700-2709.

Sela, A., Piskurewicz, U., Megies, C., Mene-Saffrane, L., Finazzi, G., and Lopez-Molina, L. (2020). Embryonic Photosynthesis Affects Post-Germination Plant Growth. Plant Physiol 182, 2166-2181.

Smolikova, G.N., and Medvedev, S.S. (2016). Photosynthesis in the seeds of chloroembryophytes. Russ J Plant Physl+ 63, 1-12.

Wang, Z., Hong, X., Hu, K., Wang, Y., Wang, X., Du, S., Li, Y., Hu, D., Cheng, K., An, B., and Li, Y. (2017). Impaired Magnesium Protoporphyrin IX Methyltransferase (ChlM) Impedes Chlorophyll Synthesis and Plant Growth in Rice. Front Plant Sci 8, 1694.

Yoo, C.Y., Pasoreck, E.K., Wang, H., Cao, J., Blaha, G.M., Weigel, D., and Chen, M. (2019). Phytochrome activates the plastid-encoded RNA polymerase for chloroplast biogenesis via nucleus-to-plastid signaling. Nat Commun 10, 2629.

Zhu, M., Liu, T., Zhang, C., and Guo, M. (2017). Flavonoids of Lotus (Nelumbo nucifera) Seed Embryos and Their Antioxidant Potential. J Food Sci 82, 1834-1841.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

As a reviewer for this manuscript, I recognize its significant contribution to understanding the immune response to saprophytic Leptospira exposure and its implications for leptospirosis prevention strategies. The study is well-conceived, addressing an innovative hypothesis with potentially high impact. However, to fully realize its contribution to the field, the manuscript would benefit greatly from a more detailed elucidation of immune mechanisms at play, including specific cytokine profiles, antigen specificity of the antibody responses, and long-term immunity. Additionally, expanding on the methodological details, such as immunophenotyping panels, qPCR normalization methods, and the rationale behind animal model choice, would enhance the manuscript's clarity and reproducibility. Implementing functional assays to characterize effector T-cell responses and possibly investigating the microbiota's role could offer novel insights into the protective immunity mechanisms. These revisions would not only bolster the current findings but also provide a more comprehensive understanding of the potential for saprophytic Leptospira exposure in leptospirosis vaccine development. Given these considerations, I believe that after substantial revisions, this manuscript could represent a valuable addition to the literature and potentially inform future research and vaccine strategy development in the field of infectious diseases.

Reviewer #2 (Public Review):

Summary:

The authors try to achieve a method of protection against pathogenic strains using saprophytic species. It is undeniable that the saprophytic species, despite not causing the disease, activates an immune response. However, based on these results, using the saprophytic species does not significantly impact the animal's infection by a virulent species.

Strengths:

Exposure to the saprophytic strain before the virulent strain reduces animal weight loss, reduces tissue kidney damage, and increases cellular response in mice.

Weaknesses:

Even after the challenge with the saprophyte strain, kidney colonization and the release of bacteria through urine continue. Moreover, the authors need to determine the impact on survival if the experiment ends on the 15th.

Reviewer #3 (Public Review):

Summary:

Kundu et al. investigated the effects of pre-exposure to a non-pathogenic Leptospira strain in the prevention of severe disease following subsequent infection by a pathogenic strain. They utilized a single or double exposure method to the non-pathogen prior to challenge with a pathogenic strain. They found that prior exposure to a non-pathogen prevented many of the disease manifestations of the pathogen. Bacteria, however, were able to disseminate, colonize the kidneys, and be shed in the urine. This is an important foundational work to describe a novel method of vaccination against leptospirosis. Numerous studies have attempted to use recombinant proteins to vaccinate against leptospirosis, with limited success. The authors provide a new approach that takes advantage of the homology between a non-pathogen and a pathogen to provide heterologous protection. This will provide a new direction in which we can approach creating vaccines against this re-emerging disease.

Strengths:

The major strength of this paper is that it is one of the first studies utilizing a live non-pathogenic strain of Leptospira to immunize against severe disease associated with leptospirosis. They utilize two independent experiments (a single and double vaccination) to define this strategy. This represents a very interesting and novel approach to vaccine development. This is of clear importance to the field.

The authors use a variety of experiments to show the protection imparted by pre-exposure to the non-pathogen. They look at disease manifestations such as death and weight loss. They define the ability of Leptospira to disseminate and colonize the kidney. They show the effects infection has on kidney architecture and a marker of fibrosis. They also begin to define the immune response in both of these exposure methods. This provides evidence of the numerous advantages this vaccination strategy may have. Thus, this study provides an important foundation for future studies utilizing this method to protect against leptospirosis.

Weaknesses:

Although they provide some evidence of the utility of pretreatment with a non-pathogen, there are some areas in which the paper needs to be clarified and expanded.

The authors draw their conclusions based on the data presented. However, they state the graphs only represent one of two independent experiments. Each experiment utilized 3-4 mice per group. In order to be confident in the conclusions, a power analysis needs to be done to show that there is sufficient power with 3-4 mice per group. In addition, it would be important to show both experiments in one graph which would inherently increase the power by doubling the group size, while also providing evidence that this is a reproducible phenotype between experiments. Overall, this weakens the strength of the conclusions drawn and would require additional statistical analysis or additional replicates to provide confidence in these conclusions.

A direct comparison between single and double exposure to the non-pathogen is not able to be determined. The ages of mice infected were different between the single (8 weeks) and double (10 weeks) exposure methods, thus the phenotypes associated with LIC infection are different at these two ages. The authors state that this is expected, but do not provide a reasoning for this drastic difference in phenotypes. It is therefore difficult to compare the two exposure methods, and thus determine if one approach provides advantages over the other. An experiment directly comparing the two exposure methods while infecting mice at the same age would be of great relevance to and strengthen this work.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major Comments

(1) Elucidation of Immune Mechanisms: The manuscript intriguingly suggests that exposure to saprophytic Leptospira primes the host for a Th1-biased immune response, contributing to survival and mitigation of disease severity upon subsequent pathogenic challenge. However, the underlying mechanisms remain broadly defined. A more detailed investigation into the cytokine profiles, particularly the levels of IFN-γ, IL-12, and other Th1-associated cytokines, could clarify the mechanism of Th1 bias. Moreover, exploring the role of antigen-presenting cells (APCs) in priming T cells towards a Th1 phenotype would add valuable insights.

In this study we continue to elucidate the immune mechanisms engaged by pathogenic and non-pathogenic Leptospira as a follow up to our previous work (Shetty et al, 2021 PMID: 34249775, and Kundu et al 2022 PMID 35392072). We, and others, have shown that saprophytic L. biflexa and pathogenic L. interrogans induce major chemo-cytokines associated with Th1 biased immune responses (Shetty et al. 2021; Cagliero et al. 2022; Krangvichian et al. 2023) and engage myeloid immune cells such as macrophages and dendritic cells. The role of antigen presenting cells such as dendritic cells in priming T cells and activating adaptive response is a separate question and can be addressed in the future. To further address this question, a recent mechanistic study (Krangvichian et al. 2023) showed that non-pathogenic leptospires (L. biflexa) promote MoDC maturation and stimulate the proliferation of IFN-γ-producing CD4+ T cells and potentially elicit a Th1-type response in mice, which also supports our current claim and it is referenced in our manuscript.

(2) Quantitative Analysis of Kidney Colonization: The manuscript reports that pre-exposure to L. biflexa did not prevent the colonization of kidneys by L. interrogans but led to a more regulated immune response and reduced fibrosis. A more nuanced quantification of bacterial loads in the kidneys, using techniques such as CFU counting or more sensitive qPCR methods, could provide a clearer picture of how saprophytic exposure affects the ability of pathogenic Leptospira to establish infection. Additionally, a time-course study showing the kinetics of bacterial colonization and clearance post-infection would be informative.

We are currently validating digital PCR to use in the future and plan to do time course studies.

(3) Characterization of B Cell and T Cell Responses: While the manuscript mentions increased B cell frequencies and effector T helper cell responses, specifics regarding the nature of these responses are lacking. For instance, detailing the isotype and specificity of antibodies produced, the proliferation rates of specific B and T cell subsets, and their functional capabilities (e.g., cytotoxicity, help for B cells) would significantly enrich the understanding of the immune response elicited by pre-exposure to saprophytic Leptospira.

Indeed, additional experiments need to be conducted to flush out the immune responses engaged after pre-exposure to saprophytic Leptospira followed by LIC challenge.

(4) Comparative Analysis with Other Models of Pre-exposure: The study primarily focuses on pre-exposure to a live saprophytic Leptospira. Including a comparison with pre-exposure to killed saprophytic bacteria, or even to other non-pathogenic microbes, could help discern whether the observed protective effect is unique to live saprophytic Leptospira exposure or if it represents a more general phenomenon of trained immunity.

Regarding the use of other non-pathogenic microbes, our lab has shown in the past that oral use of probiotic strain Lactobacillus plantarum (Potula et al 2017) also reduces the severity of Leptospirosis by recruiting myeloid cells. Thus, there may be a general phenomenon of trained immunity involved. We added this to the discussion.

(5) Assessment of Long-term Immunity: The study provides valuable insights into the short-term outcomes following saprophytic Leptospira exposure and subsequent pathogenic challenge. Extending these observations to assess long-term immunity, including memory B and T cell responses several months post-infection, would be crucial for understanding the potential of saprophytic Leptospira exposure in providing lasting protection against leptospirosis.

Long term immunity is a complex and separate question that we plan to address later.

Minor Comments

(1) Technical Specifics of Flow Cytometry Analysis: The manuscript could benefit from including more details on the flow cytometry gating strategy and the specific markers used to identify different immune cell subsets. This addition would aid in the reproducibility of the results and allow for a clearer interpretation of the immune profiling data.

We included the technical specifics of the flow-cytometry analysis in the materials and methods section. The gating strategy (Fig S1) and the specific markers (TableS1) used to identify different immune cell subsets were incorporated in the supplementary datasheet. The cell specific markers were incorporated in the figures (Fig 5 and 6) under each representative cell subset which facilitates clarity and reproducibility of immune profiling.

(2) Statistical Methodology for IgG Subtyping: The analysis of IgG subtypes in response to Leptospira exposure is intriguing but would be strengthened by specifying the statistical tests used to compare IgG1, IgG2a, and IgG3 levels between groups. Additionally, discussing the biological significance of the observed differences in IgG subtype levels would provide a more comprehensive understanding of the immune response.

We applied the ordinary One-way ANOVA test to compare the IgG subtypes between groups followed by a Tukey’s multiple comparison correction analysis (included in the figure legend of Fig 4). We addressed the biological relevance of the observed differences in IgG subtype levels in the discussion section.

(3) Details on Animal Welfare and Ethical Approval: While the manuscript mentions compliance with institutional animal care and use committee protocols, providing the specific ethical guidelines followed, such as the 3Rs (Replacement, Reduction, Refinement), would reinforce the commitment to ethical research practices.

This is addressed in our institutional IACUC which is approved and listed in Methods.

(4) Clarification of Figure Legends: Some figure legends are brief and could be expanded to more thoroughly describe what the figures show, including details on what specific data points, error bars, and statistical symbols represent.

We updated and expanded the figure legends (Fig 1-4).

(5) Revision of Introduction and Background: The introduction provides a good overview of leptospirosis and the rationale behind the study. However, it could be further improved by briefly summarizing current challenges in vaccine development against leptospirosis and how understanding the immune response to saprophytic Leptospira could address these challenges.

We revised the introduction keeping this comment in mind.

Reviewer #2 (Recommendations For The Authors):

- Perform the same challenge experiment with a hamster.

We clarified throughout the manuscript that all the work was done using the C3H-HeJ mouse model which was developed in our lab for the purpose of measuring differences in sublethal and lethal LIC infections. We leave the experiments using hamster to the investigators that have thoroughly validated the hamster model of lethal Leptospira infection.

- Review the written part where it is understood that the challenge with saprophyte strain before virulence prevents the disease.

We reviewed the manuscript to be understood that inoculation of mice with a saprophyte Leptospira before pathogenic challenge prevents severe leptospirosis and promotes kidney homeostasis and increased shedding of Leptospira in urine which is interesting. The last 2 sentences of the abstract read: “Thus, mice exposed to live saprophytic Leptospira before facing a pathogenic serovar may withstand infection with far better outcomes. Furthermore, a status of homeostasis may have been reached after kidney colonization that helps LIC complete its enzootic cycle.”

Reviewer #3 (Recommendations For The Authors):

(1) Line 83: The authors refer to the classification of Leptospira by old nomenclature. The bacteria are now categorized into clades P1, P2, S1 and S2. See Vincent et al. Revisiting the taxonomy and evolution of pathogenicity of the genus Leptospira through the prism of genomics. PLoS Negl Trop Dis. 2019 May 23;13(5):e0007270. doi: 10.1371/journal.pntd.0007270. PMID: 31120895; PMCID: PMC6532842.

We have included the categories (S1 for L. biflexa and P1+ for L. interrogans) in introduction and methods but we did not update the figures because we want to be specific about the species used in these experiments. We also include a few sentences on evolution of Leptospira species in discussion and reference Thibeaux 2018, Vincent 2019 and Giraud-Gatineau, 2024.

(2) Line 133: Please remove the extra line to be consistent with the rest of the method section format.

We addressed all formatting issues.

(3) Line 137: Are these primers specific to pathogenic L. interrogans? Or do they cross react with L. biflexa? If not specific, how long does L. biflexa stick around after infection?

The primers are specific to the genus Leptospira. Surdel et al. in 2022 used 16s rRNA target sequence to amplify L. biflexa Patoc in mice at 6 hours post infection. We did not detect any positive sample for L. biflexa with the 16s rRNA primer set because we do our analysis 30 days and 45 days post inoculation with L. biflexa. We clarified this issue in methods and results.

(4) Statistical analysis:

(a) Some of your graphs have more than 4 points on them (such as Figure 4), while the legend still reads "represents one of two independent experiments". Are these actually combined replicates in the same graph? Combining them would provide strength to your conclusions throughout your manuscript and may provide stronger power for comparisons. If they are not included, why are they not included together? Please clarify what is included in each graph, and why the two experiments were not included together.

We updated the legends with the total number of mice used in the experiment represented in the figure. Figures 1, 2, 4 and S2 contain the combined results from two independent experiments. Figures 3, 5 and 6 represent data from one of two independent experiments. For Fig 3 it would be redundant to show HE images of two experiments. Regarding Figs 5 and 6, the flow-cytometry equipment acquires data at different voltage every single time and biological samples vary between experiments even if all the markers and procedures are the same. So, we reproduce the experiment and show results from one experiment after confirming that the trend between individual experiments are the same.

(b) If ANOVA was used, were all columns compared to each other? Why in some graphs are "ns" labeled only for certain comparisons? I would suggest removing the "ns" comparisons and only highlighting the significant differences.

We have incorporated the comparison analysis between control (PBS) versus the PBS-LIC, LB versus LB-LIC and PBS-LIC versus LB-LIC in both the studies although we have compared significance between all groups.

(5) Line 165: Bacteria were not plated, extract was plated. Perhaps you mean "extract corresponding to 107-108 bacteria"?

We addressed it as follows: “Nunc MaxiSorp flat-bottom 96 well plates (eBioscience, San Diego, CA) were coated with extracts prepared from 107-108 bacteria per well and incubated at 4℃ overnight” …

(6) Line 260: The authors claim that "Exposure to non-pathogenic L. biflexa before pathogenic L. interrogans challenge provided a significant immune cell boost with an increase in overall B and helper T cell frequencies..." However, in Figure 5A, the number of B cells in both the PBS2LIC2 and the LB2LIC2 are not significantly different. Thus, the claim is not supported by the evidence provided. It appears that infection with LIC led to similar increases in B cells regardless of pretreatment.

We rephrased that title to reflect the finding that increased differences were measured in effector Helper T cells between PBS2LIC2 and LB2LIC2 (Figs 5D and 6B, 6C) and we re-wrote this section for clarity.

(7) Lines 314-315: The authors claim that it protected against kidney fibrosis, however, the data only supports that only a single exposure to LB reduced levels of a marker associated with kidney fibrosis. Fibrosis was never directly measured.

Indeed, we didn’t do Mason’s Trichrome stain to get supporting data for kidney fibrosis and only measured a fibrosis marker ColA1. We toned down this section: “ …. it may confer protection against kidney fibrosis.”

(8) Line 317: Authors state that pre-exposure induced higher antibodies in serum, however, this was never shown. Only an increase in IgG2a was shown. Please word this statement to make it clear total antibodies were never measured.

We did measure total anti-Leptospira interrogans IgM and IgG antibodies. We added the following sentence to description of these results: “In both experiments, total IgM and IgG were significantly increased in PBS-LIC and LB-LIC when compared to the respective controls, but not between PBS-LIC and LB-LIC.  Regarding IgG isotypes, IgG1…”

(9) Line 323: The authors state that the exposure "induced antibody responses that provided heterologous protection." There is no evidence that the protection is due to the antibody response in these experiments. In fact, they also showed that it induced increased T cell responses.

We toned down this statement: “In our study, exposure to a saprophytic Leptospira induced antibody responses that may provide heterologous protection against the pathogenic strain of Leptospira.”

(10) Line 328: The authors us the term "stark difference", however, only slight differences are seen.

We toned down that statement as follows:  “Differences in antibody titer among the L. interrogans infected….”

(11) Line 490: reword this sentence to provide clarity and easier to read: "inoculated once with 10^8 L. biflexa at 6 weeks and they were challenged with 10^8 L. interrogans SEROVAR Copenhageni FioCruz (LIC) at 8 weeks."

We revised the sentence.

(12) Figure 1 and 2: Quantifying bacteria in culture after infection is not meaningful, as there are numerous factors that can affect the replication in culture after infection, such as how the organ perhaps was cut before placing it in culture. The comparisons in Figure 2E and F therefore are not interpretable. I would suggest presenting this data as Culture Positive or Culture Negative.

We added these data to the figure under DFM (dark field microscopy).

(13) Figure 3A: H&E staining often leads to different qualities of stains. But is there a better image that can be chosen for the PBS1LIC1 that provides a better comparison with the other images chosen? This is not worth repeating the experiment to get one, just make the figure look better if you have one available.

We screened the images again but the one incorporated in the figure3A for PBS1LIC1 is the best.

(14) Figure 3D: I agree that the PBS-LIC treatment is significant, but please include P value, as it looks very similar to the LB-LIC group. The two LIC groups are not significantly different, so the conclusion would be pre-exposure does not mitigate renal fibrosis marker ColA in the double-exposure study.

We included the p-values in this figure. The two LIC groups are significantly different (ColA1) in the single exposure experiment, and the in double exposure we don’t expect to be able to measure ColA1 differences because the mice are older (10 wk) when we do the LIC challenge.

Author response:

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

Public Reviews.

Reviewer #1 (Public Reviews):

Summary:

The "optorepressilator", an optically controllable genetic oscillator based on the famous E. coli 3-repressor (LacI, TetR, CI) oscillator "repressilator", was developed. An individual repressilator shows a stable oscillation of the protein levels with a relatively long period that extends a few doubling times of E. coli, but when many cells oscillate, their phases tend to desynchronize. The authors introduced an additional optically controllable promoter through a conformal change of CcaS protein and let it control how much additional CI is produced. By tightly controlling the leak from the added promoter, the authors successfully kept the original repressilator oscillation when the added promoter was not activated. In contrast, the oscillation was stopped by expressing the additional CI. Using this system, the authors showed that it is possible to synchronise the phase of the oscillation, especially when the activation happens as a short pulse at the right phase of the repressilator oscillation. The authors further show that, by changing the frequency of the short pulses, the repressilator was entrained to various ratios to the pulse period, and the author could reconstruct the so-called "Arnold tongues", the signature of entrainment of the nonlinear oscillator to externally added periodic perturbation. The behaviour is consistent with the simplified mathematical model that simulates the protein concentration using ordinary differential equations.

Strengths:

Optical control of the oscillation of the protein clock is a powerful and clean tool for studying the synthetic oscillator's response to perturbation in a well-controlled and tunable manner. The article utilizes the plate reader setup for population average measurements and the mother machine setup for single-cell measurements, and they compensate nicely to acquire necessary information.

Weakness:

The current paper added the optogenetically controlled perturbation to control the phase of oscillation and entrainment, but there are a few other works that add external perturbation to a collection of cells that individually oscillate to study phase shift and/or entrainment. The current paper lacks discussion about the pros and cons of the current system compared to previously analyzed systems.

Recommendations

Even if the main purpose of the current paper is to develop a toolbox, it is beneficial to emphasize the pros and cons of the current system compared to the existing work. In addition to the ref [36] that authors cite but do not discuss concretely, example literature about entrainment includes:

- Sanchez, P.G.L., Mochulska, V., Denis,  C.M., Mönke, G., Tomita, T., Tsuchida-Straeten, N., Petersen, Y., Sonnen, K., François, P. and Aulehla, A., 2022. Arnold tongue entrainment reveals dynamical principles of the embryonic segmentation clock. Elife, 11, p.e79575.

- Heltberg M, Kellogg RA, Krishna S, Tay S, Jensen MH. Noise induces hopping between NF-κB entrainment modes. Cell systems. 2016 Dec 21;3(6):532-9.

There is surely more literature. It is recommended that a solid discussion be added on the relation between existing works and current work.

We thank the Reviewer for their positive comments on our manuscript. Their main recommendation is to expand literature and discuss how our method compares to previously reported entrainment of genetic oscillators. In summary, we believe that the main advantages of the optorepressilator are the simplicity of the transcriptional network combined with the flexibility of optical control. In the “Discussion” section of the revised manuscript, we now try to highlight this also in connection to the suggested literature.

Reviewer #2 (Public Reviews):

Summary

In this manuscript by Cannarsa et. al., the authors describe the engineering of a light-entrainable synthetic biological oscillator in bacteria. It is based on an upgraded version of one of the first synthetic circuits to be constructed, the repressilator. The authors sought to make this oscillator entrainable by an external forcing signal, analogous to the way natural biological oscillators (like the circadian clock) are synchronized. They reasoned that an optogenetic system would provide a convenient and flexible means of manipulation. To this end, the authors exploited the CcaS-CcaA light-switchable system, which allows activation and deactivation of transcription by green and red light, respectively. They used this system to make the expression of one of the repressilator's transcription factors (lacI) light-controlled, from a construct separated from the main repressilator plasmid. This way, under red light the oscillator runs freely, but exposure to green light causes overexpression of the lacI, pushing the system into a specific state. Consequently, returning to red light will restore the oscillations from the same phase in all cells, effectively synchronizing the cell population.

After demonstrating the functionality of the basic concept, the authors combined modeling and experiments to show how periodic exposure to green light enables efficient entrainment, and how the frequency of the forcing signal affects the oscillatory behavior (detuning).

This work provides an important demonstration of engineering tunability into a foundational genetic circuit, expands the synthetic biology toolbox, and provides a platform to address critical questions about synchronization in biological oscillators. Due to the flexibility of the experimental system, it is also expected to provide a fertile ground for future testing of theoretical predictions regarding non-linear oscillators.

Strengths:

The study provides a simple and elegant mechanism for the entertainment of a synthetic oscillator. The design relies on optogenetic proteins, which enable efficient experimentation compared to alternative approaches (like using chemical inducers). This way, a static culture (without microfluidics or change of growth media) can be easily exposed to flexible temporal sequences of the zeitgeber, and continuously measured through time.

The study makes use of both plate-reader-based population-level readout and mother-machine single-cell measurements. Synchronization through entrainment is a single cell level phenomenon, but with a clear population-level manifestation. Thus, this experimental approach combination provides a strong validation to their system. At the same time, differences between the readout from the two systems have emerged, and provided a further opportunity for model refinement and testing.

The authors correctly identified the main optimization goal, namely the effective leakiness of their construct even under red light. Then, they successfully overcame this issue using synthetic biology approaches.

The work is supported by a simplified model of the repressilator, which provides a convenient analytical and numerical means to draw testable predictions. The model predictions are well aligned with the experimental evidence.

Weaknesses:

Even after optimizing the expression level of the light-sensitive gene, the system is very sensitive, i.e., a very short exposure is sufficient to elicit the strongest entertainment. This limited dynamic range might hamper some model testing and future usage.

As a result of the previous point, the system is entrained by transiently "breaking" the oscillator: each pulse of green light represents a Hopf bifurcation into a single attractor. it means that the system cannot oscillate in constant green light. In comparison, this is generally not the case for natural zeitgebers like light and temperature for the circadian rhythms. Extreme values might prevent oscillations (not necessarily due to breaking the core oscillator), but usually, free running is possible in a wide range of constant conditions. In some cases, the free-running period length will vary as a function of the constant value. While the approach presented in this manuscript is valid, a comprehensive analysis of more subtle modes of repressilator entrainment could also be of value.

The entire work makes use of a single intensity and single duration of the green pulse to force entrainment. While the model has clear predictions for how those modalities should affect entrainment, none of the experiments attempted to validate those predictions.

While we agree with the Reviewer that all reported experiments were performed with pulses of constant amplitude and duration, we do not see this as a necessary limitation for future studies on the optorepressilator. Using pulse-width modulation, green light intensity could be easily and continuously modulated from zero to a maximum value (as in Fig. 4), exploring a wide range of intermediate intensity levels and therefore of mean LacI production rates from the optogenetic promoter. We do not include additional experiments in the revised manuscript but we have greatly expanded the theoretical discussion on the low amplitude regime, both for a constant illumination (new Supplementary Materials Section 5) and the pulsed case (new Supplementary Fig. 8).

Recommendations for the Authors:

(1) The introduction emphasized the utility of entrainment as a means to achieve population-wide synchrony. It is worth mentioning also that it enables synchronization of the internal oscillator with an external zeitgeber, to achieve a specific phase-locking between them. Often, this is the main utility attributed to entrainment, e.g., in circadian clocks.

Following Reviewer’s suggestion we now say in the introduction:

These oscillations maintain a constant phase relation to the external light cue that can act as a zeitgeber.

(2) It is sometimes unclear at first glance which of the figure panels show simulation data and which show experimental data (e.g., Figure 5a,b; Figure 6a,b). More explicitly labeling the panels could help.

We thank the reviewer for pointing this out, we now explicitly label all the panels.

(3) Figure 3b - please add a color bar to indicate the meaning of the red-green scale, and enlarge the markers so their color is more visible. Also, can add additional controls of (i) sfGFP expression without the ccaR, and (ii) the autofluorescent signal from wild type. Please also provide the raw data (not the time derivatives) in a supplementary figure.

A colorbar has been added and markers enlarged.

(i) Unfortunately we do not have a control for GFP expression without ccaR.

(ii) autofluorescence signal from “a negative control consisting of DHL708 with plasmids pNO286-3 and pSR58-0 (optogenetic plasmids without sfGFP cassette)” has been added for comparison to Fig.3b. This modification was actually very helpful in understanding that the sensitivity threshold in our experiments is mainly determined by autofluorescence. OD600 and fluorescence raw data are now provided in Supplementary Fig. 6.

(4) Figure 3d - the claim in the text is that the purple optorepressilator and the wildtype repressilator have identical periods and amplitude. However, it seems from the figure that there is a small difference in the period length. This deviation is not problematic in any way, but I wondered whether it might actually be explained by the model, assuming that there is still a very weak leak from the new construct. In other words, would the model predict a bifurcation diagram in which an increasing x' concentration causes a gradual decrease in amplitude and increase in period, before the loss of rhythmicity? If so, Figure 3d can serve not only as a technical optimization demonstration but also as a nice validation of the model.

We thank the reviewer for raising this interesting point. We now report, in Supplementary Materials Section 5, a theoretical prediction of the period with respect to a constant concentration of x'. For our choice of parameters (adjusted to reproduce the main experimental quantitative features) we find a period that decreases with x'. Leakage would therefore lead to a shorter period, contrary to what is observed experimentally. To explain the longer period observed in the optorepressilator we went back to extract the average growth rates of bacteria in the purple optorepressilator and repressilator curves in Fig.3d. As we now discuss in the main text:

“The slight difference in period can be explained by the presence of additional plasmids in the optorepressilator strain, which results in a lower growth rate (Supplementary Figures 4 and 5). As found in the digital approximation, the repressilator period is mainly controlled by the inverse growth rate (see Figure 1a and Supplementary Figure 9) meaning a lower growth rate results in a longer oscillation period. When we normalize the time with the growth rate the two oscillations overlap nicely (Supplementary Figure 4).”

(5) Supplementary Figure 10 has no reference from the main text. it is unclear what's the difference from Figure 3. In general, many items in the supplementary materials are not referenced from the text. In addition, on many occasions, there is a reference to "supplementary information" without a specific address, which is not so useful to the reader. In any case possible, please be more specific. Also, note that there's inconsistency in referring to the supplemental section as "supplementary materials" vs "supplemental information".

We now explicitly reference all Supplementary Figures in the main text and use consistent reference to Supplementary Materials.

(6) The discussion at the bottom of p.7 ("Optogenetic entrainment") is missing a reference to the duration and intensity of the zeitgeber: In the example from human circadian rhythms it doesn't indicate light intensity; In the modeling of the PRC, both modalities are absent. it is important at least to indicate the parameters used for the simulation and experiments. It would be even better to explore in the model how these modalities affect the PRC and entrainment. And it would be incredible if the authors could show this also experimentally.

We now report the light intensity values for:

- our experiments:

“We first demonstrate this by monitoring the population signal from CFP (reporting TetR or 𝑦 in the model) in multiwell cultures under constant red illumination (9.82 W/m^2) interrupted by green light pulses (5.64 W/m^2) with a duration of 2 h and period 𝑇 = 18 h.”

For mother machine experiments “Green and red light stimuli were provided by the two LEDs (Thorlabs M530L4, Thorlabs M660L4) with respective intensities 6 W/m^2 and 26 W/m^2 for the synchronization experiments, and 1.1 W/m^2 and 4.5 W/m^2 for the entrainment experiments.”

- and simulations:

“In Fig. 5a we report the phase shift produced by a single pulse (with duration tau=2 h and intensity beta’=80 h-1 fixed for all the simulations) as a function of the pulse arrival phase ϕ.”

We also added an additional supplementary figure (Supplementary Fig. 7) that explores how the duration and intensity of the light pulses affect the PRC in the model. An approximate analytic result is also derived for the PRC in the digital approximation that compares very well with simulation, providing physical insight into PRC shape (Supplementary Materials Section 7).

(7) The experimental validation of the PRC can be much more thorough. Notably, an entrainment experiment with repeated pulses does not provide the same level of validation as a proper PRC experiment. This is because many differently shaped PRCs can give rise to the same entrainment pattern, as long as their fixed-point phases are the same.

Luckily, there might already be a decent amount of data from the mother machine experiments to fit with the PRC prediction, given the authors have pulsed a non-synchronized population that spans the entire x-axis of the PRC. It is possible that a proper PRC experiment wouldn't be too difficult with the plate reader either, given the throughput of the author's system.

This is a very interesting suggestion but unfortunately, in our mother machine data, the first pulse arrives before the cells have completed a full cycle, so although different cells receive the first pulse at a sufficiently randomized phase, we can’t extract their individual phases at the pulse arrival time.

Indeed it would be possible to design a plate reader experiment for the specific purpose of directly measuring the PRC. However, our current protocol involves continuous manual dilutions, which makes it rather laborious. We are currently working on an automated procedure that will allow us to systematically address this and other interesting suggestions in the future.

An indirect experimental validation of the PRC is however still possible using available data. See added red points in Fig.5a and reply to point 10 below.

(8) The discrepancy between the mother machine and plate reader experiments in Figure 5 is explained by a difference in growth rate variability in the two systems. It is not readily obvious how a difference in variability rather than the mean value of the period length can cause a shifted mean phase. It is only hinted in the text that growth rate has two different effects - on the period as well as the amplitude. I hypothesize that because of this period and amplitude correlation, there is a bias contribution to the sum of trajectories that have resulted in a shifted mean phase. Maybe there is another contribution from the asymmetric waveform of the signal? or from the distribution the alpha is sampled from? A direct discussion on that point will make the results much clearer. If the period-amplitude speculation above is right, please add also a panel that shows it. It will also be helpful to show the predicted PRC for the two parameter regimens.

We thank the reviewer for highlighting this point. In the previous version of the manuscript we omitted the fact that in order to better match experimental signals we chose slightly different values for T_L/T_0 for simulations in Fig. 5d and 5e. We now report the values of all simulation parameters in the revised manuscript. This difference could also contribute to the shift in the mean phase for the two cases. We added this information in the main text.

“The bottom panel in Fig. 5d shows the result of a numerical simulation with the same parameters as in Fig. 1b and the addition of a periodic light stimulation, with period $T_L/T_0 = 1$} [...] For the simulations in the lower panel of Fig.5e, all parameters remained the same as in Fig.5d with the exception of the period of the light pulses (T_L/T_0 = 0.97) and the standard deviation of the growth rate distribution, which was increased from 0.034 h^-1 to 0.071 h^-1 to better reproduce the experimental observations in the mother machine.”

Additionally, we added a supplementary figure (Supplementary Fig. 9) demonstrating the correlation between period and amplitude of the oscillations, for simulations with varying growth rate.

(9) The results from the detuning experiments are really nice, especially the decomposition in high frequency shown in Figure 6c. However, the experiments explore only the very high forcing amplitude conditions. Is there any way to test the weaker forcing regimens, as these are expected to uncover the interesting areas in between the Arnold's tongues? If this is experimentally difficult, it would be interesting to include at least the model prediction.

We thank the reviewer for stimulating us to go in this direction. We have performed simulations to explore model predictions for areas between the Arnold’s tongues. We find onset of entrainment as the amplitude increases and also the existence of intermediate plateaus at fractional frequency ratios. These results are now included in the Supplementary Fig. 8.

(10) Another prediction from the Arnold's tongue would be the relative phase of entrainment in different f/v0 conditions. The text refers to it very briefly, but this is a quantitative prediction that can be demonstrated clearly in a figure - how well do they match? It can be shown, for example, by a plot with f/v0 on the x-axis, the phase difference between the pulse and peak expression on the y-axis, a curve representing the model prediction for that function, and dots (with error bars) representing the calculated values from the experimental data.

Generally, when suitable, this kind of direct comparison is more useful to the reader than the way the authors chose to compare simulation and experiments throughout the manuscript.

We thank the reviewer for this very interesting suggestion. We have completely rewritten the discussion on entrainment commenting on how the same PRC (phase shift vs pulse arrival phase) can be interpreted as a T_L/T_0-1 vs phase difference plot. Indeed in the new Fig.5a we plot over the theoretical PRC curve, the values of the relative phase of entrainment for three values of the period of the light pulses (from the data in Fig. 6b). The agreement is remarkably good, providing a further experimental validation of the predicted PRC.

(11) The raw data can be valuable for the community for reanalysis and further hypothesis testing. Hence, it will be very useful to make all of the data (e.g., the fluorescence signal quantification tables from all the experiments) publicly available.

We prepared files with all raw data, to be made available to the community.

Author response:

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

Public Reviews:

Reviewer #1 (Public Reviews):

Summary: 

The authors use a combination of biochemistry and cryo-EM studies to explore a complex between the cap-binding complex and an RNA binding protein, ALYREF, that coordinates mRNA processing and export.

Strengths: 

The biochemistry and structural biology are supported by mutagenesis which tests the model in vitro. The structure provides new insight into how key events in RNA processing and export are likely to be coordinated.

Weaknesses: 

The authors provide biochemical studies to confirm the interactions that they identify; however, they do not perform any studies to test these models in cells or explore the consequences of mRNA export from the nucleus. In fact, several of the amino acids that they identified in ALYREF that are critical for the interaction, as determined by their own biochemical studies, are conserved in budding yeast Yra1 (residues E124/E128 are E/Q in budding yeast and residues Y135/V138/P139 are F/S/P), where the impact on poly(A) RNA export from the nucleus could be readily evaluated. The authors could at least mention this point as part of the implications and the need for future studies. No one seems to have yet targeted any of these conserved residues, so this would be a logical extension of the current work.

We thank the reviewer for the feedback on our work. ALYREF coordinates pre-mRNA processing and export through interactions with a plethora of mRNA biogenesis factors including the DDX39B subunit of the TREX complex, CBC, EJC, and 3’ processing factors. ALYREF mediates the recruitment of the TREX complex on nascent transcripts which depends on its interactions with both CBC and EJC. Our work and studies by others indicate that ALYREF uses overlapping interfaces including both the N-terminal WxHD motif and the RRM domain to bind CBC and EJC. Thus, ALYREF mutants deficient in CBC interaction will also disrupt the ALYREF-EJC interaction and are not ideal for functional studies. In addition, the CBC plays important roles in multiple steps of mRNA metabolism through interactions with a plethora of factors, which often interact competitively with CBC. Identification of separation-of-function mutations on CBC or ALYREF that specifically disrupt their interaction but not other cellular complexes containing CBC or ALYREF would be an important future area to test the model in cells. 

We appreciate the reviewer’s insightful comments regarding yeast Yra1. Thus far, the physical and functional connection between Yra1 and CBC in yeast has not been demonstrated. There are major differences between yeast Yra1 and human ALYREF. Given the lack of an EJC in S. cerevisiae, it is unclear whether Yra1 acts in a similar manner as human ALYREF. In addition, Yra1 does not contain a WxHD motif in its N-terminal unstructured region, which is involved in CBC and EJC interactions in ALYREF. Characterization of the Yra1-CBC interaction will be an interesting future direction. We now include a discussion about yeast Yra1 in the newly added “Conclusion and perspectives” section. 

Specific suggestions:

The authors could put their work in context by speculating how some of the amino acids that they identify as being critical for the interactions they identify could contribute to cancer. For example, they mention mutations of interacting residues in NCBP2 are associated with human cancers, pointing out that NCBP2 R105C amino acid substitution has been reported in colorectal cancer and the NCBP2 I110M mutation has been found in head and neck cancer. Do the authors speculate that these changes would decrease the interaction between NCBP2 and ALYREF and, if so, how would this contribute to cancer? They also mention that a K330N mutation in NCBP1 in human uterine corpus endometrial carcinoma, where Y135 on the α2 helix of mALYREF2 makes a hydrogen bond with K330 of NCBP1. How do they speculate loss of this interaction would contribute to cancer?

In the revised manuscript, we include a discussion about these CBC mutants found in human cancers in the “Conclusion and perspectives” section. We think some of these CBC mutants, such as NCBP-1 K330N, could reduce interaction with ALYREF. Compromised CBC-ALYREF interaction will affect the recruitment of the TREX complex on nascent transcripts and cause dysregulation of mRNA export. In addition, that could also change the partition of CBC and ALYREF in different cellular complexes and cause perturbation of various steps in mRNA biogenesis that are regulated by CBC and ALYREF. Thus far, it is unclear whether and how loss of the CBC-ALYREF interaction directly contributes to cancer. Our work and that of others provide molecular insights to test in future studies. 

Reviewer #2 (Public Reviews):

Summary: 

In this manuscript, Bradley and his colleagues represented the cryo-EM structure of the nuclear cap-binding complex (CBC) in complex with an mRNA export factor, ALYREF, providing a structural basis for understanding CBC regulating gene expression.

Strengths: 

The authors successfully modeled the N-terminal region and the RRM domain of ALYREF (residues 1-183) within the CBC-ALYREF structure, which revealed that both the NCBP1 and NCBP2 subunits of the CBC interact with the RBM domain of ALYREF. Further mutagenesis and pull-down studies provided additional evidence to the observed CBC-ALYREF interface. Additionally, the authors engaged in a comprehensive discussion regarding other cellular complexes containing CBC and/or ALYREF components. They proposed potential models that elucidated coordinated events during mRNA maturation. This study provided good evidence to show how CBC effectively recruits mRNA export factor machinery, enhancing our understanding of CBC regulating gene expression during mRNA transcription, splicing, and export. 

Weaknesses: 

No in vivo or in vitro functional data to validate and support the structural observations and the proposed models in this study. Cryo-EM data processing and structural representation need to be strengthened. 

We appreciate the reviewer’s comments and suggestions. The fact that ALYREF uses highly overlapped binding interfaces for CBC and EJC interactions prevents us from a clear functional dissection of the ALYREF-CBC interaction using in vitro assays or in cells at the current stage. Please also see our response to Reviewer 1. 

In this revised manuscript, we have reprocessed the cryo-EM data using a different strategy which yields significantly improved maps. We have made improvements to the presentation of the structural work based on the reviewer’s specific comments. 

Reviewer #3 (Public Reviews):

Summary: 

The authors carried out structural and biochemical studies to investigate the multiple functions of CBC and ALYREF in RNA metabolism.

Strengths: 

For the structural study part, the authors successfully revealed how NCBP1 and NCBP2 subunits interact with mALYREF (residues 1-155). Their binding interface was then confirmed by biochemical assays (mutagenesis and pull-down assays) presented in this study. 

Weaknesses: 

The authors did not provide functional data to support their proposed models. The authors should include more details regarding the workflow of their cryo-EM data processing in the figure. 

We thank the reviewer for the comments. We completely agree that testing the proposed models in cells would be ideal. However, as we also respond to the other reviewers, functional studies are premature at the current stage because both ALYREF and CBC are components of many cellular complexes that regulate mRNA metabolism. Separation-of-function mutations on CBC or ALYREF first need to be identified in future studies for further investigation. Please also see our response to Reviewer 1. 

As suggested by the reviewer, we have included more details of the cryo-EM workflow in this revised manuscript. We have also included various validation measures including 3DFSC analyses, map vs model FSC curves, and representative density maps at various protein-protein binding interfaces. 

Recommendations for the Authors:

Reviewer #1 (Recommendations for the Authors):

Major points:

The authors should take advantage of Figure 1, which shows the domain structures of NCBP1, NCBP2, and ALYREF to indicate for the reader specifically which protein domains are included in the biochemical and structural analyses. In the current version of the manuscript, there is plenty of space to indicate below each domain structure precisely what regions are included.

In this revised manuscript, we have revised Figure 1A to indicate the protein constructs used in this work. 

Although it is fine to combine the Results and Discussion, the authors should really offer a concluding paragraph to highlight the novel results from this study and put the results in context.

We thank the reviewer for the recommendation. We now include a “Conclusion and perspectives” section in this revised manuscript.  

Minor comments:

Page 5, last sentence (and others) starts a sentence with the word "Since" when likely "As" which does not imply a time element to the phrase, is the correct word.

"Since the ALYREF/mALYREF2 interaction with the CBC is conserved and mALYREF2 exhibits better solubility, we focused on mALYREF2 in the cryo-EM investigations."

Would be more correct as: "As the ALYREF/mALYREF2 interaction with the CBC is conserved and mALYREF2 exhibits better solubility, we focused on mALYREF2 in the cryo-EM investigations."

We thank the reviewer for the comments. We have made the corrections. 

The word 'data' is plural so the sentence at the bottom of p.9 that includes the phrase "...in vivo data shows.." should read "..in vivo data show.." 

Corrected in the revised manuscript.

Reviewer #2 (Recommendations for the Authors):

Major points:

(1) The authors claimed the improved solubility of mouse ALYREF2 (mALYREF2, residues 1-155) compared to the previously employed ALYREF construct. However, human ALYREF has already been purified successfully for pull down assay, indicating soluble human ALYREF obtained, why not use human ALYREF directly? Please clarify. 

Pull-down studies were performed with GST-tagged ALYREF. For cryo-EM studies, untagged ALYREF is preferred to avoid potential issues that may arise from the expression tag. However, untagged ALYREF is less soluble than GST-tagged ALYREF and is not amenable for structural studies. We have revised the text to clarify this point. 

(2) The authors confirmed CBC-ALYREF interfaces through mutagenesis and pull-down assays in vitro. However, it would be more informative and interesting to include functional assays in vitro or/and in vivo with mutagenesis. 

We completely concur with the reviewer that testing the proposed models in vitro and in vivo would be important. However, as we pointed out in our response to public reviews, the highly overlapped binding interfaces on ALYREF for CBC and EJC interactions pose a great challenge for functional studies. Furthermore, both ALYREF and CBC are multifunctional factors and interact with a number of partners. Ideally, separation-of-function mutants that specifically disrupt the CBC-ALYREF interaction but not others need to be identified in future studies in order to perform functional studies. 

(3) About cryo-EM data processing and structural representation:

(1) In the description of the cryo-EM data processing, the authors claimed they did heterogeneous refinement, homogenous refinement, and then local refinement. This reviewer is puzzled by this process because the normal procedure should be non-uniform refinement following homogenous refinement. If the authors did not perform non-uniform refinement, they should do it because it would significantly improve the quality and resolution of cryo-EM maps. In addition, the right local refinement should include mask files and only show the density/map of the local region. 

We thank the reviewer for the suggestions. In response to the reviewer’s comment on the preferred orientation issue (point 5 below), we reprocessed the cryo-EM data and obtained significantly improved cryo-EM maps. In this revised manuscript, the CBC-mALYREF map was refined using homogeneous refinement; the CBC map was refined using homogenous refinement followed by non-uniform refinement. Refinement masks are included in Figure 2-figure supplement1. 

(2) Further local refinements with signal subtraction should be performed to improve the density and resolution of mALYREF2. 

We tested local refinement with or without signal subtraction using masks covering mALYREF2 and various regions of CBC. Unfortunately, this approach did not improve the density of mALYREF2. We suspect that the small size of mALYREF2 (77 residues for the RRM domain) and the intrinsic flexibility of CBC are the limiting factors in these attempts. 

(3) Figures with cryoEM map showing the side chains of the residues on the CBC-mALYREF2 interface should be included to strengthen the claims. Authors could add the map to Figure 3b/c or present it as a supplementary figure.

We include new supplementary figures (Figure 3-figure supplement 1) to show the electron densities corresponding to the views in Figure 3B and 3C. Residues labeled in Figure 3B and 3C are shown in sticks in these supplementary figures.

(4) For cryo-EM date processing, the authors have omitted lots of important details. Could the authors elaborate on the data processing with more details in the corresponding Figure and Methods Sections? Only one abi-initial model from the picked good particles was displayed in the figure. Are there any other different conformations of 3D classes for the dataset? In addition, too few classes have been considered in 3D classification, more classes may give a class with better density and resolution.

We thank the reviewer for the comments. We have reprocessed the cryo-EM data. A major change is to use Topaz for particle picking. We now include more details for data processing in Figure 2-figure supplement 1 and the method section. The cryo-EM sample is relatively uniform. Ab-initio reconstruction and heterogenous refinement yielded only one good class and the other classes are “junk” classes (omitted in the workflow figure). No major conformational changes were observed throughout the multiple rounds of heterogenous refinement for both CBC and CBCmALYREF2. In this revised manuscript, we have been able to obtain significantly improved maps through the new data processing strategy employing Topaz as illustrated in Figure 2-figure supplement 1 to 5.

(5) Angular distribution plots should be included to show if there is a preferred orientation issue. Based on the presented maps in validation reports, there may exist a preferred orientation issue for the reported two cryo-EM maps. Detailed 3D-Histogram and directional FSC plots for all the cryo-EM maps using 3DFSC web server should be presented to show the overall qualities (https://www.nature.com/articles/nmeth.4347 and https://3dfsc.salk.edu/).

We thank the reviewer for the recommendations. In response to the reviewer’s comment on the preferred orientation issue, we reprocessed the cryo-EM data. Topaz was used for particle picking instead of template picking. 3DFSC analyses indicate that the new CBC-mALREF2 map has a sphericity of 0.946, which is a significant improvement from the previous map which has a sphericity of 0.815. Consistently, the maps presented in this revised manuscript show significantly improved densities. We now include angular distribution and 3DFSC analyses of the EM maps (Figure 2-figure supplement 2 and 4). 

(6) Figures of model-to-map FSCs need to be present to demonstrate the quality of the models and the corresponding ones (model resolution when FSC=0.5) should also be included in Table 1. The accuracy of the model is important for structural explanations and description.

The model-to-map FSCs are now included in Figure 2-figure supplement 3A and 5A. The model resolutions of CBC-mALYREF2 and CBC are estimated to be 3.5 Å and 3.6 Å at an FSC of 0.5. These numbers are now included in Table 1. 

(7) In addition, figures of local density maps with different regions of the models, showing side chains, are necessary and important to justify the claimed resolutions. 

We now include density maps overlayed with residue side chains at various regions. For the CBCmALYREF2 map, density maps are shown at the mALYREF2-NCBP1 interfaces (Figure 3-figure supplement 1A and 1B), mALYREF2-NCBP2 interface (Figure 3-figure supplement 1C), NCBP1NCPB2 interface (Figure 2-figure supplement 5B), and the region near m7G (Figure 2-figure supplement 5C). For the CBC map, density maps are shown at the NCBP1-NCPB2 interface (Figure 2-figure supplement 3B) and the region near m7G (Figure 2-figure supplement 3C). 

Minor points:

(1) A figure superimposing the models from the CBC-mALYREF2 amp and mALYREF2 alone map is necessary to present that there are no other CBC binding-induced conformational changes in CBC except the claimed by the authors. In addition, a figure showing the density of m7GpppG should be included as well.  

Overlay of CBC and CBC-mALYREF2 models is now presented in Figure 2-figure supplement 3D. Comparing CBC and CBC-mALYREF2, NCBP1 and NCBP2 have a RMSD of 0.32 Å and 0.30 Å, respectively. The density maps near the M7G cap analog are shown in Figure 2-figure supplement 3C for CBC and Figure 2-figure supplement 5C for CBC-mALYREF2. 

(2) Authors obtained the two maps from one dataset, so "we first determined" and "we next determined" (page 6) should be replaced with something like "One class of 3D cryo-EM map revealed' and "Another class of 3D cryo-EM map defined". 

We have revised the text as suggested by the reviewer.  

(3) In 'Abstract', 'a mRNA export factor' should be 'an mRNA export factor'. 

Corrected in the revised manuscript.

(4) In 'Abstract', the final sentence 'Comparison of CBC- ALYREF to other CBC and ALYREF containing cellular complexes provides insights into the coordinated events during mRNA transcription, splicing, and export' doesn't read smoothly, I would suggest revising it to 'Comparing CBC-ALYREF with other cellular complexes containing CBC and/or ALYREF components provides insight into the coordinated events during mRNA transcription, splicing, and export.' 

We thank the reviewer for the recommendation and have revised accordingly. 

(5) In paragraph 'CBC-ALYREF and viral hijacking of host mRNA export pathway', line 6, the sentences preceding and following the term 'However' indicate a progressive or parallel relationship, rather than a transitional one. To enhance the coherence, I would suggest replacing 'However' with 'Furthermore' or 'In addition'. 

Corrected in the revised manuscript.

(6) In both Figure 5 and Figure 6, the depicted models are proposed and constructed exclusively through the comparison of the CBC-partial ALYREF with other cellular complexes containing components of CBC and/or ALYREF, which need to be confirmed by more studies. To prevent potential confusion and misunderstandings, it is recommended to replace the term 'model' with 'proposed model'. 

Corrected in the revised manuscript.

Reviewer #3 (Recommendations for the Authors):

Major points:

(1) In the Results and Discussion section, the authors mentioned "Recombinant human ALYREF protein was shown to interact with the CBC in RNase-treated nuclear extracts." However, they used mouse ALYREF for cryo-EM investigations. Can the authors include an explanation for this choice during the revision?  

In our work, we used a mixture of glutamic acid and arginine to increase the solubility of GSTALYREF. For cryo-EM studies, we use untagged ALYREF to avoid potential issues that may arise from the expression tag. However, untagged ALYREF is less soluble than GST-tagged ALYREF and is not suitable for structural studies in standard buffers. We have made further clarification on this point in this revised manuscript. 

(2) In the paragraph on "CBC-ALYREF interfaces", the authors stated "For example, E97 forms salt bridges with K330 and K381 of NCBP1. Y135 on the α2 helix of mALYREF2 makes a hydrogen bond with K330 of NCBP1. The importance of this interface between ALYREF and NCBP1 is highlighted by a K330N mutation found in human uterine corpus endometrial carcinoma." I fail to see a strong connection between their structural observations and previous findings regarding the role of a K330N mutation found in human uterine corpus endometrial carcinoma. The authors should add more words to thread these two parts.  

In response to the reviewer’s comment, we now move the discussion of these CBC mutants to the newly added “Conclusion and perspectives” section. 

(3) The authors should include side chains of the residues in their figure of Local resolution estimation and FSC curves, especially when they are presenting the binding interface between two components. 

We have now included density maps that are overlayed with structural models showing side chains of critical residues. These maps include the NCBP1-mALYREF2 interfaces (Figure 3-figure supplement 1A and 1B), NCBP2-mALYREF2 interface (Figure 3-figure supplement 1C), NCBP1NCBP2 interface (Figure 2-figure supplement 3B and 5B), and the m7G cap region (Figure 2figure supplement 3C and 5C). 

Minor points: 

(1) Some grammatical mistakes need to be corrected. For example, it is "an mRNA" instead of "a mRNA".  

Corrected in the revised manuscript.

(2) The authors can provide more information for the audience to know better about ALYREF when it first appears in the 5th line in the Abstract section. For example, "It promotes mRNA export through direct interaction with ALYREF, a key mRNA export factor, ...". 

We have revised the sentence based on the reviewer’s comment.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Some of the data is problematic and does not always support the authors' conclusions:

(1) Fig. 1K and H are identical.

Thank you for pointing out this problem in manuscript. We apologize for this unintentional mistake and have replaced Fig. 1K.

(2) The graph in Figure 2B contradicts the text. It is not obvious how the image was quantified to produce the histological score graph..

We thank the reviewer for pointing out this problem in manuscript, as the reviewer suggested, we have replaced the Figure 2B.

(3) In Figures 2C and D, there is no clear pattern of changes in pro-inflammatory or anti-inflammatory cytokines, despite the authors' claims in the text.

We appreciate the comment, we think the reason is that the level of cytokines in the tissue is low, so the pattern of changes is not obvious.

(4) It is unclear why the anti-dsDNA antibody does not stain the nucleus in Figure 4B. The staining with anti-dsDNA and DAPI does not match well. Figure 5H shows there is still lots of cytosolic DNA in OGT-/- HCF-1-C, measured by DAPI. These data do not support the authors' conclusion that HCFC600 eliminates cytosolic DNA accumulation (line 229). There is no support for the authors' claim that HCF-1 restrains the cGAS-STING pathway (line 330).

We thank these insightful comments, the most critical step in staining cytosolic DNA is to proceed to a low-permeabilization as to allow the antibody to cross the cellular membrane but not the nuclear membrane, that’s why the anti-dsDNA antibody does not stain the nucleus. In Figure 5H, we think we used a high concentrated DAPI to do the staining and nucleus DNA get stained, looks like it’s the cytosolic DNA. 

(5) In Figure 5B, there is no increase in HCF-1 cleavage after OGT over-expression.

We appreciate the reviewer for his/her comment, we think the reason is that we used the cell line to stably overexpress OGT-GFP and we may have missed the time point when the increase in HCF-1 cleavage occurred, so there is no big increase of it. However, there is a significant increase in Figure 5C.

(6) In Figure 7, the TNF-a staining does not inspire confidence.

We thank the reviewer for his/her comment, from both Figure 7K (MC38 tumor model) and Figure 7N (LLC tumor model), we observed a significant increase in TNF-α+ CD8+ T cells in the group treated with the combination of OSMI-1 and anti-PD-L1 compared to the control group, as evidenced by the clear clustering.

The writing needs significant improvement:

(1) There are multiple English grammar mistakes throughout the paper. It is recommended that the authors run the manuscript through an editing service.

We thank the reviewer for his/her suggestion. We apologize for the poor language of our manuscript. We worked on the manuscript for a long time and the repeated addition and removal of sentences and sections obviously led to poor readability. We have now worked on both language and readability and have also involved native English speakers for language corrections. We really hope that the flow and language level have been substantially improved.

(2) Some passages are misleading -- lines 161-162, line 217, lines 241-242, 263-264, 299-300. They need to be changed substantially.

We apologize for these mistakes, we have changed them.

(3) Figure legends should be rewritten. Currently, they are too abbreviated to be understood.

We apologize for that, we have rewritten them.

(4) Discussion should also be thoroughly reworked. Currently, it is merely restating the authors' findings. The authors should put their findings in the broader context of the field.

We apologize for that. For a better understanding of our study, we have reworked the discussion.

Reviewer #2 (Recommendations For The Authors):

(1) Previous studies (DOI: 10.1093/nar/gkw663, 10.1016/j.jgg.2015.07.002, 10.1016/j.dnarep.2022.103394) have suggested that OGT deficiency triggers DNA damage, connecting it to DNA repair and maintenance through various mechanisms. This should be acknowledged in the manuscript. Conversely, the role of HCF1 and its cleaved products in maintaining genomic integrity hasn't been previously shown. The authors investigate HCF1's role solely in the context of OGT inhibition. It is unclear whether this is also true under other stimuli that trigger DNA damage, whether fragments of HCF1 specifically reduce DNA damage, or if HSF1 is involved in the basal machinery that would be defective only in the absence of OGT.

We have acknowledged the manuscript mentioned above. In this paper we focused on the OGT function, which is related to HCF1. The role of HCF1 and its cleaved products in maintaining genomic integrity is an interesting topic, we may focus on it in next project.

(2) In villin-CRE-deficient mice, the authors observe generic inflammation in the intestine unrelated to tumor development. It's unclear if this also occurs in the presence of OGT inhibitors in mice, whether these inhibitors induce a systemic inflammatory (Type I interferon) response, or if certain tissues like the intestine or proliferating tumor cells are more susceptible to such a response.

We thank the comment, yes, investigating whether OGT inhibitors induce an inflammatory response, either systemically or tissue-specifically, is a very interesting project to focus on. However, in our current paper, we use a genetic method to identify the role of OGT deficiency in intestine inflammation-induced tumor development. This approach provides convincing evidence for our hypothesis. We may test the effect of OGT inhibitors on inflammation and tumor development in our next project.

(3) Another critical observation is the magnitude of the interferon response triggered by DNA damage in the OGT-deficient models. While it's known that DNA damage can activate cGAS-STING, the response's extent in the absence of OGT prompts the question of whether additional OGT-specific features could explain this phenomenon. For example, Lamin A, essential for nuclear envelope integrity and shown to be O-glycosylated (DOI: 10.3390/cells7050044), and other components of the nuclear envelope or its repair might be affected by OGT. The impact of OGT inhibition on nuclear envelope integrity compared to other DNA-damaging agents could be explored.

We appreciate the comment, in this project, we find an OGT binding protein, HCF1, though LC–MS/MS assay, it’s a top one candidate in binding profiles, so we focus on it. Like Lamin A and other components of the nuclear envelope still are good targets to check, we may explore these in our next project.

(4) The authors also demonstrate a correlation between OGT expression in tumors compared to healthy tissues. However, the reason is unclear, raising questions about whether this is a consequence of proliferation or metabolic deregulation in the cancer. The authors should address this aspect.

We appreciate the reviewer’s insightful point. It is very good questions and very interesting research. However, in this paper we focused on how OGT influence its downstream molecules to promote tumor, we didn’t check why OGT is increased in tumors, it is not the scope of this current work, we would love to investigate it in the future.

Minor points

Please add the legend to Figures S2, S3 and S5.

We thank the comment, we have added the legend to Figures S2, S3 and S5.

The sentence line 137 should be clarified as OGT deficiency seems more related to increased inflammation in this model.

We thank the comment, we have corrected the sentence line 137.

Line 732 has a ( typo before the number 34.

We thank the comment, we have corrected the sentence line 732.

Author response:

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

eLife assessment

In this important study, the authors manually assessed randomly selected images published in eLife between 2012 and 2020 to determine whether they were accessible for readers with deuteranopia, the most common form of color vision deficiency. They then developed an automated tool designed to classify figures and images as either "friendly" or "unfriendly" for people with deuteranopia. While such a tool could be used by publishers, editors or researchers to monitor accessibility in the research literature, the evidence supporting the tools' utility was incomplete. The tool would benefit from training on an expanded dataset that includes different image and figure types from many journals, and using more rigorous approaches when training the tool and assessing performance. The authors also provide code that readers can download and run to test their own images. This may be of most use for testing the tool, as there are already several free, user-friendly recoloring programs that allow users to see how images would look to a person with different forms of color vision deficiency. Automated classifications are of most use for assessing many images, when the user does not have the time or resources to assess each image individually.

Thank you for this assessment. We have responded to the comments and suggestions in detail below. One minor correction to the above statement: the randomly selected images published in eLife were from articles published between 2012 and 2022 (not 2020).

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors of this study developed a software application, which aims to identify images as either "friendly" or "unfriendly" for readers with deuteranopia, the most common color-vision deficiency. Using previously published algorithms that recolor images to approximate how they would appear to a deuteranope (someone with deuteranopia), authors first manually assessed a set of images from biology-oriented research articles published in eLife between 2012 and 2022. The researchers identified 636 out of 4964 images as difficult to interpret ("unfriendly") for deuteranopes. They claim that there was a decrease in "unfriendly" images over time and that articles from cell-oriented research fields were most likely to contain "unfriendly" images. The researchers used the manually classified images to develop, train, and validate an automated screening tool. They also created a user-friendly web application of the tool, where users can upload images and be informed about the status of each image as "friendly" or "unfriendly" for deuteranopes.

Strengths:

The authors have identified an important accessibility issue in the scientific literature: the use of color combinations that make figures difficult to interpret for people with color-vision deficiency. The metrics proposed and evaluated in the study are a valuable theoretical contribution. The automated screening tool they provide is well-documented, open source, and relatively easy to install and use. It has the potential to provide a useful service to the scientists who want to make their figures more accessible. The data are open and freely accessible, well documented, and a valuable resource for further research. The manuscript is well written, logically structured, and easy to follow.

We thank the reviewer for these comments.

Weaknesses:

(1) The authors themselves acknowledge the limitations that arise from the way they defined what constitutes an "unfriendly" image. There is a missed chance here to have engaged deuteranopes as stakeholders earlier in the experimental design. This would have allowed [them] to determine to what extent spatial separation and labelling of problematic color combinations responds to their needs and whether setting the bar at a simulated severity of 80% is inclusive enough. A slightly lowered barrier is still a barrier to accessibility.

We agree with this point in principle. However, different people experience deuteranopia in different ways, so it would require a large effort to characterize these differences and provide empirical evidence about many individuals' interpretations of problematic images in the "real world." In this study, we aimed to establish a starting point that would emphasize the need for greater accessibility, and we have provided tools to begin accomplishing that. We erred on the side of simulating relatively high severity (but not complete deuteranopia). Thus, our findings and tools should be relevant to some (but not all) people with deuteranopia. Furthermore, as noted in the paper, an advantage of our approach is that "by using simulations, the reviewers were capable of seeing two versions of each image: the original and a simulated version." We believe this step is important in assessing the extent to which deuteranopia could confound image interpretations. Conceivably, this could be done with deuteranopes after recoloration, but it is difficult to know whether deuteranopes would see the recolored images in the same way that non-deuteranopes see the original images. It is also true that images simulating deuteranopia may not perfectly reflect how deuteranopes see those images. It is a tradeoff either way. We have added comments along these lines to the paper.

(2) The use of images from a single journal strongly limits the generalizability of the empirical findings as well as of the automated screening tool itself. Machine-learning algorithms are highly configurable but also notorious for their lack of transparency and for being easily biased by the training data set. A quick and unsystematic test of the web application shows that the classifier works well for electron microscopy images but fails at recognizing red-green scatter plots and even the classical diagnostic images for color-vision deficiency (Ishihara test images) as "unfriendly". A future iteration of the tool should be trained on a wider variety of images from different journals.

Thank you for these comments. We have reviewed an additional 2,000 images, which were randomly selected from PubMed Central. We used our original model to make predictions for those images. The corresponding results are now included in the paper.

We agree that many of the images identified as being "unfriendly" are microscope images, which often use red and green dyes. However, many other image types were identified as unfriendly, including heat maps, line charts, maps, three-dimensional structural representations of proteins, photographs, network diagrams, etc. We have uploaded these figures to our Open Science Framework repository so it's easier for readers to review these examples. We have added a comment along these lines to the paper.

The reviewer mentioned uploading red/green scatter plots and Ishihara test images to our Web application and that it reported they were friendly. Firstly, it depends on the scatter plot. Even though some such plots include green and red, the image's scientific meaning may be clear. Secondly, although the Ishihara images were created as informal tests for humans, these images (and ones similar to them) are not in eLife journal articles (to our knowledge) and thus are not included in our training set. Thus, it is unsurprising that our machine-learning models would not classify such images correctly as unfriendly.

(3) Focusing the statistical analyses on individual images rather than articles (e.g. in figures 1 and 2) leads to pseudoreplication. Multiple images from the same article should not be treated as statistically independent measures, because they are produced by the same authors. A simple alternative is to instead use articles as the unit of analysis and score an article as "unfriendly" when it contains at least one "unfriendly" image. In addition, collapsing the counts of "unfriendly" images to proportions loses important information about the sample size. For example, the current analysis presented in Fig. 1 gives undue weight to the three images from 2012, two of which came from the same article. If we perform a logistic regression on articles coded as "friendly" and "unfriendly" (rather than the reported linear regression on the proportion of "unfriendly" images), there is still evidence for a decrease in the frequency of "unfriendly" eLife articles over time.

Thank you for taking the time to provide these careful insights. We have adjusted these statistical analyses to focus on articles rather than individual images. For Figure 1, we treat an article as "Definitely problematic" if any image in the article was categorized as "Definitely problematic." Additionally, we no longer collapse the counts to proportions, and we use logistic regression to summarize the trend over time. The overall conclusions remain the same.

Another issue concerns the large number of articles (>40%) that are classified as belonging to two subdisciplines, which further compounds the image pseudoreplication. Two alternatives are to either group articles with two subdisciplines into a "multidisciplinary" group or recode them to include both disciplines in the category name.

Thank you for this insight. We have modified Figure 2 so that it puts all articles that have been assigned two subdisciplines into a "Multidisciplinary" category. The overall conclusions remain the same.

(4) The low frequency of "unfriendly" images in the data (under 15%) calls for a different performance measure than the AUROC used by the authors. In such imbalanced classification cases the recommended performance measure is precision-recall area under the curve (PR AUC: https://doi.org/10.1371%2Fjournal.pone.0118432) that gives more weight to the classification of the rare class ("unfriendly" images).

We now calculate the area under the precision-recall curve and provide these numbers (and figures) alongside the AUROC values (and figures). We agree that these numbers are informative; both metrics lead to the same overall conclusions.

Reviewer #2 (Public Review):

Summary:

An analysis of images in the biology literature that are problematic for people with a color-vision deficiency (CVD) is presented, along with a machine learning-based model to identify such images and a web application that uses the model to flag problematic images. Their analysis reveals that about 13% of the images could be problematic for people with CVD and that the frequency of such images decreased over time. Their model yields 0.89 AUC score. It is proposed that their approach could help making biology literature accessible to diverse audiences.

Strengths:

The manuscript focuses on an important yet mostly overlooked problem, and makes contributions both in expanding our understanding of the extent of the problem and in developing solutions to mitigate the problem. The paper is generally well-written and clearly organized. Their CVD simulation combines five different metrics. The dataset has been assessed by two researchers and is likely to be of high-quality. Machine learning algorithm used (convolutional neural network, CNN) is an appropriate choice for the problem. The evaluation of various hyperparameters for the CNN model is extensive.

We thank the reviewer for these comments.

Weaknesses:

The focus seems to be on one type of CVD (deuteranopia) and it is unclear whether this would generalize to other types.

We agree that it would be interesting to perform similar analyses for protanopia and other color-vision deficiencies. But we leave that work for future studies.

The dataset consists of images from eLife articles. While this is a reasonable starting point, whether this can generalize to other biology/biomedical articles is not assessed.

This is an important point. We have reviewed an additional 2,000 images, which were randomly selected from PubMed Central, and used our original model to make predictions for those images. The corresponding results are now included in the paper.

"Probably problematic" and "probably okay" classes are excluded from the analysis and classification, and the effect of this exclusion is not discussed.

We now address this in the Discussion section.

Machine learning aspects can be explained better, in a more standard way.

Thank you. We address this comment in our responses to your comments below.

The evaluation metrics used for validating the machine learning models seem lacking (e.g., precision, recall, F1 are not reported).

We now provide these metrics (in a supplementary file).

The web application is not discussed in any depth.

The paper includes a paragraph about how the Web application works and which technologies we used to create it. We are unsure which additional aspects should be addressed.

Reviewer #3 (Public Review):

Summary:

This work focuses on accessibility of scientific images for individuals with color vision deficiencies, particularly deuteranopia. The research involved an analysis of images from eLife published in 2012-2022. The authors manually reviewed nearly 5,000 images, comparing them with simulated versions representing the perspective of individuals with deuteranopia, and also evaluated several methods to automatically detect such images including training a machine-learning algorithm to do so, which performed the best. The authors found that nearly 13% of the images could be challenging for people with deuteranopia to interpret. There was a trend toward a decrease in problematic images over time, which is encouraging.

Strengths:

The manuscript is well organized and written. It addresses inclusivity and accessibility in scientific communication, and reinforces that there is a problem and that in part technological solutions have potential to assist with this problem.

The number of manually assessed images for evaluation and training an algorithm is, to my knowledge, much larger than any existing survey. This is a valuable open source dataset beyond the work herein.

The sequential steps used to classify articles follow best practices for evaluation and training sets.

We thank the reviewer for these comments.

Weaknesses:

I do not see any major issues with the methods. The authors were transparent with the limitations (the need to rely on simulations instead of what deuteranopes see), only capturing a subset of issues related to color vision deficiency, and the focus on one journal that may not be representative of images in other journals and disciplines.

We thank the reviewer for these comments. Regarding the last point, we have reviewed an additional 2,000 images, which were randomly selected from PubMed Central, and used our original model to make predictions for those images. The corresponding results are now included in the paper.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

N/A

Thank you.

Reviewer #2 (Recommendations For The Authors):

- The web application link can be provided in the Abstract for more visibility.

We have added the URL to the Abstract.

- They focus on deuteranopia in this paper. It seems that protanopia is not considered. Why? What are the challenges in considered this type of CVD?

We agree that it would be interesting to perform similar analyses for protanopia and other color-vision deficiencies. But we leave that work for future studies. Deuteranopia is the most common color-vision deficiency, so we focused on the needs of these individuals as a starting point.

- The dataset is limited to eLife articles. More discussion of this limitation is needed. Couldn't one also include some papers from PMC open access dataset for comparison?

We have reviewed an additional 2,000 images, which we randomly selected from PubMed Central, and used our original model to make predictions for those images. The corresponding results are now included in the paper.

- An analysis of the effect of selecting a severity value of 0.8 can be included.

We agree that this would be interesting, but we leave it for future work.

- "Probably problematic" and "probably okay" classes are excluded from analysis, which may oversimplify the findings and bias the models. It would have been interesting to study these classes as well.

We agree that this would be interesting, but we leave it for future work. However, we have added a comment to the Discussion on this point.

- Some machine learning aspects are discussed in a non-standard way. Class weighting or transfer learning would not typically be considered hyperparameters."corpus" is not a model. Description of how fine-tuning was performed could be clearer.

We have updated this wording to use more appropriate terminology to describe these different "configurations." Additionally, we expanded and clarified our description of fine tuning.

- Reporting performance on the training set is not very meaningful. Although I understand this is cross-validated, it is unclear what is gained by reporting two results. Maybe there should be more discussion of the difference.

We used cross validation to compare different machine-learning models and configurations. Providing performance metrics helps to illustrate how we arrived at the final configurations that we used. We have updated the manuscript to clarify this point.

- True positives, false positives, etc. are described as evaluation metrics. Typically, one would think of these as numbers that are used to calculate evaluation metrics, like precision (PPV), recall (sensitivity), etc. Furthermore, they say they measure precision, recall, precision-recall curves, but I don't see these reported in the manuscript. They should be (especially precision, recall, F1).

We have clarified this wording in the manuscript.

- There are many figures in the supplementary material, but not much interpretation/insights provided. What should we learn from these figures?

We have revised the captions and now provide more explanations about these figures in the manuscript.

- CVD simulations are mentioned (line 312). It is unclear whether these methods could be used for this work and if so, why they were not used. How do the simulations in this work compare to other simulations?

This part of the manuscript refers to recolorization techniques, which attempt to make images more friendly to people with color vision deficiencies. For our paper, we used a form of recolorization that simulates how a deuteranope would see a figure in its original form. Therefore, unless we misunderstand the reviewer's question, these two types of simulation have distinct purposes and thus are not comparable.

- relu -> ReLU

We have corrected this.

Reviewer #3 (Recommendations For The Authors):

The title can be more specific to denote that the survey was done in eLife papers in the years 2012-2022. Similarly, this should be clear in the abstract instead of only "images published in biology-oriented research articles".

Thank you for this suggestion. Because we have expanded this work to include images from PubMed Central papers, we believe the title is acceptable as it stands. We updated the abstract to say, "images published in biology- and medicine-oriented research articles"

Two mentions of existing work that I did not see are to Jambor and colleagues' assessment on color accessibility in several fields: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8041175/, and whether this work overlaps with the 'JetFighter' tool

(https://elifesciences.org/labs/c2292989/jetfighter-towards-figure-accuracy-and-accessibility).

Thank you for bringing these to our attention. We have added a citation to Jambor, et al.

We also mention JetFighter and describe its uses.

Similarly, on Line 301: Significant prior work has been done to address and improve accessibility for individuals with CVD. This work can be generally categorized into three types of studies: simulation methods, recolorization methods, and estimating the frequency of accessible images.

- One might mention education as prior work as well, which might in part be contributing to a decrease in problematic images (e.g., https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8041175/)

We now suggest that there are four categories and include education as one of these.

Line 361, when discussing resources to make figures suitable, the authors may consider citing this paper about an R package for single-cell data: https://elifesciences.org/articles/82128

Thank you. We now cite this paper.

The web application is a good demonstration of how this can be applied, and all code is open so others can apply the CNN in their own uses cases. Still, by itself, it is tedious to upload individual image files to screen them. Future work can implement this into a workflow more typical to researchers, but I understand that this will take additional resources beyond the scope of this project. The demonstration that these algorithms can be run with minimal resources in the browser with tensorflow.js is novel.

Thank you.

General:

It is encouraging that 'definitely problematic' images have been decreasing over time in eLife. Might this have to do with eLife policies? I could not quickly find if eLife has checks in place for this, but given that JetFighter was developed in association with eLife, I wonder if there is an enhanced awareness of this issue here vs. other journals.

This is possible. We are not aware of a way to test this formally.

Author response:

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

Reviewer #1 (Public Review):

Tang et al present an important manuscript focused on endogenous virus-like particles (eVLP) for cancer vaccination with solid in vivo studies. The author designed eVLP with high protein loading and transfection efficiency by PEG10 self-assembling while packaging neoantigens inside for cancer immunotherapy. The eVLP was further modified with CpG-ODN for enhanced dendritic cell targeting. The final vaccine ePAC was proven to elicit strong immune stimulation with increased killing effect against tumor cells in 2 mouse models. Below are my specific comments:

Thanks very much to comment our work as “important”. We sincerely appreciate the extremely helpful comments from the reviewer to significantly improve the quality of our manuscript.

(1) The figures were well prepared with minor flaws, such as missed scale bars in Figures 4B, 4K, 5B, and 5C. The author should also add labels representing statistical analysis for Figures 3C, 3D, and 3E. In Figure 6G, the authors should label which cell type is the data for.

Thanks very much for the very suggestive comments. The scale bars and statistical analysis have been added in Figures 4B, 4K, 5B, 5C, 3C, 3D, and 3E. For Figure 6G, we have added “CD44+ CD62L- in CD8+ T cells” to explain the cell type.

(2) In Figure 3H, the antigen-presenting cells (APCs) increased significantly, but there was also a non-negligible 10% of APCs found in the control group, indicating some potential unwanted immune response; the authors need to explain this phenomenon or add a cytotoxic test on the normal liver or other cell lines for confirmation.

Thanks very much for this extremely helpful suggestion. The antigen-presenting cells (APCs) in Figure 3H were isolated from mouse bone marrow and then cultured in vitro for about 5 days with cytokine stimulation (IL-4 and GM-CSF). Due to the stimulation effects of IL-4 and GM-CSF, a small proportion of the APCs (~10%) was tending to mature (co-expressing CD80 and CD86) in the control group, as pointing out by the reviewer. Similarly, in Figure 3I, these 10% activated APCs can activate T cells in vitro and exhibit certain cytotoxicity. Since APCs must be induced and cultured in vitro before using in this experiment, the background cytotoxicity induced by cytokines is unavoidable, and this has been well documented in literatures.

(3) In Figure 3I, the ePAC seems to have a very similar effect on cytotoxic T-cell tumor killing compared to the peptides + CpG group. If the concentrations were also the same, based on that, questions will arise as to what is the benefit of using the compact vector other than just free peptide and CpG? Please explain and elaborate.

Thanks very much for the comment. In vitro experiments indeed demonstrated that peptides + CpG had the same T cell activating ability as ePAC, as pointing out by the reviewer. However, due to the instability of peptides and the lack of targeting, the efficiency of activating the immune system for peptides + CpG after subcutaneous injection is significantly lower than that for ePAC in vivo, as shown in Figure 3D and Figure 2A. Then, as expected, the antitumor efficacy induced by peptides alone + CpG is significantly lower than that induced by ePAC in Figure 5. We have provided a detailed description in “Results” section of “Antitumor effect of ePAC in subcutaneous HCC model” as follows: Furthermore, ePAC with the ability to target DCs and increased stability by encapsulating peptides, exhibited significantly higher tumor growth inhibition efficiency (p=0.0002) comparing with the eVLP + CpG-ODN treated group similar to the simple mixture of neoantigen peptides and adjuvant (Figures 5B and 5C). Meanwhile, the Kaplan-Meier analysis of tumor progression free survival (PFS) also clearly demonstrated the therapeutic advantages of our ePAC (p=0.0194, Figure 5B).

(4) In the animal experiment in Figures 4F to L, the activation effect of APCs was similar between ePAC and CpG-only groups with no significance, but when it comes to the HCC mouse model in Figure 5, the anti-tumor effect was significantly increased between ePAC and CpG-only group. The authors should explain the difference between these two results.

Thanks very much for the comment. Since PEG10 protein does not have an adjuvant effect, the adjuvant effect of ePAC mainly comes from the modified CpG. Therefore, although ePAC can effectively deliver tumor neoantigens, it does not have a significant advantage over free CpG in activating APCs. However, CpG only possesses the adjuvant effect and does not carry neoantigens. While it can promote the maturation of APCs, it cannot generate neoantigen-specific T cells. Consequently, the antitumor effect of CpG-only is much lower than that of ePAC in Figure 5.

Reviewer #2 (Public Review):

Summary:

The authors provided a novel antigen delivery system that showed remarkable efficacy in transporting antigens to develop cancer therapeutic vaccines.

Strengths:

This manuscript was innovative, meaningful, and had a rich amount of data.

Weaknesses:

There are still some issues that need to be addressed and clarified.

Thanks very much to comment our work as “innovative”. We sincerely appreciate the extremely helpful comments from the reviewer to significantly improve the quality of our manuscript, and the listed weaknesses have been all carefully addressed.

(1) The format of images and data should be unified. Specifically, as follows: a. The presentation of flow cytometry results; b, The color schemes for different groups of column diagrams.

Thanks very much. Following the reviewer’s comment, we have unified the format of all images and data as suggested.

(2) The P-value should be provided in Figures, including Figure 1F, 1H, 3C, 3D, and 3E.

Thanks very much. We have provided the corresponding P-values in Figure 1F, 1H, 3C, 3D, and 3E.

(3) The quality of Figure 1C was too low to support the conclusion. The author should provide higher-quality images with no obvious background fluorescent signal. Meanwhile, the fluorescent image results of "Egfp+VSVg" group were inconsistent with the flow cytometry data. Additionally, the reviewer recommends that the authors use a confocal microscope to repeat this experiment to obtain a more convincing result.

Thanks very much for this comment. Following the reviewer’s suggestion, we uniformly adjusted the original images in Figure 1C to reduce background interference and increase its quality. After eliminating background interference, the fluorescence image of the "Egfp+VSVg" group was consistent with the flow cytometry result.

(4) The survival situation of the mouse should be provided in Figure 5, Figure 6, and Figure 7 to support the superior tumor therapy effect of ePAC.

Thanks very much for the extremely helpful comment. Following the reviewer’s suggestion, we have added the progression free survival (PFS) of mice in Figure 5 and described this result in the “Results” section of “Antitumor effect of ePAC in subcutaneous HCC model” as follows: Meanwhile, the Kaplan-Meier analysis of tumor progression free survival (PFS) also clearly demonstrated the therapeutic advantages of our ePAC (p=0.0194, Figure 5B). For Figure 6 and Figure 7, to promptly detect the immune changes in the tumor microenvironment after vaccination, we were unable to conduct long-term observations on tumor-bearing mice, and therefore, we did not provide the survival curve. However, we monitored the tumor volume changes in real-time, which also can serve as an important measure for evaluating antitumor efficacy.

(5) To demonstrate that ePAC could trigger a strong immune response, the positive control group in Figure 4K should be added.

Thanks very much for this very helpful comment. Following the reviewer’s suggestion, the mouse anti-CD3 antibody was used as the positive control in vitro to activate splenic T cells for ELISPOT assay, and the corresponding results have been added in revised Figure 4K. To address this, we have provided a detailed description in “Figure legends” section of “Figure 4. ePAC delivery and immune activation in vivo” as follows: The mouse anti-CD3 antibody was used to activate splenic T cells in vitro as the positive control for ELISPOT assay.

(6) In Figure 6G-I and other figures, the author should indicate the time point of detection. Meanwhile, there was no explanation for the different numbers of mice in Figure 6G-I. If the mouse was absent due to death, it may be necessary to advance the detection time to obtain a more convincing result.

Thanks very much for the comment. The samples for Figure 6 G-I data were collected and analyzed at the day 28 after the start of treatment. Following the reviewer’s suggestion, we have specifically marked the time point of “Sacrifice for sampling” in Figure 6A. And we have provided a detailed description in “Figure legends” section of “Figure 6. Evaluation ePAC antitumor efficacy in orthotopic HCC model by αTIM-3 combination” as follows: The mice were sacrificed and sampled for analysis on the day of 28 after initiating treatment. In addition, in Figure 6G-I we have clearly indicated the sample size for each group. Although three mice in the PBS group died, we still have obtained enough samples for statistical analysis (n>3).

(7) In Figure 6B, the rainbow color bar with an accurate number of maximum and minimum fluorescence intensity should be provided. In addition, the corresponding fluorescence intensity in Figure 6B should be noted.

Thanks very much for this very helpful comment. Following the reviewer’s suggestion, we have added the rainbow color bar with an accurate number of maximum and minimum fluorescence intensity, and the statistic results in revised Figure 6B.

(8) The quality of images in Figure 1D and Figure S1B could not support the author's conclusion; please provide higher-quality images.

Thanks very much. In Figure 1D and Figure S1B, to ensure the authenticity of the results, we tried our best to improve the quality of the pictures and provided the WB results with the full membrane scan. Although some non-specific bands appeared in the results, the target bands remained prominent. Additionally, we used two tags (HA and eGFP) for verification, which fully guarantees the reliability of our findings.

(9) In Figure 2F, the bright field in the overlay photo may disturb the observation. Meanwhile, the scale bar should be provided in enlarged images.

Thanks very much. Following the reviewer’s suggestion, we have deleted the bright field in revised Figure 2F and added the scale bar in the enlarged images.

Reviewer #3 (Public Review):

Summary:

The authors harnessed the potential of mammalian endogenous virus-like proteins to encapsulate virus-like particles (VLPs), enabling the precise delivery of tumor neoantigens. Through meticulous optimization of the VLP component ratios, they achieved remarkable stability and efficiency in delivering these crucial payloads. Moreover, the incorporation of CpG-ODN further heightened the targeted delivery efficiency and immunogenicity of the VLPs, solidifying their role as a potent tumor vaccine. In a diverse array of tumor mouse models, this novel tumor vaccine, termed ePAC, exhibited profound efficacy in activating the murine immune system. This activation manifested through the stimulation of dendritic cells in lymph nodes, the generation of effector memory T cells within the spleen, and the infiltration of neoantigen-specific T cells into tumors, resulting in robust anti-tumor responses.

Strengths:

This study delivered tumor neoantigens using VLPs, pioneering a new method for neoantigen delivery. Additionally, the gag protein of VLP is derived from mammalian endogenous virus-like protein, which offers greater safety compared to virus-derived gag proteins, thereby presenting a strong potential for clinical translation. The study also utilized a humanized mouse model to further validate the vaccine's efficacy and safety. Therefore, the anti-tumor vaccine designed in this study possesses both innovation and practicality.

Thanks very much to comment our work as “novel”, “innovation” and “practicality”. We sincerely appreciate the extremely helpful comments from the reviewer to significantly improve the quality of our manuscript.

Weaknesses:

(1) CpG-ODN is an FDA-approved adjuvant with various sequence structures. Why was CpG-ODN 1826 directly chosen in this study instead of other types of CpG-ODN? Additionally, how does DEC-205 recognize CpG-ODN 1826, and can DEC-205 recognize other types of CpG-ODN?

Thanks very much for the comment. CpG-ODNs are classified into three main types based on their structural composition: A, B, and C. Among them, only the B-class CpG-ODNs 1668, 1826, and 2006 have been directly proven to effectively bind DEC-205 and activate DC cells [1]. Therefore, in this study, B-class CpG-ODN 1826 was chosen as the ligand targeting DEC-205 on the surface of DC cells. DEC-205 primarily binds sequences containing the CpG motif core in a pH-dependent manner, thus theoretically allowing DEC-205 to bind a wide range of CpG-ODNs.

[1] Lahoud MH et al. DEC-205 is a cell surface receptor for CpG oligonucleotides. PNAS. 2012

(2) Why was it necessary to treat DCs with virus-like particles three times during the in vitro activation of T cells? Can this in vitro activation method effectively obtain neoantigen-responsive T cells?

Thanks very much for the comment. DCs need to be pre-stimulated before being used to activate T cells. Although Single DC stimulation can activate T cells, but the activation efficiency is insufficient. Current research suggests that three DC-T interactions can more effectively activate T cells [2]. Therefore, we prepared virus-like particle stimulated DCs for three times to fully activate T cells. Our results in Figures 3I and 7D also demonstrate that three-time stimulations effectively activated antigen-specific T cells, resulting in stronger tumor cell killing effects.

[2] Ali M et al. Induction of neoantigen-reactive T cells from healthy donors. Nature protocol. 2019.

(3) In the humanized mouse model, the authors used Hepa1-6 cells to construct the tumor model. To achieve the vaccine's anti-tumor function, these Hepa1-6 cells were additionally engineered to express HLA-A0201. However, in the in vitro experiments, the authors used the HepG2 cell line, which naturally expresses HLA-A0201. Why did the authors not continue to use HepG2 cells to construct the tumor model, instead of Hepa1-6 cells?

Thanks very much for the comment. HepG2 cells are derived from human liver cancer. When directly implant into immunocompetent mice, they will be cleared by the mouse immune system and will not form tumors. Therefore, we have not continued to use HepG2 cells to construct the tumor model.

(4) The advantages of low immunogenicity viruses as vaccines compared with conventional adenovirus and lentivirus, etc. should be discussed.

Thanks very much for the very suggestive comment. In the introduction starting from line 76, we first described the structure and function of lentiviruses and discussed the design and application of virus-like particles (VLPs) based on lentiviruses. To provide a more comprehensive comparison, we included a discussion on VLPs, lentiviruses, and adenoviruses in the discuss section (from line 441 to line 447) as follows: “Furthermore, comparing to the virus-based delivery vectors, the lentiviruses although can stably integrate into the host genome but carry risks of insertional mutagenesis; adenoviruses although have high transduction efficiency but strong immunogenicity, which leads to fast clearance by the immune system of the host and affects the efficiency of the secondary injection. Instead, our VLPs offer low immunogenicity and superior safety, making them more suitable for repeated use and vaccine development.”

(5) In Figure 6B, the authors should provide statistical results.

Thanks very much. We have provided the statistical results in revised Figure 6B following the reviewer’s suggestion.

(6) The entire article demonstrates a clear logical structure and substantial content in its writing. However, there are still some minor errors, such as the misspelling of "Spleenic" in Figure 3B, and the sentence from line 234 should be revised.

Thanks very much. We have carefully checked and corrected the typos throughout the whole manuscript as much as possible.

(7) The authors demonstrated the efficiency of CpG-ODN membrane modification by varying the concentration of DBCO, ultimately determining the optimal modification scheme for eVLP as 3.5 nmol of DBCO. However, in Figure 2B, the author did not provide the modification efficiency when the DBCO concentration is lower than 3.5 nmol. These results should be provided.

Thanks very much for the suggestion. We have repeated the experiment and reduced the concentration of DBCO to 2.1 nmol and 0.7 nmol, respectively. The results showed that in a 200 µl eVLP reaction system, 3.5 nmol DBCO achieved the highest modification efficiency. We have provided a detailed description in “Results” section of “Envelope decoration of neoantigen-loaded eVLP” as follows: Furthermore, by varying the concentration of DBCO-C6-NHS Ester from 0 to 14 nmol, ePAC exhibited different CpG-ODN loading efficiency as evidenced by agarose gel electrophoresis (Figure 2B and Figure S3). And the results showed that in a 200 µl eVLP reaction system, 3.5 nmol DBCO achieved the highest modification efficiency.

(8) In Figure 3, the authors presented a series of data demonstrating that ePAC can activate mouse DC2.4 cells and BMDCs in vitro. However, in Figure 7, there is no evidence showing whether human DC cells can be activated by ePAC in vitro. This data should be provided.

Thanks very much for this very helpful suggestion. We used ePAC to activate human DCs and the results indicate that, compared to the blank control group, both eVLP and ePAC increased the co-expression of CD80 and CD86 in DCs, and ePAC was the most efficient. We have provided a detailed description in the “Results” section of “Antitumor effect by HLA-A*0201 restricted vaccine” as follows: After the stimulation, the DCs in ePAC treated group showed the highest level of maturation comparing to the eVLP treated group and control group (Figure S4), by using flow cytometry analysis.”

Author response:

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

Reviewer #1 (Recommendations For The Authors):

(1) Figure 2B and 2D: unlike what is written in the results part, the results are not consistent, but opposite: LSS has higher activity in 2B, less in 2D. 

The activities in Figure 2B come from NMR kinetic experiments with pGly, whereas Figure 2D reports on activity towards whole S. aureus cells. The LytM and LSS activities in these two experiments are indeed not directly comparable, but served to highlight the fact that simple pentaglycine is a poor model substrate for M23 enzymes. We carried out a turbidity assay with pristine enzymatic preparation and indeed it is highly consistent both with the kinetic assay using pentaglycine (Fig. 2B) as well as with larger PG fragments (Fig. 2K) indicating that the catalytic domain of LSS is significantly more efficient than LytM in hydrolyzing cells from community acquired methicillin resistant S. aureus strain USA300 as well as synthetic PG fragments.  The corresponding paragraph in Results has now been updated and rephrased.

(2) Figure 2, panel K missing statistical analysis, which makes it difficult to appreciate if the difference is significant. If it is a one-time experiment or a single value, the value should be presented as a table. The corresponding text in the results part is confusing. The fold change or drop in percentage is unclear in the figure. 

We have added a table (panel L) to Figure 2, which shows absolute values of LSS and LytM hydrolysis rates. Indeed, most of the values are from single NMR kinetic measurements, however, PG fragment (2) for LSS and PG fragment (3) for LytM were measured as duplicates to verify the reproducibility of the data. This is now mentioned in Figure 3 legend and in the Materials and Methods. Also, the corresponding text in the Results has been updated and rephrased.

(3) Figure 3H: the cleavage of D-ala-gly is unclear, the cleavage products need to be labeled and quantified. The experiment used purified PG treated with mutanolysin. Presumably, mixed monomers, dimers, trimers, and multimers are used. It would be helpful to show the HPLC profile of the purified muropeptide. It would be informative to analyze which fractions generate D-ala-gly. In addition, the intact murein sacculus should be included. 

For the sake of clarity, we have moved the 13C-HMBC spectra presented in Figure 3H to Fig. S7 in the Supplementary Material. The full carbonyl carbon region of the reference (prior to addition of enzyme) 13C-HMBC spectrum together with larger expansions of spectra acquired from enzyme-treated muropeptides are now shown. Furthermore, graphical presentations of identified PG fragments due to LSS/LytM activity are included. No HPLC analysis of the muropeptides was performed at this stage. Being insoluble, the intact murein sacculus is not amenable to liquid-state NMR studies, but we envisage studies of this remarkably complex structure also with solid-state NMR.

Reviewer #2 (Recommendations For The Authors): 

Overall, the experiments address the question asked by the authors and no additional experiments are required to strengthen the conclusions drawn. 

Abstract: 

The abstract is not well written and more specific (and accurate) information should be provided by the authors. 

We are grateful for the constructive and helpful comments to improve our manuscript. The abstract has now been modified by taking into account the Reviewer’s suggestions.

Introduction 

The intro is relatively long and wordy. It could most certainly be shortened and written in a more simple way to make it more impactful.

The introduction has now been modified by taking into account the Reviewer’s suggestions.

(2) One of the peptide stems in Figure 1 is missing a pentaglycine side chain; I would recommend increasing the font size; the peptide stem looks like it is attached to the carbon in position 2, it may be a good idea to move it to the left? 

We thank the Reviewer for this comment. Figure 1 has been improved, the frameshift has been fixed and the non-cross-linked pGly bridge has been included to the lysine side-chain in tetraStem.

Results 

Figure 2 is a bit overwhelming and its description is sketchy. Fig 2B shows a much higher activity of LSS on pGly as compared to LytM whilst 2K shows a very similar rate. 

We have rearranged Figures 1 and 2 by moving the original panel J in Figure 2 (structures of PG fragments) to Figure 1 panel C. The bar graph in Figure 2J now shows absolute rates of substrate hydrolysis for 2 mM LSS and LytM. These indicate that LSS is much more efficient against PG fragments in vitro in comparison to LytM. Rates normalized with respect to pGly are shown in Figure 2K. Also, a table showing absolute rates of hydrolysis for 2 mM LSS and 50 mM LytM has been included in Figure 2, panel L. In this Table, the values for PG fragments 2 and 3 were determined by two independent measurements to test and accredit the reproducibility of the method. This is also now elaborated further in the Materials and Methods.

Figure 3 is impressive and very informative but again hard to follow. 

- Panels 3A and 3B are nicely conceived but the resolution is rather poor and it is difficult to know exactly where the arrows point. 

We very much value suggestions given by the Reviewer to improve readability of our manuscript. In the case of Figure 3, we have now greatly enhanced the resolution and readability of the figure by horizontal scaling of panels A and B.

Figure 4 shows a comparative analysis of catalytic rate using various substrates, the authors may want to present graphs with the same y-axis to get the most out of the comparison between substrates. 

The scaling of the y-axis is the same for all the substrates now. In addition, we have reorganized the panels in the figure to enhance readability.

Figure 5: - The same remark as above, please cite all panels in alphabetical order. 

Citing to Figure 5 has now been revised.

Material and methods: 

- How were the peptide concentrations determined? It may be useful to indicate if specific conditions were required to solubilize some peptides, pGly is particularly insoluble in aqueous solutions. 

- Page 19, replace cpm by rpm; biological or technical replicates?

These have now been added and edited accordingly.

Author response:

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

Reviewer #1:

After reviewing the authors' response letter and the revised manuscript, I believe they have done a commendable job in addressing my comments.

Additionally, I concur with the concerns raised by Reviewer #2 regarding several potential confounding factors that require better control in their experimental design. These include the differences in physical properties between vocal and nonvocal stimuli, as well as the infant's exposure to the speech/auditory environment. These concerns should be thoroughly and explicitly discussed in the manuscript, ensuring a clearer understanding for the readers.

Thank you for the suggestion. We have discussion these limitations in our revised manuscript. In this round of revision, we have tempered our conclusion due to these limitations.

Reviewer #2:

The revised manuscript does discuss the limitations of the control stimuli, as well as the limitations with regard to conclusions that can be drawn from this data set. I therefore expected the authors to temper a bit their recommendation that this could be a 'screening' signal for autism because these data are not sufficiently strong to make that recommendation. Also, in the same vein, perhaps the title might be adjusted somewhat to suggest less certainty, for example, by using the word "change" rather than "milestone"'? The data are of interest, but the limitations are genuine limitations.

Thank you for your expert comments and considerations. We have moderated our recommendation for autism screening and softened the statement of “milestone” throughout the manuscript. Please see the updated article title, abstract, significance statement, and discussion.

Author response:

Reviewer #1 (Public Review):

Summary:

A nice study trying to identify the relationship between E. coli O157 from cattle and humans in Alberta, Canada.

Strengths:

(1) The combined human and animal sampling is a great foundation for this kind of study.

(2) Phylogenetic analyses seem to have been carried out in a high-quality fashion.

Weaknesses:

I think there may be a problem with the selection of the isolates for the primary analysis. This is what I'm thinking:

(1) Transmission analyses are strongly influenced by the sampling frame.

(2) While the authors have randomly selected from their isolate collections, which is fine, the collections themselves are not random.

(3) The animal isolates are likely to represent a broad swathe of diversity, because of the structured sampling of animal reservoirs undertaken (as I understand it).

(4) The human isolates are all from clinical cases. Clinical cases of the disease are likely to be closely related to other clinical cases, because of outbreaks (either detected, or undetected), and the high ascertainment rate for serious infections.

(5) Therefore, taking an equivalent number of animal and clinical isolates, will underestimate the total diversity in the clinical isolates because the sampling of the clinical isolates is less "independent" (in the statistical sense) than sampling from the animal isolates.

(6) This could lead to over-estimating of transmission from cattle to humans.

We appreciate the reviewer’s careful thoughts about our sampling strategy. We agree with points (1) and (2), and we will provide additional details on the animal collections as requested.

We agree with point (3) in theory but not in fact. As shown in Figure 3a, the cattle isolates were very closely related, despite the temporal and geographic breadth of sampling within Alberta. The median SNP distance between cattle sequences was 45 (IQR 36-56), compared to 54 (IQR 43-229) SNPs between human sequences from cases in Alberta during the same years. Additionally, as shown in Figure 2, only clade A and B isolates – clades that diverge substantially from the rest of the tree – were dominated by human cases in Alberta. We will better highlight this evidence in the revision.

We agree with the reviewer in point (4) that outbreaks can be an important confounder of phylogenetic inference. This is why we down-sampled outbreaks (based on genetic relatedness, not external designation) in our extended analyses (lines 192-194). We did not do this in the primary analysis, because there were no large clusters of identical isolates. Figure 3b shows a limited number of small clusters; however, clustered cattle isolates outnumbered clustered human isolates, suggesting that any bias would be in the opposite direction the reviewer suggests. Regarding severe cases being oversampled among the clinical isolates, this is absolutely true and a limitation of all studies utilizing public health reporting data. We will make this limitation to generalizability clearer in the discussion. However, as noted above, clinical isolates were more variable than cattle isolates, so it does not appear to have heavily biased the analysis.

We disagree with the reviewer on point (5). While the bias toward severe cases could make the human isolates less independent, the relative sampling proportions are likely to induce greater distance between clinical isolates than cattle isolates, which is exactly what we observe (see response to point (3) above). Cattle are E. coli O157:H7’s primary reservoir, and humans are incidental hosts not able to sustain infection chains long-term. Not only is the bacteria prevalent among cattle, cattle are also highly prevalent in Alberta. Thus, even with 89 sampling points, we are still capturing a small proportion of the E. coli O157:H7 in the province. Being able to sample only a small proportion of cattle’s E. coli O157:H7 increases the likelihood of only sampling from the center of the distribution, making extreme cases such as that shown at the very bottom of the tree in Figure 3b, rare and important. In comparison, sampling from human cases constitutes a higher proportion of human infections relative to cattle, and is therefore more representative of the underlying distribution, including extremes. We will add this point to the limitations. As with the clustering above, if anything, this outcome would have biased the study away from identifying cattle as the primary reservoir. Additionally, the relatively small proportion of cattle sampled makes our finding that 15.7% of clinical isolates were within 5 SNPs of a cattle isolate, the distance most commonly used to indicate transmission for E. coli O157:H7, all the more remarkable.

Because of the aforementioned points, we disagree with the reviewer’s conclusion in point (6). We believe transmission from cattle-to-humans is likely underestimated for the reasons given above. Not only do all prior studies indicate ruminants as the primary reservoirs of E. coli O157:H7, and humans as only incidental hosts, our specific data do not support the reviewer’s individual contentions. That said, we will conduct a sensitivity analysis as recommended to determine the impact of sampling and inclusion of the small clusters on our primary findings.

(7) We hypothesize that the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence" - this seems a bit tautological. There is a lot of O157 because there's a lot of transmission. What part of the fact it is local means that it is a principal cause of high incidence? It seems that they've observed a high rate of local transmission, but the reasons for this are not apparent, and hence the cause of Alberta's incidence is not apparent. Would a better conclusion not be that "X% of STEC in Alberta is the result of transmission of local variants"? And then, this poses a question for future epi studies of what the transmission pathway is.

The reviewer is correct, and the suggestion for the direction of future studies was our intent with this statement. We will revise it.

Reviewer #2 (Public Review):

This study identified multiple locally evolving lineages transmitted between cattle and humans persistently associated with E. coli O157:H7 illnesses for up to 13 years. Furthermore, this study mentions a dramatic shift in the local persistent lineages toward strains with the more virulent stx2a-only profile. The authors hypothesized that this phenomenon is the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence. These opinions more effectively explain the role of the cattle reservoir in the dynamics of E. coli O157:H7 human infections.

(1) The authors acknowledge the possibility of intermediate hosts or environmental reservoirs playing a role in transmission. Further discussion on the potential roles of other animal species commonly found in Alberta (e.g., sheep, goats, swine) could enhance the understanding of the transmission dynamics. Were isolates from these species available for analysis? If not, the authors should clearly state this limitation.

We will expand the discussion of other species in Alberta, as suggested, including other livestock, wildlife, and the potential role of birds and flies. Unfortunately, we did not have sequences available from other species, and we will add this to the limitations. Sequences from other species may be available from sequences collected by others, which as we note in the limitations do not have sufficient metadata to assign them to Alberta vs. the rest of Canada. While we have requested this data, we have been unsuccessful in obtaining it. We will continue to pursue it.

(2) The focus on E. coli O157:H7 is understandable given its prominence in Alberta and the availability of historical data. However, a brief discussion on the potential applicability of the findings to non-O157 STEC serogroups, and the limitations therein, would be beneficial. Are there reasons to believe the transmission dynamics would be similar or different for other serogroups?

We appreciate this comment and will expand our discussion of relevance to non-O157 STEC. Other authors have proposed that transmission dynamics differ, and studies of STEC risk factors, including our own, support this. However, there has been very little direct study of non-O157 transmission dynamics and there is even less cross-species genomic and metadata available for non-O157 isolates of concern.

(3) The authors briefly mention the need for elucidating local transmission systems to inform management strategies. A more detailed discussion on specific public health interventions that could be targeted at the identified LPLs and their potential reservoirs would strengthen the paper's impact.

We agree with the reviewer that this would be a good addition to the manuscript. The public health implications for control are several and extend to non-STEC reportable zoonotic enteric infections, such as Campylobacter and Salmonella. We will add a discussion of these.

(4) Understanding the relationship between specific risk factors and E. coli O157:H7 infections is essential for developing effective prevention strategies. Have case-control or cohort studies been conducted to assess the correlation between identified risk factors and the incidence of E. coli O157:H7 infections? What methodologies were employed to control for potential confounders in these studies?

Yes, there have been several case-control studies of reported cases. Many of these are referenced in the discussion in terms of the contribution of different sources to infection. However, we will add a more explicit discussion of risk factors.

(5) The study's findings are noteworthy, particularly in the context of E. coli O157:H7 epidemiology. However, the extent to which these results can be replicated across different temporal and geographical settings remains an open question. It would be constructive for the authors to provide additional data that demonstrate the replication of their sampling and sequencing experiments under varied conditions. This would address concerns regarding the specificity of the observed patterns to the initial study's parameters.

We appreciate the reviewer’s comment, as we are currently building on this analysis with an American dataset with different types of data available than were used in this study. We will add a discussion of this. We will also be adding a sensitivity analysis to the manuscript simulating a different sampling approach, which should also be informative to this question.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Weaknesses:

The authors need to discuss their study in the context of previous papers that have shown an important role for E. tarda flagellin in inflammasome activation and test whether flagellin and/or E. tarda T3SSs needle or rod can activate NLRC4.

We will add discussions on E. tarda flagellin and examine whether E. tarda flagellin or T3SS needle/rod can activate NLRC4.

The authors show that eseB and its homologs can activate NLRC4, but there are also other translocon proteins that are very different such as YopB or PopB. and share little homology with eseB. It would be nice to include a section comparing the different type 3 secretion systems. are there 2 different families of T3SSs, those that feature translocon components that are recognized by NAIP-NLRC4 and those that cannot be recognized?

The reviewer raises an interesting question. We will explore this question and provide relevant discussions/hypothesis in the revised manuscript.

Reviewer #2 (Public Review):

Weaknesses:

The functional assessment of EseB homologues is limited to inflammasome activation at the protein level but does not include the effects on cell viability as shown for E. tarda EseB. Confirmation that EseB homologues have similar effects on cell death would strengthen this portion of the manuscript.

According to the reviewer’s suggestion, we plan to examine the effects of representative EseB homologs on cell death.

Author response:

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

The concerns raised during the review have been incorporated into the discussion of the results, and the need for further research is acknowledged in the paper. This is not possible in the present study, as the clinical project has been completed and further patients cannot be enrolled without starting a new project. We are confident that the results are scientifically valid and that the methodology was scientifically sound and up to date. They were obtained on a dataset that was obviously large enough to allow 20% of it to be set aside and a machine-learned classifier to be trained on the remaining 80%, which then assigned samples to neuropathy with an accuracy better than guessing.

Furthermore, our results are at least tentatively replicated in a completely independent data set from another patient cohort. The strengths and limitations of the study design, in particular the latter, are discussed in the necessary depth. In summary, the machine-learned results provided major hits on one side and probably unimportant lipids on the other side of the variable importance scale. Both could be verified in vitro. We are therefore confident that we have contributed to the advancement of knowledge about cancer therapy-associated neuropathy and look forward to further developments in this area.

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

Weaknesses Reviewer 1: 

There are a number of weaknesses in the study. The small sample size is a significant limitation of the study. Out of 31 patients, only 17 patients were reported to develop neuropathy, with significant neuropathy (grade 2/3) in only 5 patients. The authors acknowledge this limitation in the results and discussion sections of the manuscript, but it limits the interpretation of the results. Also acknowledged is the limited method used to assess neuropathy. 

We agree with the reviewer that the cohort size and assessment of neuropathy are limitations of our study as we already described in the corresponding section of the manuscript. However, occurrence and grade of the neuropathy are in line with results reported from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70% (54.9% in our cohort), and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (13). In these studies, neuropathy is assessed by using questionnaires or by grading via NCTCTCAE as in our study. In summary, assessment and occurrence of neuropathy of our reported cohort are in line with previous reports.

Potentially due to this small number of patients with neuropathy, the machine learning algorithms could not distinguish between samples with and without neuropathy. Only selected univariate analyses identified differences in lipid profiles potentially related to neuropathy.  

The data analysis consistently followed a "mixture of experts" approach, as this seems to be the most successful way to deal with omics data. We have elaborated on this in the Methods section, including several supporting references. Regarding the quoted sentence from the results section, after rereading it, we realized that it was somewhat awkwardly worded. What we mean is now better worded in the results section, namely “Although the three algorithms detected neuropathy in new cases, unseen during training, at balanced accuracy of up to 0.75, while only the guess level of 0.5 was achieved when using permuted data for training, the 95% CI of the performance measures was not separated from guess level”. Therefore, multivariate feature selection was not considered a valid approach, since it requires that the algorithms from which the feature importance is read can successfully perform their task of class assignment (4). Therefore, univariate methods (Cohen's d, FPR, FWE) were preferred, as well as a direct hypothesis transfer of the top hits from the abovementioned day1/2 assessments to neuropathy. Classical statistics consisting of direct group comparisons using Kruskal-Wallis tests (5) were performed.” 

It was our approach to investigate the data set in an unbiased manner by different machine learning algorithms and select those lipids that the majority of the algorithms considered important for distinguishing the patient groups (majority voting). This way, the inconsistencies and limitations of a single evaluation method, such as regression analysis, that occur in some datasets, can be mitigated. 

Three sphingolipid mediators including SA1P differed between patients with and without neuropathy at the end of treatment. These sphingolipids were elevated at the end of treatment in the cohort with neuropathy, relative to those without neuropathy. However, across all samples from pre to post-paclitaxel treatment, there was a significant reduction in SA1P levels. It is unclear from the data presented what the underlying mechanism for this result would be. 

We agree with the reviewer that our study does not identify the mechanism by which paclitaxel treatment alters sphingolipid concentrations in the plasma of patients. It has been reported before that paclitaxel may increase expression and activity of serine palmitoyltransferase (SPT) which is the crucial enzyme and rate-limiting step in the denovo synthesis of sphingolipids. This may be associated with a shift towards increased synthesis of 1-deoxysphingolipids and a decrease of “classical” sphingolipids (6) and may explain the general reduction of SA1P and other sphingolipid levels after paclitaxel treatment in our study. 

It is also conceivable that paclitaxel reduces the release of sphingolipids into the plasma. Paclitaxel is a microtubule stabilizing agent (7) that may interfere with intracellular transport processes and release of paracrine mediators. 

The mechanistic details of paclitaxel involvement in sphingolipid metabolism or transport are highly interesting but identifying them is beyond the scope of our manuscript.

If elevated SA1P is associated with neuropathy development, it would be expected to increase in those who develop neuropathy from pre to post-treatment time points. 

There is a general trend of reduced plasma SA1P concentrations following paclitaxel treatment. Nevertheless, patients experiencing neuropathy exhibit significantly elevated SA1P levels post-treatment. 

It has been shown before that paclitaxel-induced neuropathic pain requires activation of the S1P1 receptor in a preclinical study (8). Moreover, a meta-analysis of genome-wide association studies (GWAS) from two clinical cohorts identified multiple regulatory elements and increased activity of S1PR1 associated with paclitaxel-induced neuropathy (9). These data imply that enhanced S1P receptor activity and signaling are key drivers of paclitaxel-induced neuropathy. It seems that both, increased levels of the sphingolipid ligands in combination with enhanced expression and activity of S1P receptors can potentiate paclitaxel-induced neuropathy in patients. This explains why also decreased SA1P concentrations after paclitaxel treatment can still enhance neuropathy via the S1PRTRPV1 axis in sensory neurons.

We added this paragraph to the discussions section of our manuscript.

Primary sensory neuron cultures were used to examine the effects of SA1P application.

SA1P application produced calcium transients in a small proportion of sensory neurons. It is not clear how this experimental model assists in validating the role of SA1P in neuropathy development as there is no assessment of sensory neuron damage or other hallmarks of peripheral neuropathy. These results demonstrate that some sensory neurons respond to SA1P and that this activity is linked to TRPV1 receptors. However, further studies will be required to determine if this is mechanistically related to neuropathy.

As we detected elevated levels of SA1P in the plasma of PIPN patients, we can assume higher concentrations in the vicinity of sensory neurons. These neurons are the main drivers for neuropathy and neuropathic pain and are strongly affected by paclitaxel in their activity (10-15). Also, TRPV1 shows altered activity patterns in response to paclitaxel treatment (16). Because of its relevance for nociception and pathological pain, TRPV1 activity is a suitable and representative readout for pathological pain states in peripheral sensory neurons (17, 18), which is why we investigated them.

We would like to point out the potency of SA1P to increase capsaicin-induced calciumtransients in sensory neurons at submicromolar concentrations. 

We also agree with the reviewer that further studies need to investigate the underlying mechanisms in more detail. We added this sentence to the final paragraph in the discussion section of our manuscript.

Weaknesses Reviewer 2: 

The article is poorly written, hindering a clear understanding of core results. While the study's goals are apparent, the interpretation of sphingolipids, particularly SA1P, as key mediators of paclitaxel-induced neuropathy lacks robust evidence. 

We agree that the relevance of SA1P as key mediator of paclitaxel-induced neuropathy might be overstated and changed the wording throughout the manuscript accordingly. However, we would like to point out the potency of this lipid to increase capsaicin-induced calcium-transients in sensory neurons at submicromolar concentrations. 

Also, the lipid signature in the plasma of PIPN patients shows a unique pattern and sphingolipids are the group that showed the strongest alterations when comparing the patient groups. We also measured eicosanoids, such as prostaglandins, linoleic acid metabolites, endocannabinoids and other lipid groups that have previously been associated with influences on pain perception or nociceptor sensitization. However, none of these lipids showed significant differences in their concentrations in patient plasma. This is why we consider sphingolipids as contributors to or markers of paclitaxel-induced neuropathy in patients.

We also revised the entire article to improve its clarity.

The introduction fails to establish the significance of general neuropathy or peripheral neuropathy in anticancer drug-treated patients, and crucial details, such as the percentage of patients developing general neuropathy or peripheral neuropathy, are omitted. This omission is particularly relevant given that only around 50% of patients developed neuropathy in this study, primarily of mild Grade 1 severity with negligible symptoms, contradicting the study's assertion of CIPN as a significant side effect. 

As we already described in the introduction, CIPN is a serious dose- and therapy-limiting side effect, which affects up to 80% of treated patients. This depends on dose and combination of chemotherapeutic agents. For paclitaxel, therapeutic doses range from 80 – 225 mg/m². As CIPN symptoms are dose-dependent, the number of PIPN patients that receive a high paclitaxel dose is higher than the number of PIPN patient receiving a low dose.

In our study, we mainly used a low dose paclitaxel, because this therapeutic regimen is the most widely used paclitaxel monotherapy. From previous studies, the expected occurrence of neuropathy with this therapeutic regimen is around 50-70%, and most patients (8090%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3).

Our results are within the range reported by these studies (54.9% patients with neuropathy). Also, as we highlight in Table S1, the neuropathy symptoms persist in most cases for several years after chemotherapy, affecting quality of life of these patients which makes it far from being a negligible symptom.

We added some more information concerning PIPN in the introduction section in which we emphasize the clinical problem.

The lack of clarity in distinguishing results obtained by lipidomics using machine learning methods and conventional methods adds to the confusion. The poorly written results section fails to specify SA1P's downregulation or upregulation, and the process of narrowing down to sphingolipids and SA1P is inadequately explained. 

We have tried to keep the machine learning part in the main manuscript short and moved major parts of it to a supplement. However, as this has been claimed to have led to a lack of clarity, we have expanded the description of the data analysis and added extensive explanations and supporting references for the mixed expert approach that was used throughout the analysis. We hope this is now clear.

Integrating a significant portion of the discussion section into the results section could enhance clarity. An explanation of the utility of machine learning in classifying patient groups over conventional methods and the citation of original research articles, rather than relying on review articles, may also add clarity to the usefulness of the study. 

As suggested by the reviewer, we moved the relevant parts from the discussion to the results section in the revised version of our manuscript.

Reviewer #1 (Recommendations For The Authors): 

Figure 2 should be better explained or removed. In its current form, it does not add to the interpretation of the manuscript.  

As mentioned above, we have expanded the description of the ESOM/U-matrix method in the Methods section and rewritten the figure legend. In addition, we have annotated the U-matrix in the figure. The method has been reported extensively in the computer science and biomedical literature, and a more detailed description in the referenced papers would go beyond the current focus on lipidomics. However, we believe that this discussion is sufficiently detailed for the readers of this report: "… a second unsupervised approach was used to verify the agreement between the lipidomics data structure and the prior classification, implemented as self-organizing maps (SOM) of artificial neurons (19). In the special form of an “emergent” SOM (ESOM (20)), the present map consisted of 4,000 neurons arranged on a two-dimensional toroidal grid with 50 rows and 80 columns (21, 22). ESOM was used because it has been repeatedly shown to correctly detect subgroup structures in biomedical data sets comparable to the present one (20, 22, 23). The core principle of SOM learning is to adjust the weights of neurons based on their proximity to input data points. In this process, the best matching unit (BMU) is identified as the neuron closest to a given data point. The adaptation of the weights is determined by a learning rate (η) and a neighborhood function (h), both of which gradually decrease during the learning process. Finally, the groups are projected onto separate regions of the map. On top of the trained ESOM, the distance structure in the high-dimensional feature space was visualized in the form of a so-called U-matrix (24) which is the canonical tool for displaying the distance structures of input data on ESOM (21). 

The visual presentation facilitates data group separation by displaying the distances between BMUs in high-dimensional space in a color-coding that uses a geographical map analogy, where large "heights" represent large distances in feature space, while low "valleys" represent data subsets that are similar. "Mountain ranges" with "snow-covered" heights visually separate the clusters in the data. Further details about ESOM can be found in (24)."

The second patient cohort is only included in the discussion - with cohort details in the supplementary material and figures included in the main text. Perhaps these data should be removed entirely. The findings are described as trends and not statistically significant and multiple issues with this second cohort are mentioned in the discussion. 

We agree with the reviewer that including the second patient cohort in the discussion is inadequate. Of course, there are differences between the patient cohorts that do not allow direct comparison and that are highlighted in the section on limitations of the study. However, we still think it is interesting and relevant to show these data, because we used our algorithms trained on the first patient cohort to analyze the second cohort. And these data support the main results. 

We therefore moved the entire paragraph to the results section of to improve coherence of our manuscript. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

The title does not reflect the content of the paper and should be changed to better reflect the content and its significance. 

We change the title to “Machine learning and biological validation identify sphingolipids as potential mediators of paclitaxel-induced neuropathy in cancer patients” to avoid overstating the results as suggested by the Reviewer.

Further, the discussion should be modified to avoid overstating the results. 

As the reviewer suggests, we changed the wording to avoid overstating the results. 

Reviewer #2 (Recommendations For The Authors): 

Please address the absence of clear neuropathy in the majority of patients after treatment with paclitaxel in your discussion. 

As stated above, occurrence and grade of the neuropathy are in line with the results from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70%, (the variability is due to differences in the assessment methods) and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3). 

We added this information in the discussion section of the revised manuscript.

Line 65: Kindly replace review articles with original research articles for proper citation. 

We replaced the review articles with original publications, focusing on clinical observations. We added the following publications: Jensen et al., Front Neurosci 2020; Chen et al., Neurobiol Aging 2018; Igarashi et al., J Alzheimers Dis. 2011; Kim et al., Oncotarget 2017 as references 17-20 in the revised version of our manuscript.

Line 260: The mention of SA1P is introduced here without prior reference (do not use words like "again", or "see above", if it is not previously mentioned). Adjust the text for coherence.

We agree with the reviewer that the introduction of SA1P in this passage in incoherent. We replaced the sentence in line 260 with: 

The small set of lipid mediators emerging from all three methods as informative for neuropathy included the sphingolipid sphinganine-1-phosphate (SA1P), also known as dihydrosphingosine-1-phosphate (DH-S1P)…”

Lines 301-315: Consider relocating several lines from this section to the results section for improved clarity. 

We moved the lines 309-312 explaining the algorithm selection and their validation success in the corresponding results section (Lipid mediators informative for assigning postpaclitaxel therapy samples to neuropathy).

Lines 382-396: Move this content to the results section to enhance the organization and coherence of the manuscript. 

We moved the entire paragraph to the results section of our manuscript to improve coherence. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

References

(1) Barginear M, Dueck AC, Allred JB, Bunnell C, Cohen HJ, Freedman RA, et al. Age and the Risk of Paclitaxel-Induced Neuropathy in Women with Early-Stage Breast Cancer (Alliance A151411): Results from 1,881 Patients from Cancer and Leukemia Group B (CALGB) 40101. Oncologist. 2019;24(5):617-23.

(2) Mauri D, Kamposioras K, Tsali L, Bristianou M, Valachis A, Karathanasi I, et al. Overall survival benefit for weekly vs. three-weekly taxanes regimens in advanced breast cancer: A metaanalysis. Cancer Treat Rev. 2010;36(1):69-74.

(3) Budd GT, Barlow WE, Moore HC, Hobday TJ, Stewart JA, Isaacs C, et al. SWOG S0221: a phase III trial comparing chemotherapy schedules in high-risk early-stage breast cancer. J Clin Oncol. 2015;33(1):58-64.

(4) Lötsch J, and Ultsch A. Pitfalls of Using Multinomial Regression Analysis to Identify ClassStructure-Relevant Variables in Biomedical Data Sets: Why a Mixture of Experts (MOE) Approach Is Better. BioMedInformatics. 2023;3(4):869-84.

(5) Kruskal WH, and Wallis WA. Use of Ranks in One-Criterion Variance Analysis. J Am Stat Assoc. 1952;47(260):583-621.

(6) Kramer R, Bielawski J, Kistner-Griffin E, Othman A, Alecu I, Ernst D, et al. Neurotoxic 1deoxysphingolipids and paclitaxel-induced peripheral neuropathy. FASEB J. 2015;29(11):4461-72.

(7) Field JJ, Diaz JF, and Miller JH. The binding sites of microtubule-stabilizing agents. Chem Biol. 2013;20(3):301-15.

(8) Janes K, Little JW, Li C, Bryant L, Chen C, Chen Z, et al. The development and maintenance of paclitaxel-induced neuropathic pain require activation of the sphingosine 1-phosphate receptor subtype 1. J Biol Chem. 2014;289(30):21082-97.

(9) Chua KC, Xiong C, Ho C, Mushiroda T, Jiang C, Mulkey F, et al. Genomewide Meta-Analysis Validates a Role for S1PR1 in Microtubule Targeting Agent-Induced Sensory Peripheral Neuropathy. Clin Pharmacol Ther. 2020;108(3):625-34.

(10) Kawakami K, Chiba T, Katagiri N, Saduka M, Abe K, Utsunomiya I, et al. Paclitaxel increases high voltage-dependent calcium channel current in dorsal root ganglion neurons of the rat. J Pharmacol Sci. 2012;120(3):187-95.

(11) Pittman SK, Gracias NG, Vasko MR, and Fehrenbacher JC. Paclitaxel alters the evoked release of calcitonin gene-related peptide from rat sensory neurons in culture. Exp Neurol. 2013.

(12) Luo H, Liu HZ, Zhang WW, Matsuda M, Lv N, Chen G, et al. Interleukin-17 Regulates NeuronGlial Communications, Synaptic Transmission, and Neuropathic Pain after Chemotherapy.

Cell reports. 2019;29(8):2384-97 e5.

(13) Pease-Raissi SE, Pazyra-Murphy MF, Li Y, Wachter F, Fukuda Y, Fenstermacher SJ, et al. Paclitaxel Reduces Axonal Bclw to Initiate IP3R1-Dependent Axon Degeneration. Neuron. 2017;96(2):373-86 e6.

(14) Duggett NA, Griffiths LA, and Flatters SJL. Paclitaxel-induced painful neuropathy is associated with changes in mitochondrial bioenergetics, glycolysis, and an energy deficit in dorsal root ganglia neurons. Pain. 2017.

(15) Li Y, Adamek P, Zhang H, Tatsui CE, Rhines LD, Mrozkova P, et al. The Cancer Chemotherapeutic Paclitaxel Increases Human and Rodent Sensory Neuron Responses to TRPV1 by Activation of TLR4. J Neurosci. 2015;35(39):13487-500.

(16) Hara T, Chiba T, Abe K, Makabe A, Ikeno S, Kawakami K, et al. Effect of paclitaxel on transient receptor potential vanilloid 1 in rat dorsal root ganglion. Pain. 2013;154(6):882-9.

(17) Jardin I, Lopez JJ, Diez R, Sanchez-Collado J, Cantonero C, Albarran L, et al. TRPs in Pain Sensation. Front Physiol. 2017;8:392.

(18) Julius D. TRP Channels and Pain. Annual review of cell and developmental biology.

2013;29:355-84.

(19) Kohonen T. Self-Organized Formation of Topologically Correct Feature Maps. Biol Cybern. 1982;43(1):59-69.

(20) Lötsch J, Lerch F, Djaldetti R, Tegder I, and Ultsch A. Identification of disease-distinct complex biomarker patterns by means of unsupervised machine-learning using an interactive R toolbox (Umatrix). Big Data Analytics. 2018;3(1):5.

(21) Ultsch A. 2003.

(22) Lotsch J, Geisslinger G, Heinemann S, Lerch F, Oertel BG, and Ultsch A. Quantitative sensory testing response patterns to capsaicin- and ultraviolet-B-induced local skin hypersensitization in healthy subjects: a machine-learned analysis. Pain. 2018;159(1):11-24.

(23) Lötsch J, Thrun M, Lerch F, Brunkhorst R, Schiffmann S, Thomas D, et al. Machine-Learned Data Structures of Lipid Marker Serum Concentrations in Multiple Sclerosis Patients Differ from Those in Healthy Subjects. Int J Mol Sci. 2017;18(6).

(24) Lötsch J, and Ultsch A. Cham: Springer International Publishing; 2014:249-57.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Wu et al. introduce a novel approach to reactivate the Muller glia cell cycle in the mouse retina by simultaneously reducing p27Kip1 and increasing cyclin D1 using a single AAV vector. The approach effectively promotes Muller glia proliferation and reprograming without disrupting retinal structure or function. Interestingly, reactivation of the Muller glia cell cycle downregulates IFN pathway, which may contribute to the induced retinal regeneration. The results presented in this manuscript may offer a promising approach for developing Müller glia cell-mediated regenerative therapies for retinal diseases.

Strengths:

The data are convincing and supported by appropriate, validated methodology. These results are both technically and scientifically exciting and are likely to appeal to retinal specialists and neuroscientists in general.

Weaknesses:

There are some data gaps that need to be addressed.

(1) Please label the time points of AAV injection, EdU labeling, and harvest in Figure 1B.

We thank the reviewer for highlighting the lack of clarity in our experimental design. We will label all experiment timelines in the figures where appropriate in the revised version.

(2) What fraction of Müller cells were transduced by AAV under the experimental conditions?

We apologize for not clearly conveying the transduction efficiency. The retinal region adjacent to the injection site, typically near the central retina, exhibits a transduction efficiency of nearly 100%. In contrast, the peripheral retina shows a lower transduction efficiency compared to the central region. We will include the quantification of AAV transduction efficiency in the revised manuscript.

The quantification of Edu+ MG or other markers was conducted in the area with the highest efficiency. 

(3) It seems unusually rapid for MG proliferation to begin as early as the third day after CCA injection. Can the authors provide evidence for cyclin D1 overexpression and p27 Kip1 knockdown three days after CCA injection?

In our pilot study, we tested the onset time of GFP expression from AAV-GFAP-GFP following intravitreal injection. We observed GFP expression in MG as early as two days post-infection. These findings will be included in the revised manuscript. Additionally, we plan to perform qPCR or Western blot analysis to confirm cyclin D1 overexpression and p27kip1 knockdown at the onset of Müller glia proliferation, which will also be included in the revised manuscript.

(4) The authors reported that MG proliferation largely ceased two weeks after CCA treatment. While this is an interesting finding, the explanation that it might be due to the dilution of AAV episomal genome copies in the dividing cells seems far-fetched.

We believe that the lack of durability in high Cyclin D1 and low p27kip1 levels in MG contributes to the cessation of their proliferation. A potential reason for the loss of high Cyclin D1 overexpression and p27kip1 knockdown during MG proliferation could be the dilution of the AAV episomal genome. However, testing this hypothesis is challenging. Instead, we plan to provide direct evidence in the revised manuscript by examining the levels of Cyclin D1 and p27kip1 in the retina treated with CCA before and after the peak of MG proliferation.

Reviewer #2 (Public Review):

This manuscript by Wu, Liao et al. reports that simultaneous knockdown of P27Kip1 with overexpression of Cyclin D can stimulate Muller glia to re-enter the cell cycle in the mouse retina. There is intense interest in reprogramming mammalian muller glia into a source for neurogenic progenitors, in the hopes that these cells could be a source for neuronal replacement in neurodegenerative diseases. Previous work in the field has shown ways in which mouse Muller glia can be neurogenically reprogrammed and these studies have shown cell cycle re-entry prior to neurogenesis. In other works, typically, the extent of glial proliferation is limited, and the authors of this study highlight the importance of stimulating large numbers of Muller glia to re-enter the cell cycle with the hopes they will differentiate into neurons. While the evidence for stimulating proliferation in this study is convincing, the evidence for neurogenesis in this study is not convincing or robust, suggesting that stimulating cell cycle-reentry may not be associated with increasing regeneration without another proneural stimulus.

Below are concerns and suggestions.

Intro:

(1) The authors cite past studies showing "direct conversion" of MG into neurons. However, these studies (PMID: 34686336; 36417510) show EdU+ MG-derived neurons suggesting cell cycle re-entry does occur in these strategies of proneural TF overexpression.

We thank the reviewer for pointing this out. We will revise the statement to "MG neurogenesis," which encompasses both direct conversion and Müller glia proliferation followed by neuronal differentiation.

(2) Multiple citations are incorrectly listed, using the authors first name only (i.e. Yumi, et al; Levi, et al;). Studies are also incompletely referenced in the references.

We apologize for the mistake with the reference. We will fix these mistakes in the revised version.

Figure 1:

(3) When are these experiments ending? On Figure 1B it says "analysis" on the end of the paradigm without an actual day associated with this. This is the case for many later figures too. The authors should update the paradigms to accurately reflect experimental end points.

We thank the reviewer for highlighting the lack of clarity in our experimental design. We will label all experiment timelines in the figures where appropriate in the revised version.

(4) Are there better representative pictures between P27kd and CyclinD OE, the EdU+ counts say there is a 3 fold increase between Figure 1D&E, however the pictures do not reflect this. In fact, most of the Edu+ cells in Figure 1E don't seem to be Sox9+ MG but rather horizontally oriented nuclei in the OPL that are likely microglia.

Thanks to the reviewer for pointing this out. We will replace the image of Cyclin D1 which a better representative image.

(5) Is the infection efficacy of these viruses different between different combinations (i.e. CyclinD OE vs. P27kd vs. control vs. CCA combo)? As the counts are shown in Figure 1G only Sox9+/Edu+ cells are shown not divided by virus efficacy. If these are absolute counts blind to where the virus is and how many cells the virus hits, if the virus efficacy varies in efficiency this could drive absolute differences that aren't actually biological.

Because the AAV-GFAP-Cyclin D1 and AAV-GFAP-Cyclin D1-p27kip1 shRNA viruses do not carry a fluorescent reporter gene, we cannot easily measure viral efficacy in the same experiment. We believe that variations in viral efficacy cannot account for the significant differences in MG proliferation for two reasons: 1) We injected the same titer for all three viruses, and 2) Viral infection efficacy is very high, approaching 100% in the central retina. Nonetheless, to rule out the possibility that the differences in MG proliferation among the Cyclin D overexpression, p27kip1 knockdown, and CCA groups are due to variations in viral efficacy, we will include the p27kip1 knockdown and Cyclin D1 overexpression efficiencies for all four groups using qPCR and/or Western blot analysis in the revised manuscript.

(6) According to the Jax laboratories, mice aren't considered aged until they are over 18months old. While it is interesting that CCA treatment does not seem to lose efficacy over maturation I would rephrase the findings as the experiment does not test this virus in aged retinas.

Thank you to the reviewer for bringing this to our attention. We will void using “aged mice” in our revised manuscript.

(7) Supplemental Figure 2c-d. These viruses do not hit 100% of MG, however 100% of the P27Kip staining is gone in the P27sh1 treatment, even the P27+ cell in the GCL that is likely an astrocyte has no staining in the shRNA 1 picture. Why is this?

For Supplementary Figure 2c-d, we focused on the central area where knockdown efficiency was high, approaching 100%. We will replace this image with one that includes both high and low Müller glia transduction efficiency regions, clearly demonstrating the complete loss of p27kip1 staining in the area of high transduction efficiency.

Figure 2

(8) Would you expect cells to go through two rounds of cell cycle in such a short time? The treatment of giving Edu then BrdU 24 hours later would have to catch a cell going through two rounds of division in a very short amount of time. Again the end point should be added graphically to this figure.

We thank the reviewer for raising this important point. While the typical cell cycle time for human cells is approximately 24 hours, we hypothesized that 24 hours would be the most likely timepoint to capture cells continuously progressing through the cell cycle. However, we acknowledge that we cannot exclude the possibility of some cells entering a second cell cycle at much later timepoints.

In the revised manuscript, we will carefully qualify our conclusion to state that the majority of MG do not immediately undergo another cell division, rather than making a definitive statement. This more cautious phrasing will better reflect the limitations of the 24-hour timepoint and allow for the potential of a small subset of cells proceeding through additional rounds of division at later stages.

Figure 3

(9) I am confused by the mixing of ratios of viruses to indicate infection success. I know mixtures of viruses containing CCA or control GFP or a control LacZ was injected. Was the idea to probe for GFP or LacZ in the single cell data to see which cells were infected but not treated? This is not shown anywhere?

The virus infection was not uniform across the entire retina. To mark the infection hotspots, we added 10% GFP virus to the mixture. Regions of the retina with low infection efficiency were removed by dissection and excluded from the scRNA-seq analysis. We apologize for not clearly explaining this methodological detail in the original text, and will update the Methods section accordingly.

(10) The majority of glia sorted from TdTomato are probably not infected with virus. Can you subset cells that were infected only for analysis? Otherwise it makes it very hard to make population judgements like Figure 3E-H if a large portion are basically WT glia.

This question is related to the last one. Since the regions with high virus infection efficiency were selectively dissected and isolated for analysis, the percentage of CCA-infected MG should constitute the majority in the scRNA-seq data.

(11) Figure 3C you can see Rho is expressed everywhere which is common in studies like this because the ambient RNA is so high. This makes it very hard to talk about "Rod-like" MG as this is probably an artifact from the technique. Most all scRNA-seq studies from MG-reprogramming have shown clusters of "rods" with MG hybrid gene expression and these had in the past just been considered an artifact.

We agree that the low levels of Rho in other MG clusters (such as quiescent, reactivated, and proliferating MG) are likely due to RNA contamination. However, the level of Rho in the rod-like MG is significantly higher than in the other clusters, indicating that this is unlikely to be solely due to contamination.

As shown in Supplementary Figure 7A-C, a cluster of MG-rod hybrid cells (cluster C4) was present in all three experimental groups at similar ratios, and this hybrid cluster was excluded from further analysis. In contrast, the rod-like Müller glia (cluster C3) were predominantly found in the CCA and CCANT groups, suggesting a genuine response to CCA treatment.

Furthermore, we will conduct Rho and Gnat1 RNA in situ hybridization on the dissociated retinal cells to further support the conclusion that rod-specific genes are upregulated in a subset of MG in the revised manuscript.

(12) It is mentioned the "glial" signature is downregulated in response to CCA treatment. Where is this shown convincingly? Figure H has a feature plot of Glul , which is not clear it is changed between treatments. Otherwise MG genes are shown as a function of cluster not treatment.

We will add box plots of several MG-specific genes to better illustrate the downregulation of the glial signature in the relevant cell cluster in the revised manuscript.

Figure 4

(13) The authors should be commended for being very careful in their interpretations. They employ the proper controls (Er-Cre lineage tracing/EdU-pulse chasing/scRNA-seq omics) and were very careful to attempt to see MG-derived rods. This makes the conclusion from the FISH perplexing. The few puncta dots of Rho and GNAT in MG are not convincing to this reviewer, Rho and GNAT dots are dense everywhere throughout the ONL and if you drew any random circle in the ONL it would be full of dots. The rigor of these counts also comes into question because some dots are picked up in MG in the INL even in the control case. This is confusing because baseline healthy MG do not express RNA-transcripts of these Rod genes so what is this picking up? Taken together, the conclusion that there are Rod-like MG are based off scRNA-seq data (which is likely ambient contamination) and these FISH images. I don't think this data warrants the conclusion that MG upregulate Rod genes in response to CCA.

We performed RNA in situ hybridization on retinal sections because we aimed to correlate cell localization with rod gene expression. We understand the reviewer’s concern that the punctate signals of Rho and GNAT1 in the ONL MG may actually originate from neighboring rods. In the revised manuscript, we will conduct RNAscope on dissociated retinal cells to avoid this issue.

Figure 5

(14) Similar point to above but this Glul probe seems odd, why is it throughout the ONL but completely dark through the IPL, this should also be in astrocytes can you see it in the GCL? These retinas look cropped at the INL where below is completely black. The whole retinal section should be shown. Antibodies exist to GS that work in mouse along with many other MG genes, IHC or western blots could be done to better serve this point.

Indeed, the GCL was cropped out in Figure 5 A-B. We have other images with all retinal layers, which we will use in the revised manuscript. Additionally, we will perform the GS antibody staining to demonstrate partial MG dedifferentiation following CCA treatment.

Figure 6

(15) Figure 6D is not a co-labeled OTX2+/ TdTomato+ cell, Otx2 will fill out the whole nucleus as can be seen with examples from other MG-reprogramming papers in the field (Hoang, et al. 2020; Todd, et al. 2020; Palazzo, et al. 2022). You can clearly see in the example in Figure 6D the nucleus extending way beyond Otx2 expression as it is probably overlapping in space. Other examples should be shown, however, considering less than 1% of cells were putatively Otx2+, the safer interpretation is that these cells are not differentiating into neurons. At least 99.5% are not.

We have additional examples of Otx2+ Tdt+ Edu+ cells, which suggest that MG neurogenesis to Otx2+ cells does occur, despite the low efficiency. We will include these images in the revised manuscript.

(16) Same as above Figure 6I is not convincingly co-labeled HuC/D is an RNA-binding protein and unfortunately is not always the clearest stain but this looks like background haze in the INL overlapping. Other amacrine markers could be tested, but again due to the very low numbers, I think no neurogenesis is occurring.

We have additional examples of HuC/D+ Tdt+ Edu+ cells, which we will show in the revised manuscript.

(17) In the text the authors are accidently referring to Figure 6 as Figure 7.

We thank the reviewer for pointing out the mistake. We will correct the mistake in the revised manuscript.

Figure 7

(18) I like this figure and the concept that you can have additional MG proliferating without destroying the retina or compromising vision. This is reminiscent of the chick MG reprogramming studies in which MG proliferate in large numbers and often do not differentiate into neurons yet still persist de-laminated for long time points.

General:

(19) The title should be changed, as I don't believe there is any convincing evidence of regeneration of neurons. Understanding the barriers to MG cell-cycle re-entry are important and I believe the authors did a good job in that respect, however it is an oversell to report regeneration of neurons from this data.

We thank the reviewer for the suggestion. We will consider changing the title in the revised manuscript.

(20) This paper uses multiple mouse lines and it is often confusing when the text and figures switch between models. I think it would be helpful to readers if the mouse strain was added to graphical paradigms in each figure when a different mouse line is employed.

We will label the mouse lines used in each experiment in the figures where appropriate.

Author response:

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

eLife assessment

Shore et al. report important effects of a heterozygous mutation in the KCNT1 potassium channel on ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of KCNT1-Y777H mice. The authors provide solid evidence of physiological differences between this heterozygous mutation and their previous work with homozygotes. The reviewers appreciated the inclusion of recordings in ex vivo slices and dissociated cortical neurons, as well as the additional evidence showing an increase in persistent sodium currents (INaP) in parvalbumin-positive interneurons in heterozygotes. However, they were unclear regarding the likelihood of the increased sodium influx through INaP channels increasing sodium-activated potassium currents in these neurons.

Regarding the last sentence of the eLife assessment, we’ve added a new paragraph to the Discussion section of the paper to address this concern. Please see the response to comment 1B of Reviewer #1 below for more details. We feel that the question of whether an increase in INaP would further increase KCNT1 activity is a valid discussion point but not a limitation of the importance or rigor of the work itself.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript reports the effects of a heterozygous mutation in the KCNT1 potassium channels on the properties of ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of mice expressing KCNT1-Y777H. In humans, this mutation as well as multiple other heterozygotic mutations produce very severe early-onset seizures and produce a major disruption of all intellectual function. In contrast, in mice, this heterozygous mutation appears to have no behavioral phenotype or any increased propensity to seizures. A relevant phenotype is, however, evident in mice with the homozygous mutation, and the authors have previously published the results of similar experiments with the homozygotes. As perhaps expected, the neuronal effects of the heterozygous mutation presented in this manuscript are generally similar but markedly smaller than the previously published findings on homozygotes. There are, however, some interesting differences, particularly on PV+ interneurons, which appear to be more excitable than wild type in the heterozygotes but more excitable in the heterozygotes. This raises the interesting question, which has been explicitly discussed by the authors in the revised manuscript, as to whether the reported changes represent homeostatic events that suppress the seizure phenotype in the mouse heterozygotes or simply changes in excitability that do not reach the threshold for behavioral outcomes.

Strengths and Weaknesses:

(1) The authors find that the heterozygous mutation in PV+ interneurons increases their excitability, a result that is opposite from their previous observation in neurons with the corresponding homozygous mutation. They propose that this results from the selective upregulation of a persistent sodium current INaP in the PV+ interneurons. These observations are very interesting ones, and they raised some issues in the original submission:

A) The protocol for measuring the INaP current could potentially lead to results that could be (mis)interpreted in different ways in different cells. First, neither K currents nor Ca currents are blocked in these experiments. Instead, TTX is applied to the cells relatively rapidly (within 1 second) and the ramp protocol is applied immediately thereafter. It is stated that, at this time, Na currents and INaP are fully blocked but that any effects on Na-activated K currents are minimal. In theory this would allow the pre- to post- difference current to represent a relatively uncontaminated INaP. This would, however, only work if activation of KNa currents following Na entry is very slow, taking many seconds. A good deal of literature has suggested that the kinetics of activation of KNa currents by Na influx vary substantially between cell types, such that single action potentials and single excitatory synaptic events rapidly evoke KNa currents in some cell types. This is, of course, much faster than the time of TTX application. Most importantly, the kinetics of KNa activation may be different in different neuronal types, which would lead to errors that could produce different estimates of INaP in PV+ interneurons vs other cell types.

In their revised manuscript, the authors have provided good data demonstrating that, at least for the PV and SST neurons, loss of KNa currents after TTX application is slow relative to the time course of loss of INaP, justifying the use of this protocol for these neuronal types.

B) As the authors recognize, INaP current provides a major source of cytoplasmic sodium ions for the activation. An expected outcome of increased INaP is, therefore, further activation of KNa currents, rather than a compensatory increase in an inward current that counteracts the increase in KNa currents, as is suggested in the discussion.

The authors comment in the rebuttal that, despite the fact that sodium entry through INaP is known to activate KNa channels, an increase in INaP does not necessarily imply increased KNa current. This issue should be addressed directly somewhere in the text, perhaps most appropriately in the discussion.

We’ve added the following new paragraph to the Discussion section of the manuscript to address this concern:

“As the persistent sodium current has been shown to act as a source of cytoplasmic sodium ions for KCNT1 channel activation in some neuron types (Hage & Salkoff, 2012), one might expect that the compensatory increase in INaP in YH-HET PV neurons would further increase, rather than counteract, KNa currents. Unfortunately, there is insufficient information on the relative locations of the INaP and KCNT1 channels, as well as the kinetics of sodium transfer to KCNT1 channels, among cortical neuron subtypes, and even less is known in the context of KCNT1 GOF neurons; thus, it is difficult to predict how alterations in one of these currents may affect the other. One plausible reason that increased INaP would not alter KNa currents in YH-HET PV neurons is that the particular sodium channels that are responsible for the increased INaP are not located within close proximity to the KCNT1 channels. Moreover, homeostatic mechanisms that modify the length and/or location of the sodium channel-enriched axon initial segment (AIS) in neurons in response to altered excitability are well described (Grubb & Burrone, 2010; Kuba et al., 2010); thus, it is possible that in YH-HET PV neurons, the length or location of the AIS is altered, leading to uncoupling of the sodium channels that are responsible for the increased INaP to the KCNT1 channels. Future studies will aim to further investigate potential mechanisms of neuron-type-specific alterations in NaP and KNa currents downstream of KCNT1 GOF.”  

C) The numerical simulations, in general, provide a very useful way to evaluate the significance of experimental findings. Nevertheless, while the in-silico modeling suggests that increases in INaP can increase firing rate in models of PV+ neurons, there is as yet insufficient information on the relative locations of the INaP channels and the kinetics of sodium transfer to KNa channels to evaluate the validity of this specific model.

The authors have now put in all of the appropriate caveats on this very nicely in the revised manuscript.

(2) The effects of the KCNT1 channel blocker VU170 on potassium currents are somewhat larger and different from those of TTX, suggesting that additional sources of sodium may contribute to activating KCNT1, as suggested by the authors. Because VU170 is, however, a novel pharmacological agent, it may be appropriate to make more careful statements on this. While the original published description of this compound reported no effect on a variety of other channels, there are many that were not tested, including Na and cation channels that are known to activate KCNT1, raising the possibility of off-target effects.

In the revised version, the authors have added more to the manuscript on this issue and have added a very clear discussion of this to the text (in the discussion section).

This is a very clear and thorough piece of work, and the authors are to be congratulated on this. My one remaining suggestion would be to make an explicit statement about whether increased sodium influx through INaP channels, which is thought to activate KNa channels, would be likely to increase KNa current in these neurons (see comment 1B).

Please see response to comment 1B.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shore et al. investigate the consequent changes in excitability and synaptic efficacy of diverse neuronal populations in an animal model of juvenile epilepsy. Using electrophysiological patch-clamp recordings from dissociated neuronal cultures, the authors find diverging changes in two major populations of inhibitory cell types, namely somatostatin (SST)- and parvalbumin (PV)-positive interneurons, in mice expressing a variant of the KCNT1 potassium channel. They further suggest that the differential effects are due to a compensatory increase in the persistent sodium current in PV interneurons in pharmacological and in silico experiments. It remains unclear why this current is selectively enhanced in PV-interneurons.

Strengths:

(1) Heterozygous KCNT1 gain of function variant was used which more accurately models the human disorder.

(2) The manuscript is clearly written, and the flow is easy to follow. The authors explicitly state the similarities and differences between the current findings and the previously published results in the homozygous KCNT1 gain of function variant.

(3) This study uses a variety of approaches including patch clamp recording, in silico modeling and pharmacology that together make the claims stronger.

(4) Pharmacological experiments are fraught with off-target effects and thus it bolsters the authors' claims when multiple channel blockers (TTX and VU170) are used to reconstruct the sodium-activated potassium current.

Weaknesses:

(1) This study mostly relies on recordings in dissociated cortical neurons. Although specific WT interneurons showed intrinsic membrane properties like those reported for acute brain slices, it is unclear whether the same will be true for those cells expressing KCNT1 variants, especially when the excitability changes are thought to arise from homeostatic compensatory mechanisms. The authors do confirm that mutant SST-interneurons are hypoexcitable using an ex vivo slice preparation which is consistent with work for other KCTN1 gain of function variants (e.g. Gertler et al., 2022). However, the key missing evidence is the excitability state of mutant PV-interneurons, given the discrepant result of reduced excitability of PV cells reported by Gertler et al in acute hippocampal slices.

Reviewer #3 (Public Review):

Summary:

The present manuscript by Shore et al. entitled Reduced GABAergic Neuron Excitability, Altered Synaptic Connectivity, and Seizures in a KCNT1 Gain-of-Function Mouse Model of Childhood Epilepsy" describes in vitro and in silico results obtained in cortical neurons from mice carrying the KCNT1-Y777H gain-of-function (GOF) variant in the KCNT1 gene encoding for a subunit of the Na+-activated K+ (KNa) channel. This variant corresponds to the human Y796H variant found in a family with Autosomal Dominant Nocturnal Frontal lobe epilepsy. The occurrence of GOF variants in potassium channel encoding genes is well known, and among potential pathophysiological mechanisms, impaired inhibition has been documented as responsible for KCNT1-related DEEs. Therefore, building on a previous study by the same group performed in homozygous KI animals, and considering that the largest majority of pathogenic KCNT1 variants in humans occur in heterozygosis, the Authors have investigated the effects of heterozygous Kcnt1-Y777H expression on KNa currents and neuronal physiology among cortical glutamatergic and the 3 main classes of GABAergic neurons, namely those expressing vasoactive intestinal polypeptide (VIP), somatostatin (SST), and parvalbumin (PV), crossing KCNT1-Y777H mice with PV-, SST- and PV-cre mouse lines, and recording from GABAergic neurons identified by their expression of mCherry (but negative for GFP used to mark excitatory neurons).

The results obtained revealed heterogeneous effects of the variant on KNa and action potential firing rates in distinct neuronal subpopulations, ranging from no change (glutamatergic and VIP GABAergic) to decreased excitability (SST GABAergic) to increased excitability (PV GABAergic). In particular, modelling and in vitro data revealed that an increase in persistent Na current occurring in PV neurons was sufficient to overcome the effects of KCNT1 GOF and cause an overall increase in AP generation.

Strengths:

The paper is very well written, the results clearly presented and interpreted, and the discussion focuses on the most relevant points.

The recordings performed in distinct neuronal subpopulations (both in primary neuronal cultures and, for some subpopulations, in cortical slices, are a clear strength of the paper. The finding that the same variant can cause opposite effects and trigger specific homeostatic mechanisms in distinct neuronal populations is very relevant for the field, as it narrows the existing gap between experimental models and clinical evidence.

Weaknesses:

My main concern regarding the epileptic phenotype of the heterozygous mice investigated has been clarified in the revision, where the infrequent occurrence of seizures is more clearly stated. Also, a more detailed statistical analysis of the modeled neurons has been added in the revision.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This is a very clear and thorough piece of work, and the authors are to be congratulated on this. My one remaining suggestion would be to make an explicit statement about whether increased sodium influx through INaP channels, which is thought to activate KNa channels, would be likely to increase KNa current in these neurons (see comment 1B).

Please see response to comment 1B.

Reviewer #2 (Recommendations For The Authors):

This revised manuscript is significantly improved and addresses most of my concerns. However, I would still recommend including the ex vivo slice recordings in mutant PV-interneurons as the authors proposed in their rebuttal. The I-V recordings using sequential TTX and VU170 blockade in WT SST and PV-interneurons that are provided in the rebuttal are interesting and may point to a preferential expression of persistent sodium currents in PV-interneurons normally. It would be helpful to readers as a supplemental figure.

As proposed in the rebuttal, we are currently recording PV neurons using ex vivo slice preparations from WT and Kcnt1-YH Het mice. We look forward to including those data in a future manuscript.

We agree with the reviewer that the differences in INaP between WT PV and SST neurons are notable. The data provided in the rebuttal were only from 5 neurons/group, and they were meant to illustrate a side-by-side comparison of TTX and VU170 subtraction methods to assess KNa currents. However, in Figure 7 of the manuscript, we performed more robust measurements of INaP and observed differences in the current between WT PV and SST neurons. Thus, we’ve added the following sentence to the Results section:

“Interestingly, the mean peak amplitude of INaP in WT PV neurons was 70% larger than that in WT SST neurons (-1.42 ± 0.16 vs. -0.85 ± 0.07 pA/pF; Fig. 7B and 7D), suggesting there may be differences in sodium channel expression, localization, or regulation inherent to each neuron type that confer their differential response to KCNT1 GOF.”

References

Grubb, M. S., & Burrone, J. (2010). Activity-dependent relocation of the axon initial segment fine-tunes neuronal excitability. Nature, 465(7301), 1070-1074. https://doi.org/10.1038/nature09160

Hage, T. A., & Salkoff, L. (2012). Sodium-activated potassium channels are functionally coupled to persistent sodium currents. J Neurosci, 32(8), 2714-2721. https://doi.org/10.1523/JNEUROSCI.5088-11.2012

Kuba, H., Oichi, Y., & Ohmori, H. (2010). Presynaptic activity regulates Na(+) channel distribution at the axon initial segment. Nature, 465(7301), 1075-1078. https://doi.org/10.1038/nature09087

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors show for the first time that deleting GLS from rod photoreceptors results in the rapid death of these cells. The death of photoreceptor cells could result from loss of synaptic activity because of a decrease in glutamate, as has been shown in neurons, changes in redox balance, or nutrient deprivation. 

Strengths: 

The strength of this manuscript is that the author shows a similar phenotype in the mice when Gls was knocked out early in rod development or the adult rod. They showed that rapid cell death is through apoptosis, and there is an increase in the expression of genes responsive to oxidative stress. 

We thank the reviewer for their time reviewing the manuscript and their comments regarding the potential mechanism(s) by which rod photoreceptors rapidly degenerate upon knockout of GLS.

Weaknesses: 

In this manuscript, the authors show a "metabolic dependency of photoreceptors on glutamine catabolism in vivo". However, there is a potential bias in their thinking that glutamine metabolism in rods is similar to cancer cells where it feeds into the TCA cycle. They should consider that as in neurons, GLS1 activity provides glutamate for synaptic transmission. The modest rescue shown by providing α-ketoglutarate in the drinking water suggests that glutamine isn't a key metabolic substrate for rods when glucose is plentiful. The ERG studies performed on the iCre-Glsflox/flox mice showed a large decrease in the scotopic b wave at saturating flashes which could indicate a decrease in glutamate at the rod synapse as stated by the authors. While EM micrographs of wt and iCre-Glsflox/flox mice were shown for the outer retina at p14, the synapse of the rods needs to be examined by EM. 

We agree with the reviewer that in the presence of sufficient glucose, it appears a lack of GLS-driven glutamine (Gln) catabolism does not drastically alter the levels of TCA cycle metabolites or mitochondrial function as we demonstrated in Figure 4, and supplementation with alpha-ketoglutarate improved outer nuclear layer thickness by only a small amount as observed in Figure 5e. Hence, as we stated in the Results and Discussion, at least in the mouse where Gls is selectively deleted from rod photoreceptors by crossing Glsfl/fl mice with Rho-Cre mice (Glsfl/fl; Rho-Cre+, cKO), Gln’s role in supporting the TCA cycle is not the major mechanism by which rod photoreceptors utilize Gln to suppress apoptosis.

With regards to GLS-driven Gln catabolism providing glutamate (Glu) for synaptic transmission, we again agree with the reviewer that Glu is an important excitatory neurotransmitter, but it is also a key metabolite necessary for the synthesis of glutathione, amino acids, and proteins. As noted and discussed at length in the manuscript, a lack of GLS-driven Gln catabolism in rod photoreceptors leads to reduced levels of oxidized glutathione (Figure 4D) possibly signaling an overall reduction in the biosynthesis of glutathione as Glu is directly and indirectly responsible for its synthesis. Furthermore, Gln and GLS-derived Glu play a central role in the biosynthesis of several nonessential amino acids and proteins. To this end, we see a reduction in the level of Glu, which is the product of the GLS reaction and further confirms the loss of GLS function. We also noted a significant decrease in aspartate (Asp), which can be constructed from the carbons and nitrogens of Gln as discussed at length in the manuscript (Figure 6A). Finally, we noted a significant decrease in global protein synthesis in the cKO retina as compared to the wild-type animal as well (Figure 6E). Therefore, the data suggest that GLS-driven Gln catabolism is critical for amino acid metabolism and protein synthesis and to some degree redox balance; although, the small but statistically significant changes in oxidized glutathione, NADP/NADPH, and redox gene expression may not fully account for the rapid and complete photoreceptor degeneration observed. Future studies are necessary to shed light on the role of redox imbalance in this novel transgenic mouse model.

Glu also plays a role in synaptic transmission, and we considered this scenario as described in Figure 1 – figure supplement 5. Here, the synaptic connectivity between photoreceptors and the inner retina did not demonstrate significant differences in the labeling of photoreceptor synaptic membranes in the outer plexiform layer nor alterations in the labeling of a key protein (Bassoon) in ribbon synapses. These data suggest that the synaptic connectivity between photoreceptors and second-order neurons was unaltered at P14 in the cKO retina, which is the time just prior to rapid photoreceptor degeneration. We agree, though, that to obtain greater insight into the alterations in the ribbon synapse, EM images can be examined. The EM images shown in Figure 1 – figure supplement 4 are from P21 and will be utilized to assess the ribbon synapse for the revised version of the article.

With regards to the ERG changes noted in Figure 2, we agree with the reviewer that a large decrease was noted in the scotopic b-wave at P21 and P42 in the cKO. However, an even larger reduction in the scotopic a-wave was noted at these ages as well. In animal models that disrupt photoreceptor synaptic function (Dick et al. Neuron. 2003; Johnson et al. J Neuroscience. 2007; Haeseleer et al. Nature Neuroscience. 2004; Chang et al. Vis Neurosci. 2006), a more negative ERG pattern is typically observed with the b-wave altered to a much larger degree than the a-wave. Additionally, in these models that disrupt photoreceptor synaptic transmission, the overall structure of the retina with respect to thickness is maintained (Dick et al. Neuron. 2003) or noted to have modest changes in the outer plexiform layer within the first two months of age with the outer nuclear layer not significantly altered until 8-10 months of age (Haeseleer et al. Nature Neuroscience. 2004). In contrast, a rapid decline in the outer nuclear layer thickness was observed in the cKO retina after P14 likely contributing to the ERG changes noted in Figure 2.  Also, Gln is catabolized to Glu primarily by GLS as suggested by the approximately 50% reduction in Glu levels in the cKO retina (Figure 6A), but other enzymes are also capable of catabolizing Gln to Glu, so Glu levels in the rod photoreceptors are unlikely to be zero. Coupling this with the fact that rods are equipped with a self-sufficient Glu recollecting system at their synaptic terminals (Hasegawa et al. Neuron. 2006; Winkler et al. Vis Neurosci. 1999) and that GLS activity is at least two-fold higher in the photoreceptor inner segments, which support energy production and metabolism, than any other layer in the retina (Ross et al. Brain Res. 1987) suggests that altered synaptic transmission secondary to reduced levels of Glu likely does not account in full for the rapid and robust photoreceptor degeneration observed in the cKO retina.

The authors note that the outer segments are shorter but they do not address whether there is a decrease in the number of cones. 

The number of cones will be assessed and provided in the revised version of the article.

Rod-specific Gls ko mice with an inducible promoter were generated by crossing the Pde6g-CreERT2 and homozygous for either the WT or floxed Gls allele (IND-cKO). In Figure 3 the authors document that by western blots and antibody labeling the GLS1 expression is lost in the IND-cKO 10 days post tamoxifen. OCT images show a decrease in the thickness of the outer nuclear layer between 17 and 38 days post-TAM. Ergs should be performed on the animals at 10 and 30 days post TAM, before and after major structural changes in rod photoreceptor cells, to determine if changes in light-stimulated responses are observed. These studies could help to parse out the cause of photoreceptor cell death. 

We agree with the reviewer that the IND-cKO is a useful tool to help parse out the cause of photoreceptor cell death in this model as well as shed light on the role of GLS-driven Gln catabolism in photoreceptor synaptic transmission as discussed at length above. Hence, ERG analyses will be provided for these animals in the revised version of the article.

The studies in Figure 4 were all performed on iCre-Glsflox/flox and control mice at p14, why weren't the IND-cKO mice used for these studies since the findings would not be confounded by development? 

To gain further insight into the role of GLS-driven Gln catabolism in the maintenance of rod photoreceptors as compared to their development/maturation, we will provide ERG and targeted metabolomic analyses of the IND-cKO retina in the revised version of the article.

In all rescue studies, the endpoint was an ONL thickness, which only addressed rod cell death. The authors should also determine whether there are small improvements in the ERG, which would distinguish the role of GLS in preventing oxidative stress. 

Optical coherence tomography (OCT) provides a sensitive in vivo method to detect small changes in retinal thickness without potential artifacts incurred through histological processing. Considering the Gls cKO retina demonstrates significant and rapid photoreceptor degeneration, we wanted to assess pathways that may be critical to photoreceptor survival downstream of GLS-driven Gln catabolism using rescue experiments with pharmacologic treatment or metabolite supplementation. That said, disruption of GLS-driven Gln catabolism may also significantly alter rod photoreceptor function beyond that which is secondary to photoreceptor cell death. As such, changes in ERG will be examined and provided in the revised version of the article for certain rescue experiments that demonstrated a robust change in ONL thickness.

Reviewer #2 (Public Review): 

Summary: 

Photoreceptor neurons are crucial for vision, and discovering pathways necessary for photoreceptor health and survival can open new avenues for therapeutics. Studies have shown that metabolic dysfunction can cause photoreceptor degeneration and vision loss, but the metabolic pathways maintaining photoreceptor health are not well understood. This is a fundamental study that shows that glutamine catabolism is critical for photoreceptor cell health using in vivo model systems. 

Strengths: 

The data are compelling, and the consideration of potential confounding factors (such as glutaminase 2 expression) and additional experiments to examine the synaptic connectivity and inner retina added strength to this work. The authors were also careful not to overstate their claims, but to provide solid conclusions that fit the results and data provided in their study. The findings linking asparagine supplementation and the inhibition of the integrated stress response to glutamine catabolism within the rod photoreceptor cell are intriguing and innovative. Overall, the authors provide convincing data to highlight that photoreceptors utilize various fuel sources to meet their metabolic needs, and that glutamine is critical to these cells for their biomass, redox balance, function, and survival. 

We greatly appreciate the reviewer’s thoughtful comments and time spent reviewing this manuscript.

Weaknesses: 

Recent studies have explored the metabolic "crosstalk" that exists within the mammalian retina, where metabolites are transferred between the various retinal cells and the retinal pigment epithelium. It would be of interest to test whether the conditional knockout mice have changes in metabolism (via qPCR such as shown in Figure 4 - Supplemental Figure 1) within the retinal pigment epithelium that may be contributing to the authors' findings in the neural retina. Additionally, the authors have very compelling data to show that inhibition of eIF2a or supplementation with asparagine can delay photoreceptor death via OCT measurements in their conditional knockout mouse model (Figure 6G, H). However, does inhibition of eIF2a or asparagine adversely impact the WT retina? It would also be impactful to know whether this has a prolonged effect, or if it is short-term, as this would provide strength to potential therapeutic targeting of these pathways to maintain photoreceptor health. 

We agree with the reviewer that metabolic communication in the outer retina is crucial to the function and survival of both photoreceptors and RPE. We will perform qRT-PCR on the eyecups of these mice to assess any changes in the expression of metabolic genes. This data will be provided in the revised manuscript.

We have data demonstrating systemic treatment with ISRIB does not adversely impact the anatomy of the wild-type retina; this data will be included in the revised manuscript as a supplement to Figure 6. Additionally, we have recent data to suggest that the effect of ISRIB extends beyond P21 in the cKO mouse. This data will be included in the revised manuscript.

Reviewer #3 (Public Review): 

Summary: 

The authors explored the role of GLS, a glutaminase, which is an enzyme that catalyzes the conversion of glutamine to glutamate, in rod photoreceptor function and survival. The loss of GLS was found to cause rapid autonomous death of rod photoreceptors. 

Strengths: 

Interesting and novel phenotype. Two types of cre-lines were rigorously used to knockout the Gls gene in rods. Both of the conditional knockouts led to a similar phenotype, i.e. rod death. Histology and ERG were carefully done to characterize the loss of rods over specific ages. A necessary metabolomic study was performed and appreciated. Some rescue experiments were performed and revealed possible mechanisms. 

We thank the reviewer for their comments and appreciation of the methods utilized herein to address the role of GLS-driven Gln catabolism in rod photoreceptors.

Weaknesses: 

No major weaknesses were identified. The mechanism of GLS-loss-induced rod death seems not fully elucidated by this study but could be followed up in the future, and the same for GLS's role in cones.

We agree with the reviewer that the downstream metabolic and molecular mechanisms by which Gln catabolism impacts rod photoreceptor health are not fully elucidated. Defining these mechanisms will advance our understanding of photoreceptor metabolism and identify therapeutic targets promoting photoreceptor resistance to stress. Future studies are underway to uncover these mechanisms. Additionally, while outside the scope of the current manuscript, we have generated mice lacking GLS in cone photoreceptors specifically and are currently elucidating the role of GLS in cone photoreceptor metabolism, function, and survival. These results will be published in a separate manuscript.

Author response:

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

Response to reviewers

A general comment was that this study left several key questions unanswered, in particular the causal mechanism for the reported ribosomal distributions.  We have been interested in the evolution of asymmetric bacterial growth and aging for many years. However, a motivational difference is that we are more interested in the evolutionary process, and evolution by natural selection works on the phenotype.  Thus, we wanted to start with the phenotype closest to fitness, appropriately defined for the conditions, work downwards.  We examined first the asymmetry of elongation rates in single cells, then gene products, and now ribosomes.  As we have pointed out, our demonstration of ribosomal asymmetry shows that the phenomenon was not peculiar and unique to the gene products we examined.  Rather, the asymmetry is acting higher up in the metabolic network and likely affecting all genes.  We find such conceptual guidance to be important.  In the ideal world, of course we would have liked to have worked out the causal mechanisms in one swoop.  In a less than ideal situation, it is a subjective decision as where to stop.  We believe that the publication of this manuscript is more than appropriate at this juncture.  We work at the interface of evolutionary theory and microbiology.  Our results could appeal to both fields.  If we attract new researchers, progress could be accelerated.  Could the delay caused by publishing only completed stories slow the rate of discovery?  These questions are likely as old as science (e.g., https://telliamedrevisited.wordpress.com/2021/01/28/how-not-to-write-a-response-to-reviewers/).

We present below our response to specific comments by reviewers.  We have not added a new discussion of papers suggested by Reviewer #1 because we feel that the speculations would have been too unfocused.  We were already criticized for speculation in the Discussion about a link between aggregate size and ribosomal density.

Respond to Major comments by Reviewer #1.

a) Fig. 1 only shows 2 divisions (rather than 3 as per Rev1) to avoid an overly elaborate figure.  We have added text to the figure legend that the old and new poles and daughters in the subsequent 3, 4, 5, 6, and 7 generations can be determined by following the same notations and tracking we presented for generations 1 and 2 in Fig. 1.  For example, if we know the old and new poles of any of the four daughters after 2 divisions (as in Fig. 1), and allow that daughter to elongate, become a mother, and divide to produce 2 “grand-daughters”, the polarity of the grand-daughters can also be determined.

b) Because division times were normalized and analyzed as quartiles, the raw values were never used.  Rather than annotating unused values, we have provided the mean division times in the Material and Methods section on normalization to provide representative values.

c) We did not quantify in our study the changes over generations for three reasons.  First, the sample sizes for the first generations (cohorts of 1, 2, 4, and 8 cells) are statistically small.  Second, and most importantly, cells on an agar pad in a microscope slide, despite being inoculated as fresh exponentially growing cells, experience a growth lag, as all cells transferred to a new physiological condition.  Thus, to be safe, we do not collect data from cohorts 1, 2, 4, and 8 to ensure that our cells are as much as possible physiologically uniform.  Lastly, as we noted in the Material and Methods they also slow down after 7 generations (128 cells).  Thus, we have collected ribosome and length measurements primarily from cohorts 16, 32, 64, and 128.  Measurable cells from the 128 cohort are actually rare because a colony with that many cells often starts to form double layers, which are not measurable.  Most of our measurements came from the 16, 32, and 64 cohorts, in which case a time series would not be meaningful.  Some of these details were not included in our manuscript but have been added to the Material and Methods (Microscopy and time-lapse movies).  For these reasons we have not added a time series as requested by the reviewer.

d) We have added the additional figure as requested, but as a supplement rather than in the main article (Supplemental Materials Fig. S1).  This figure showed the normalized density of ribosomes along the normalized length of old and new daughters.  The density was continuous rather than quartiles.  This figure was included in the original manuscript, but readers recommended that it be removed because the all the analyzed data had been done with quartiles.  Readers felt mislead and confused.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study presents careful biochemical experiments to understand the relationship between LRRK2 GTP hydrolysis parameters and LRRK2 kinase activity. The authors report that incubation of LRRK2 with ATP increases the KM for GTP and decreases the kcat. From this they suppose an autophosphorylation process is responsible for enzyme inhibition. LRRK2 T1343A showed no change, consistent with it needing to be phosphorylated to explain the changes in G-domain properties. The authors propose that phosphorylation of T1343 inhibits kinase activity and influences monomer-dimer transitions.

Strengths:

Strengths of the work are the very careful biochemical analyses and interesting result for wild type LRRK2.

Weaknesses:

The conclusions related to involvement of a monomer-dimer transition are to this reviewer, premature and an independent method needs to be utilized to bolster this aspect of the story.

The monomer-dimer transition has been described in detail in our recent preprint Guaitoli et al., 2023 (doi: 10.1101/2023.08.11.549911). Where we in addition to mass-photometry have used blue-native page. Furthermore, to better elucidate the mechanistic impact of the phosphorylation, we have provided AlphaFold3 models. As the new AlphaFold version allows to consider PTMs as well as small molecules, we compared the models of the GDP vs the GTP-state of pT1343 LRRK2. Interestingly, the AF3 model suggests, that the phosphate of the pT1343 is orientated inwards thereby substituting the gamma phosphate (see Supplementary Figure 5). This finding is in well agreement with MD simulations published recently (Stormer et al., 2023, doi: 10.1042/BCJ20230126). As we are determining GTP hydrolysis in a multi turnover situation, the pT1343 might hamper the hydrolysis by competing with GTP re-binding. Final models have been deposited on Zenodo (https://doi.org/10.5281/zenodo.11242230).

Reviewer #2 (Public Review):

As discussed in the original review, this manuscript is an important contribution to a mechanistic understanding of LRRK2 kinase. Kinetic parameters for the GTPase activity of the ROC domain have been determined in the absence/presence of kinase activity. A feedback mechanism from the kinase domain to GTP/GDP hydrolysis by the ROC domain is convincingly demonstrated through these kinetic analyses. However, a regulatory mechanism directly linking the T1343 phosphosite and a monomer/dimer equilibrium is not fully supported. The T1343A mutant has reduced catalytic activity and can form similar levels of dimer as WT. The revised manuscript does point out that other regulatory mechanisms can also play a role in kinase activity and GTP/GDP hydrolysis (Discussion section). The environmental context in cells cannot be captured from the kinetic assays performed in this manuscript, and the introduction contains some citations regarding these regulatory factors. This is not a criticism, the detailed kinetics here are rigorous, but it is simply a limitation of the approach. Caveats concerning effects of membrane localization, Rab/14-3-3 proteins, WD40 domain oligomers, etc... should be given more prominence than a brief (and vague) allusion to 'allosteric targeting' near the end of the Discussion.

We thank the reviewer for the evaluation of the manuscript and suggestions made. With respect to the mentioned caveats regarding the complex regulation of LRRK2 in its native cellular environment by effectors, localization and effector binding, we have revised the discussion, accordingly. We nevertheless, want to emphasize that the phospho-null mutant T1343A leads to an increase in Rab10 phosphorylation in cells, demonstrating a relevance of this regulatory mechanism under near physiological conditions (shown in Figure 6). In addition, to further elucidate the molecular mechanisms of the p-loop phosphorylation at T1343, we have performed AlphaFold3 modelling allowing to include phosphoresidues (see comment above, Supplemental Figure 5).

Specific comments

(1) The revised version is better organized with respect to the significance of monomer/dimer equilibrium and the relevance of the GTP-binding region of ROC domain that encompasses the T1343 phospho-site. The relevance of monomers/dimers of LRRK2 from previous studies is better articulated and readers are able to follow the reasoning for the various mutations.

We thank the reviewer for the positive feedback. 

(2) As a suggestion I would change the following on page 6 to clarify for readers: "...would show no change in kcat and KM values upon in vitro ATP treatment" to:

"...would show no change in kcat and KM values for GTP hydrolysis upon in vitro

ATP treatment"

(3) The levels of dimer in WT (+ATP) and T1343A (+/- ATP) are the same, about 40-45%. These data are cited when the authors state that ATP-induced monomerization is 'abolished' (page 6). My suggestion is to re-phrase this conclusion for consistency with data (Fig 5). For example, one can state that 'ATP incubation does not affect the percentage of dimer for the T1343A variant of LRRK2'. This would be similar to the authors' description of these data on page 8 - 'no difference in dimer formation upon ATP treatment'.

We thank the reviewer for the suggestions. We revised the manuscript accordingly. Changes have been highlighted in the version provided for reviewing purposes.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Minor revisions

-change 'Although functional work on LRRK2 has been made significant progress...' to 'Although there is significant progress toward functional characterization of LRRK2...'

-change 'exact mechanisms' to 'precise mechanisms', and similarly 'exact interplay' to 'precise interplay'

-change 'On a contrary' to 'On the contrary' in Discussion

-change remained to be unchanged' to 'remains unchanged', page 8

We thank the reviewer for having noticed this. We have revised the manuscript accordingly.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, the researchers aimed to address whether bees causally understand string-pulling through a series of experiments. I first briefly summarize what they did:

- In experiment 1, the researchers trained bees without string and then presented them with flowers in the test phase that either had connected or disconnected strings, to determine what their preference was without any training. Bees did not show any preference.

- In experiment 2, bees were trained to have experience with string and then tested on their choice between connected vs. disconnected string.

- experiment 3 was similar except that instead of having one option which was an attached string broken in the middle, the string was completely disconnected from the flower.

- In experiment 4, bees were trained on green strings and tested on white strings to determine if they generalize across color.

- In experiment 5, bees were trained on blue strings and tested on white strings.

- In experiment 6, bees were trained where black tape covered the area between the string and the flower (i.e. so they would not be able to see/ learn whether it was connected or disconnected).

- In experiments 2-6, bees chose the connected string in the test phase.

- In experiment 7, bees were trained as in experiment 3 and then tested where the string was either disconnected or coiled i.e. still being 'functional' but appearing different.

- In experiment 8, bees were trained as before and then tested on a string that was in a different coiled orientation, either connected or disconnected.

- In experiments 7 and 8 the bees showed no preference.

Strengths:

I appreciate the amount of work that has gone into this study and think it contains a nice, thorough set of experiments. I enjoyed reading the paper and felt that overall it was well-written and clear. I think experiment 1 shows that bees do not have an untrained understanding of the function of the string in this context. The rest of the experiments indicate that with training, bees have a preference for unbroken over broken string and likely use visual cues learned during training to make this choice. They also show that as in other contexts, bees readily generalize across different colors.

Weaknesses:

(1) I think there are 2 key pieces of information that can be taken from the test phase - the bees' first choice and then their behavior across the whole test. I think the first choice is critical in terms of what the bee has learned from the training phase - then their behavior from this point is informed by the feedback they obtain during the test phase. I think both pieces of information are worth considering, but their behavior across the entire test phase is giving different information than their first choice, and this distinction could be made more explicit. In addition, while the bees' first choice is reported, no statistics are presented for their preferences.

We agree with the reviewer that the first choice is critical in terms of what the bumblebees have learned from the training phase. We analyzed the bees’ first choice in Table 1, and we added the tested videos. The entire connected and disconnected strings were glued to the floor, the bees were unable to move either the connected or disconnected strings, and avoid learning behavior during the tests. We added the data of bee's each choice in the Supplementary table.

(2) It seemed to me that the bees might not only be using visual feedback but also motor feedback. This would not explain their behavior in the first test choice, but could explain some of their subsequent behavior. For example, bees might learn during training that there is some friction/weight associated with pulling the string, but in cases where the string is separated from the flower, this would presumably feel different to the bee in terms of the physical feedback it is receiving. I'd be interested to see some of these test videos (perhaps these could be shared as supplementary material, in addition to the training videos already uploaded), to see what the bees' behavior looks like after they attempt to pull a disconnected string.

We added supplementary videos of testing phase. As noted in General Methods, both connected and disconnected strings were glued to the floor to prevent the air flow generated by flying bumblebees’ wings from changing the position of the string during the testing phase. The bees were unable to move either the connected or disconnected strings during the tests, and only attempted to pull them. Therefore, the difference in the friction/weight of pulling the both strings cannot be a factor in the test.

(3) I think the statistics section needs to be made clearer (more in private comments).

We changed the statistical analysis section as suggested by the reviewer.

(4) I think the paper would be made stronger by considering the natural context in which the bee performs this behavior. Bees manipulate flowers in all kinds of contexts and scrabble with their legs to achieve nectar rewards. Rather than thinking that it is pulling a string, my guess would be that the bee learns that a particular motor pattern within their usual foraging repertoire (scrabbling with legs), leads to a reward. I don't think this makes the behavior any less interesting - in fact, I think considering the behavior through an ecological lens can help make better sense of it.

Here we respectfully disagree. The solving of Rubik’s cube by humans could be said to be version of finger-movements naturally required to open nuts or remove ticks from fur, but this is somewhat beside the point: it’s not the motor sequences that are of interest, but the cognition involved. A general approach in work on animal intelligence and cognition is to deliberately choose paradigms that are outside the animals’ daily routines-this is what we have done here, in asking whether there is means-end comprehension in bee problem solving. Like comparable studies on this question in other animals, the experiments are designed to probe this question, not one of ecological validity.

Reviewer #2 (Public Review):

Summary:

The authors wanted to see if bumblebees could succeed in the string-pulling paradigm with broken strings. They found that bumblebees can learn to pull strings and that they have a preference to pull on intact strings vs broken ones. The authors conclude that bumblebees use image matching to complete the string-pulling task.

Strengths:

The study has an excellent experimental design and contributes to our understanding of what information bumblebees use to solve a string-pulling task.

Weaknesses:

Overall, I think the manuscript is good, but it is missing some context. Why do bumblebees rely on image matching rather than causal reasoning? Could it have something to do with their ecology? And how is the task relevant for bumblebees in the wild? Does the test translate to any real-life situations? Is pulling a natural behaviour that bees do? Does image matching have adaptive significance?

We appreciate the valuable comment from the reviewer. Our explanation, which we have now added to the manuscript, is as follows:

“Different flower species offer varying profitability in terms of nectar and pollen to bumblebees; they need to make careful choices and learn to use floral cues to predict rewards (Chittka, 2017). Bumblebees can easily learn visual patterns and shapes of flower (Meyer-Rochow, 2019); they can detect stimuli and discriminate between differently coloured stimuli when presented as briefly as 25 ms (Nityananda et al., 2014). In contrast, causal reasoning involves understanding and responding to causal relationships. Bumblebees might favor, or be limited to, a visual approach, likely due to the efficiency and simplicity of processing visual cues to solve the string-pulling task. ”

As above, it worth noting that our work is not designed as an ecological study, but one about the question of whether causal reasoning can explain how bees solve a string-pulling puzzle. We have a cognitive focus, in line with comparable studies on other animals. We deliberately chose a paradigm that is to some extent outside of the daily challenges of the animal.

Reviewer #3 (Public Review):

Summary:

This paper presents bees with varying levels of experience with a choice task where bees have to choose to pull either a connected or unconnected string, each attached to a yellow flower containing sugar water. Bees without experience of string pulling did not choose the connected string above chance (experiment 1), but with experience of horizontal string pulling (as in the right-hand panel of Figure 4) bees did choose the connected string above chance (experiments 2-3), even when the string colour changed between training and test (experiments 4-5). Bees that were not provided with perceptual-motor feedback (i.e they could not observe that each pull of the string moved the flower) during training still learned to string pull and then chose the connected string option above chance (experiment 6). Bees with normal experience of string pulling then failed to discriminate between connected and unconnected strings when the strings were coiled or looped, rather than presented straight (experiments 7-8).

Weaknesses:

The authors have only provided video of some of the conditions where the bees succeeded. In general, I think a video explaining each condition and then showing a clip of a typical performance would make it much easier to follow the study designs for scholars. Videos of the conditions bees failed at would be highly useful in order to compare different hypotheses for how the bees are solving this problem. I also think it is highly important to code the videos for switching behaviours. When solving the connected vs unconnected string tasks, when bees were observed pulling the unconnected string, did they quickly switch to the other string? Or did they continue to pull the wrong string? This would help discriminate the use of perceptual-motor feedback from other hypotheses.

We added the test videos as suggested by the reviewer, and we added the data for each bee's choice. However, both connected and disconnected strings were glued to the floor, and therefore perceptual-motor feedback was equal and irrelevant between the choices during the test.

The experiments are also not described well, for my below comments I have assumed that different groups of bees were tested for experiments 1-8, and that experiment 6 was run as described in line 331, where bees were given string-pulling training without perceptual feedback rather than how it is described in Figure 4B, which describes bees as receiving string pulling training with feedback.

We now added figures of Experiment 6 and 7 in the Figure 1B, and we mentioned that different groups of bees were tested for Experiments 1-9.

The authors suggest the bees' performance is best explained by what they term 'image matching'. However, experiment 6 does not seem to support this without assuming retroactive image matching after the problem is solved. The logic of experiment 6 is described as "This was to ensure that the bees could not see the familiar "lollipop shape" while pulling strings....If the bees prefer to pull the connected strings, this would indicate that bees memorize the arrangement of strings-connected flowers in this task." I disagree with this second sentence, removing perceptual feedback during training would prevent bees memorising the lollipop shape, because, while solving the task, they don't actually see a string connected to a yellow flower, due to the black barrier. At the end of the task, the string is now behind the bee, so unless the bee is turning around and encoding this object retrospectively as the image to match, it seems hard to imagine how the bee learns the lollipop shape.

We agree with the reviewer that while solving the task in the last step during training, the bees don't actually see a string connected to a yellow flower, due to the black barrier. Since the full shape is only visible after the pulling is completed and this requires the bee to “check back” on the entire display after feeding, to basically conclude “ this is the shape that I need to be looking for later”.

Another possibility is that bumblebees might remember the image of the “lollipop shape” while training the bees in the first step, in which the “lollipop shape” was directly presented to the bumblebee in the early step of the training.

We added the experiment suggested by the reviewer, and the result showed that when a green table was placed behind the string to obscure the “lollipop shape” at any point during the training phase, the bees were unable to identify the connected string. The result further supports that bumblebees learn to choose the connected string through image matching.

Despite this, the authors go on to describe image matching as one of their main findings. For this claim, I would suggest the authors run another experiment, identical to experiment 6 but with a black panel behind the bee, such that the string the bee pulls behind itself disappears from view. There is now no image to match at any point from the bee's perspective so it should now fail the connectivity task.

Strengths:

Despite these issues, this is a fascinating dataset. Experiments 1 and 2 show that the bees are not learning to discriminate between connected and unconnected stimuli rapidly in the first trials of the test. Instead, it is clear that experience in string pulling is needed to discriminate between connected and unconnected strings. What aspect of this experience is important? Experiment 6 suggests it is not image matching (when no image is provided during problem-solving, but only afterward, bees still attend to string connectivity) and casts doubt on perceptual-motor feedback (unless from the bee's perspective, they do actually get feedback that pulling the string moves the flower, video is needed here). Experiments 7 and 8 rule out means-end understanding because if the bees are capable of imagining the effect of their actions on the string and then planning out their actions (as hypotheses such as insight, means-end understanding and string connectivity suggest), they should solve these tasks. If the authors can compare the bees' performance in a more detailed way to other species, and run the experiment suggested, this will be a highly exciting paper

We appreciate the valuable comment from the reviewer. We compared the bees' performance to other species, and conducted the experiment as suggested by the reviewer.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Smaller comments:

Line 64: is the word 'simple' needed here? It could also be explained by more complex forms of associative learning, no?

We deleted “simple”.

Methods:

Line 230: was it checked that this was high-contrast for the bees?

We added the relevant reference in the revised manuscript.

Line 240: how much sucrose solution was present in the flowers?

We added 25 microliters sucrose solution in the flowers. We added the information in the revised manuscript.

Line 266: check grammar.

We checked the grammar as follows: “During tests, both strings were glued to the floor of the arena to prevent the air flow generated by flying bumblebees’ wings from changing the position of the string.”

Statistical analysis:

- What does it mean that "Bees identity and colony were analyzed with likelihood ratio tests"?

Bees identity and colony was set as a random variable. We changed the analysis methods in the revised manuscript, and results of the all the experiments did not changed.

- Line 359: do you mean proportion rather than percentage?

We mean the percentage.

- "the number of total choices as weights" - this should be explained further. This is the number of choices that each bee made? What was the variation and mean of this number? If bees varied a lot in this metric, it might make more sense to analyze their first choice (as I see you've done) and their first 10 choices or something like that - for consistency.

This refers to the total number of choices made by each bumblebee. We added the mean and standard error of each bee’s number of choices in Table 1. Some bees pulled the string fewer than 10 times; we chose to include all choices made by each bee.

- More generally I think the first test is more informative than the subsequent choices, since every choice after their first could be affected by feedback they are getting in that test phase. Or rather, they are telling you different things.

All the bees were tested only once, however, you might be referring to the first choice. We used Chi-square test to analyze the bumblebees’ first choices in the test. It is worth noting that both connected and disconnected strings were glued to the floor. The bees were unable to move either the connected or disconnected strings during the tests, and only attempted to pull them. Therefore,the feedback from pulling either the connected or disconnected strings is the same.

- Line 362: I think I know what you mean, but this should be re-phrased because the "number of" sounds more appropriate for a Poisson distribution. I think what you are testing is whether each individual bee chose the connected or the disconnected string - i.e. a 0 or 1 response for each bee?

We agree with the reviewer that each bee chose the connected or the disconnected string - i.e. a 0 or 1 response for each bee, but not the number. We clarify this as: “The total number of the choices made by each bee was set as weights.” 

- Line 364-365: here and elsewhere, every time you mention a model, make it clear what the dependent and independent variables are. i.e. for the mixed model, the 'bee' is the random factor? Or also the colony that the bee came from? Were these nested etc?

We clarify this in the revised manuscript. The bee identity and colony is the random factor in the mixed model.

- Line 368: "Latency to the first choice of each bee was recorded" - why? What were the hypotheses/ predictions here?

The latency to the first choice was intended to see if the bumblebees were familiarizing with the testing pattern. A shorter delay time might indicate that the bumblebees were more familiar with the pattern.

- Line 371: "Multiple comparisons among experiments were.." - do you mean 'within' experiments? It seems that treatments should not be compared between different experiments.

We mean multiple comparisons among different experiments; we clarify this in the revised manuscript.

Results

Experiment 1: From the methods, it sounded like you both analyzed the bees' first choice and their total no. of choices, but in the results section (and Figure 1) I only see the data for all choices combined here.

In table 1 and in the text you report the number of bees that chose each option on their first choice, but there are no statistical results associated with these results. At the very least, a chi square or binomial test could be run.

Line 138: "Interestingly, ten out of fifteen bees pulled the connected string in their first choice" - this is presented like it is a significant majority of bees, but a chi-square test of 10 vs 5 has a p-value = 0.1967

We used the Chi square test to analyzed of the bees’ first choice. We also added the analyzed data in the Table 1.

Line 143: "It makes sense because the bees could see the "lollipop shape" once they pulled it out from the table." - this feels more like interpretation (i.e. Discussion) rather than results.

We moved the sentence to the discussion.

Line 162: again this feels more like interpretation/ conjecture than results.

We removed the sentence in the results.

Line 184: check grammar.

We checked the grammar. We changed “task” to “tasks”.

Figures

I really appreciated the overview in Figure 5 - though I think this should be Figure 1? Even if the methods come later in eLife, I think it would be nice to have that cited earlier on (e.g. at the start of the results) to draw the reader's attention to it quickly, since it's so helpful. It also then makes the images at the bottom of what is currently Figure 1 make more sense. I also think that the authors could make it clearer in Figure 5 which strings are connected vs disconnected in the figure (even if it means exaggerating the distance more than it was in real life). I had to zoom in quite a bit to see which were connected vs. not. Alternatively, you could have an arrow to the string with the words "connected" "disconnected" the first time you draw it - and similar labels for the other string conditions.

We appreciate the valuable comment from the reviewer. We changed Figure 5 to Figure 2, and Figure 4 to Figure 1. We cited the Figures at the start of the results. We also changed the gap distance between the disconnected strings. Additionally, we added arrows to indicate “connected” and “disconnected” strings in the Figure.

Figure 1 - I think you could make it clearer that the bars refer to experiments (e.g. have an x-axis with this as a label). Also, check the grammar of the y-axis.

We added the experiments number in the Figures. Additionally, we checked the grammar of the y-axis. We changed “percentages” to “parentage”. 

I also think it's really helpful to see the supplementary videos but I think it would be nice to see some examples of the test phase, and not just the training examples.

We added Supplementary videos of the testing phase.

Reviewer #2 (Recommendations For The Authors):

Below are also some minor comments:

L40: "approaches".

We changed “approach” to “approaches”.

L42: but likely mainly due to sampling bias of mammals and birds.

We changed the sentence as follows: String pulling is one of the most extensively used approaches in comparative psychology to evaluate the understanding of causal relationships (Jacobs & Osvath, 2015), with most research focused on mammals and birds, where a food item is visible to the animal but accessible only by pulling on a string attached to the reward (Taylor, 2010; Range et al., 2012; Jacobs & Osvath, 2015; Wakonig et al., 2021).

L64: remove "in this study"

We removed “in this study”.

L64: simple associative learning of what? Isn't your image matching associative too?

We removed “ simple”.

L97: remove "a" before "connected".

We removed “a” before “connected”.

L136-138: but maybe they could still feel the weight of the flower when pulling?

Because both strings were glued to the floor in the test phase, the feedback was the same and therefore irrelevant. This information is noted in the General Methods.

L161: what are these numbers?

We removed the latency in the revised manuscript.

L167/ Table 1: I realise that the authors never tried slanted strings to check if bumblebees used proximity as a cue. Why?

This was simply because we wanted to focus on whether bumblebees could recognize the connectivity of the string.

Discussion: Why did you only control for colour of the string? What if you had used strings with different textures or smells? Unclear if the authors controlled for "bumblebee smell" on the strings, i.e., after a bee had used the string, was the string replaced by a new one or was the same one used multiple times?

We used different colors to investigate featural generalization of the visual display of the string connected to the flower in this task. We controlled for color because it is a feature that bumblebees can easily distinguish.

Both the flowers and the strings were used only once, to prevent the use of chemosensory cues. We clarify this in the revised manuscript.

L182: since what?

We deleted “since” in the revised manuscript.

L182-188: might be worth mentioning that some crows and parrots known for complex cognition perform poorly on broken strings (e.g., https://doi.org/10.1098/rspb.2012.1998 ; https://doi.org/10.1163/1568539X-00003511 ; https://doi.org/10.1038/s41598-021-94879-x ) and Australian magpies use trial and error (https://doi.org/10.1007/s00265-023-03326-6).

We added the following sentences as suggested by the reviewer: “It is worth noting that some crows and parrots known for complex cognition perform poorly on the broken string task without perceptual feedback or learning. For example, New Caledonian crows use perceptual feedback strategies to solve the broken string-pulling task, and no individual showed a significant preference for the connected string when perceptual feedback was restricted (Taylor et al., 2012). Some Australian magpies and African grey parrots can solve the broken string task, but they required a high number of trials, indicating that learning plays a crucial role in solving this task (Molina et al., 2019; Johnsson et al., 2023).”

L193: maybe expand on this to put the task into a natural context?

We added the following sentences as suggested by the reviewer:

“Different flower species offer varying profitability in terms of nectar and pollen to bumblebees; they need to make careful choices and learn to use floral cues to predict rewards (Chittka, 2017). Bumblebees can easily learn visual patterns and shapes of flower (Meyer-Rochow, 2019); they can detect stimuli and discriminate between differently coloured stimuli when presented as briefly as 25 ms (Nityananda et al., 2014). In contrast, causal reasoning involves understanding and responding to causal relationships. Bumblebees might favor, or be limited to, a visual approach, likely due to the efficiency and simplicity of processing visual cues to solve the string-pulling task. ”

L204: is causal understanding the same as means-end understanding?

Means-end understanding is expressed as goal-directed behavior, which involves the deliberate and planned execution of a sequence of steps to achieve a goal. Includes some understanding of the causal relationship (Jacobs & Osvath, 2015; Ortiz et al., 2019). .

L235: this is a very big span of time. Why not control for motivation? Cognitive performance can vary significantly across the day (at least in humans).

Bumblebee motivation is understood to be rather consistent, as those that were trained and tested came to the flight arena of their own volition and were foragers looking to fill their crop load each time to return it to the colony.

L232: what is "(w/w)" ? This occurs throughout the manuscript.

“w/w” represents the weight-to-weight percentage of sugar.

L250: this sentence sounds odd. "containing in the central well.." ?? Perhaps rephrase? Unclear what central well refers to? Did the flowers have multiple wells?

We rephrased the sentence as follows: For each experiment, bumblebees were trained to retrieve a flower with an inverted Eppendorf cap at the center, containing 25 microliters of 50% sucrose solution, from underneath a transparent acrylic table

L268: why euthanise?

The reason for euthanizing the bees is that new foragers will typically only become active after the current ones were removed from the hive.

L270: chemosensory cues answer my concern above. Maybe make it clear earlier.

We moved this sentence earlier in the result.

L273: did different individuals use different pulling strategies? Do you have the data to analyse this? This has been done on birds and would offer a nice comparison.

We analyzed the string-pulling strategies among different individuals, and provided Supplementary Table 1 to display the performances of each individual in different string-pulling experiments.

L365: unclear why both models. Would be nice to see a GLM output table.

The duration of pulling different kinds of strings were first tested with the Shapiro-Wilk test to assess data normality. The duration data that conforms to a normal distribution was compared using linear mixed-effects models (LMM), while the data that deviates from normality were examined with a generalized linear-mixed model (GLMM). We added a GLM and GLMM output table in the revised manuscript.

L377: should be a space between the "." and "This".

We added a space between the “.” and “This”.

L383-390: some commas and semicolons are in the wrong places.

We carefully checked the commas and semicolons in this sentence.

Reviewer #3 (Recommendations For The Authors):

Minor comments

Line 32: seems to be missing a word, suggest "the bumblebees' ability to distinguish".

we added “the” in the revised manuscript.

Line 47: it would be good to reference other scholars here, this is the central focus of all work in comparative psychology.

We added the reference in the revised manuscript.

Line 50-61: I think the string-pulling literature could be described in more detail here, with mention of perceptual-motor feedback loops as a competing hypothesis to means-end understanding (see Taylor et al 2010, 2012). It seems a stretch to suggest that "String-pulling studies have directly tested means-end comprehension in various species", when perceptual-motor feedback is a competing hypothesis that we have positive evidence for in several species.

We mentioned the perceptual-motor feedback in the introduction as follow:

“Multiple mechanisms can be involved in the string-pulling task, including the proximity principle, perceptual feedback and means-end understanding (Taylor et al., 2012; Wasserman et al., 2013; Jacobs & Osvath, 2015; Wang et al., 2020). The principle of proximity refers to animals preferring to pull the reward that is closest to them (Jacobs & Osvath, 2015). Taylor et al. (2012) proposed that the success of New Caledonian crows in string-pulling tasks is based on a perceptual-motor feedback loop, where the reward gradually moves closer to the animal as they pull the strings. If the visual signal of the reward approaching is restricted, crows with no prior string-pulling experience are unable to solve the broken string task (Taylor et al., 2012).

However, when a green table was placed behind the string to obscure the “lollipop” structure during the training, the bees could not see the “lollipop” during the initial training stage or after pulling the string from under the table. In this situation, the bees were unable to identify the connected string, further proving that bumblebees chose the connected string based on image matching.

Line 68: suggest remove 'meticulously'.

We removed “meticulously”.

Line 99: This is an exciting finding, can the authors please provide a video of a bee solving this task on its first trial?

We added videos in the supplementary materials.

Line 133: perceptual-motor feedback loops should be introduced in the introduction.

We introduced perceptual-motor feedback loops in the revised manuscript.

Line 136: please clarify the prior experience of these bees, it is not clear from the text.

We clarified the prior experience of these bees as follow: Bumblebees were initially attracted to feed on yellow artificial flowers, and then trained with transparent tables covered by black tape (S7 video) through a four-step process.

Line 138: from the video it is not possible to see the bee's perspective of this occlusion. Do the authors have a video or image showing the feedback the bees received? I think this is highly important if they wish to argue that this condition prevents the use of both image matching and a perceptual-motor feedback loop.

We prevented the use of image matching: the bees were unable to see the flower moving towards them above the table during the training phase in this condition. But the bees may receive visual image both after pulling the string out from the table and in the initial stages of training in this condition.

Line 147: please clarify what experience these bees had before this test.

We added the prior experience of bumblebees before training as follow: We therefore designed further experiments based on Taylor et al. (2012) to test this hypothesis. Bumblebees were first trained to feed on yellow artificial, and then trained with the same procedure as Experiment 2, but the connected strings were coiled in the test.

Line 155: This is a highly similar test to that used in Taylor et al 2012, have the authors seen this study?

We mentioned the reference in the revised manuscript as follows: We therefore designed further experiments based on Taylor et al. (2012) to test this hypothesis.

Line 183: This sentence needs rewriting "Since the vast majority of animals, including dogs 183 (Osthaus et al., 2005), cats (Whitt et al., 2009), western scrub-jays (Hofmann et al.,2016) and azure-winged magpies (Wang et al., 2019) are failing in such tasks spontaneously".

We changed the sentence as suggested by the reviewer as follow:  Some animals, including dogs (Osthaus et al., 2005), cats (Whitt et al., 2009), western scrub-jays (Hofmann et al., 2016) and azure-winged magpies (Wang et al., 2019) fail in such task spontaneously.

Line 186: "complete comprehension of the functionality of strings is rare" I am not sure the evidence in the current literature supports any animal showing full understanding, can the authors explain how they reach this conclusion?

We wished to say that few animal species could distinguish between connected and disconnected strings without trial and error learning. We revised the sentence as follows:

It is worth noting that some crows and parrots known for complex cognition perform poorly on broken string task without perceptual feedback or learning. For example, New Caledonian crows use perceptual feedback strategies to solve broken string-pulling task, and no individual showed a significant preference for the connected string when perceptual feedback is restricted (Taylor et al., 2012). Some Australian magpies and African grey parrots can solve the broken string task, but it required a high number of trials, indicating that learning plays a crucial role in solving this task (Molina et al., 2019; Johnsson et al., 2023).

Line 190: the authors need to clarify which part of their study provides positive evidence for this conclusion.

We added the evidence for this conclusion as follows: Our findings suggest that bumblebees with experience of string pulling prefer the connected strings, but they failed to identify the interrupted strings when the string was coiled in the test.

Line 265: was the far end of the string glued only?

The entire string was glued to the floor, not just the far ends of the string.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review):

Summary: 

In this paper, the authors used target agnostic MBC sorting and activation methods to identify B cells and antibodies against sexual stages of Plasmodium falciparum. While they isolated some Mabs against PFs48/45 and PFs230, two well-known candidates for "transmission blocking" vaccines, these antibodies' efficacies, as measured by TRA, did not perform as well as other known antibodies. They also isolated one cross-reactive mAb to proteins containing glutamic acid-rich repetitive elements, that express at different stages of the parasite life cycle. They then determined the structure of the Fab with the highest protein binder they could determine through protein microarray, RESA, and observed homotypic interactions. 

Strengths: 

-  Target agnostic B cell isolation (although not a novel methodology). 

-  New cross-reactive antibody with some "efficacy" (TRA) and mechanism (homotypic interactions) as demonstrated by structural data and other biophysical data. 

Weaknesses: 

The paper lacks clarity at times and could benefit from more transparency (showing all the data) and explanations. 

We have added the oocyst count data from the SMFA experiments as Supplementary Table 2, and ELISA binding curves underlying Figure 4B as Supplementary Figure 5.

In particular: 

- define SIFA 

- define TRAbs 

We have carefully gone through the manuscript and have introduced abbreviations at first use, removed unnecessary abbreviations and removed unnecessary jargon to increase readability.

- it is not possible to read the Figure 6B and C panels. 

We regret that the labels in Supplementary Figures 6 and 7 were of poor quality and have now included higher resolution images to solve this issue.

Reviewer #2 (Public Review): 

This manuscript by Amen, Yoo, Fabra-Garcia et al describes a human monoclonal antibody B1E11K, targeting EENV repeats which are present in parasite antigens such as Pfs230, RESAs, and 11.1. The authors isolated B1E11K using an initial target agnostic approach for antibodies that would bind gamete/gametocyte lysate which they made 14 mAbs. Following a suite of highly appropriate characterization methods from Western blotting of recombinant proteins to native parasite material, use of knockout lines to validate specificity, ITC, peptide mapping, SEC-MALS, negative stain EM, and crystallography, the authors have built a compelling case that B1E11K does indeed bind EENV repeats. In addition, using X-ray crystallography they show that two B1E11K Fabs bind to a 16 aa RESA repeat in a head-to-head conformation using homotypic interactions and provide a separate example from CSP, of affinity-matured homotypic interactions. 

There are some minor comments and considerations identified by this reviewer, These include that one of the main conclusions in the paper is the binding of B1E11K to RESAs which are blood stage antigens that are exported to the infected parasite surface. It would have been interesting if immunofluorescence assays with B1E11K mAb were performed with blood-stage parasites to understand its cellular localization in those stages. 

In the current manuscript, we provide multiple lines of evidence that B1E11K binds (with high affinity) to repeats that are present in RESAs, i.e. through micro-array studies, in vitro binding experiments such as Western blot, ELISA and BLI, and through X-ray crystallography studies on B1E11k – repeat peptide complexes. Taken together, we think we provide compelling evidence that B1E11k binds to repeats present in RESA proteins. We do agree that studies on the function of this mAb against other stages of the parasite could be of interest, but as our manuscript focuses on the sexual stage of the parasite, we feel that this is beyond scope of the current work. However, this line of inquiry will be strongly considered in follow up studies.   

Reviewer #3 (Public Review): 

The manuscript from Amen et al reports the isolation and characterization of human antibodies that recognize proteins expressed at different sexual stages of Plasmodium falciparum. The isolation approach was antigen agnostic and based on the sorting, activation, and screening of memory B cells from a donor whose serum displays high transmission-reducing activity. From this effort, 14 antibodies were produced and further characterized. The antibodies displayed a range of transmission-reducing activities and recognized different Pf sexual stage proteins. However, none of these antibodies had substantially lower TRA than previously described antibodies. 

The authors then performed further characterization of antibody B1E11K, which was unique in that it recognized multiple proteins expressed during sexual and asexual stages. Using protein microarrays, B1E11K was shown to recognize glutamate-rich repeats, following an EE-XX-EE pattern. An impressive set of biophysical experiments was performed to extensively characterize the interactions of B1E11K with various repeat motifs and lengths. Ultimately, the authors succeeded in determining a 2.6 A resolution crystal structure of B1E11K bound to a 16AA repeat-containing peptide. Excitingly, the structure revealed that two Fabs bound simultaneously to the peptide and made homotypic antibody-antibody contacts. This had only previously been observed with antibodies directed against CSP repeats. 

Overall I found the manuscript to be very well written, although there are some sections that are heavy on field-specific jargon and abbreviations that make reading unnecessarily difficult. For instance, 'SIFA' is never defined. 

We have carefully gone through the manuscript and have introduced abbreviations at first use, removed unnecessary abbreviations and removed unnecessary jargon to increase readability.

Strengths of the manuscript include the target-agnostic screening approach and the thorough characterization of antibodies. The demonstration that B1E11K is cross-reactive to multiple proteins containing glutamate-rich repeats, and that the antibody recognizes the repeats via homotypic interactions, similar to what has been observed for CSP repeat-directed antibodies, should be of interest to many in the field. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Figure 1 - why only gametes ELISA and Spz or others?  

The volumes of the single B cell supernatants were too small to screen against multiple antigens/parasite stages. As we aimed to isolate antibodies against the sexual stages of the parasite, our assay focused on this stage and supernatants were not tested against other stages. Furthermore, we screened for reactivity against gametes as TRA mAbs likely target gametes rather than other forms of sexual stage parasites.

Figure 2 A 

(a) Wild type (WT) and Pfs48/45 knock-out (KO) gametes.

(b) I am a bit confused about what GMT is vs Pfs48/45 

We have changed the column titles in Figure 2A to “wild-type gametes” and “Pfs48/45 knockout gametes” to improve clarity.  

(c) Binding is high % why is it red? 

We chose to present the results in a heatmap format with a graded color scale, from strong binders in red to weak binders in green. It has now been clarified in the legend of the figure. 

Please state acronyms clearly 

TRA - transmission reducing activity 

SMFA - standard membrane feeding assay 

We have added the full terms to clarify the acronyms.

1123- VRC01 (not O1)

We have corrected this.

Figure 2 C bottom panels, clarify which ones are TRAbs (Assuming the Mabs with over 80% TRA at 500 ug/ml) (right gel) and the ones that are not (left gel)? 

In the Western blot in Figure 2c, we have marked the antibodies with >80% TRA with an asterisk.

Furthermore, we have replaced ‘TRAbs’ by ‘mAbs with >80% TRA at 500 µg/mL’ in the figure legend.

ITC show the same affinity of the Fab to the 2 peptides but not the ELISA, not the BLI/SPR would be more appropriate. Any potential explanation?  

The way binding affinity is determined across various techniques can result in slight differences in determined values. For instance, ELISAs utilize long incubation times with extensive washing steps and involve a spectroscopic signal, isothermal titration calorimetry (ITC) uses calorimetric signal at different concentration equilibriums to extract a KD, and BLI determines kinetic parameters for KD determination. Discrepancies in binding affinities between orthologous techniques have indeed been observed previously in the context of peptide-antibody binding (e.g. PMID: 34788599).

Despite this, regardless of technique, the relative relationships in all three sets of data is the same - higher binding affinity is observed to the longer P2 peptide. This is the main takeaway of the section. As the reviewer suggests, BLI is likely the most appropriate readout here and is the only value explicitly mentioned in the main text. We primarily use ITC to support our proposed binding stoichiometry which is important to substantiate the SEC-MALS and nsEM data in Figure 4H-I. We added the following sentences to help reinforce these points: “The determined binding affinity from our ITC experiments (Table 1) differed from our BLI experiments (Fig. 4D and 4E), which can occur when measuring antibody-peptide interactions. Regardless, our data across techniques all trend toward the same finding in which a stronger binding affinity is observed toward the longer RESA P2 (16AA) peptide.”

Figure 5C - would be helpful to have the peptide sequence above referring to what is E1, E2 etc... 

We added two panels (Figure 5C-D) showcasing the binding interface that shows the peptide numbering in the context of the overall complex. We hope that this will help better orient the reader. 

Figure S4 - maybe highlight in different colors the EENVV, EEIEE, Etc, etc 

Repeats found in the sequence of the various proteins in Figure S4 have now been highlighted with different colors.

Line 163 - why 14 mabs if 11 wells? Isn't it 1 B cell per well? The authors should explain right away that some wells have more than 1 B cell and some have 1 HC, 1LC, and 1 KC. 

We agree that this was somewhat confusing and have modified the text which now reads: “We obtained and cloned heavy and light chain sequences for 11 out of 84 wells. For three wells we obtained a kappa light chain sequence and for five wells a lambda light chain sequence. For three wells we obtained both a lambda and kappa light chain sequence suggesting that either both chains were present in a single B cell or that two B cells were present in the well. For all 14 wells we retrieved a single heavy chain sequence. Following amplification and cloning, 14 mAbs, from 11 wells, were expressed as full human IgG1s (Table S1) (Dataset S1).”

Line 166-167 - were they multiple HC (different ones) as well when Lambda and kappa were present?

This is not clear at first. 

We clarified this point in the text, see also comment above.

Line 177 - expressed Pfs48/45 and Pfs230, is it lacking both or just Pfs48/45 (as stated on line 172)? 

Pfs48/45 binds to the gamete surface via a GPI anchor, while Pfs230 is retained to the surface through binding to Pfs48/45. Hence, the Pfs48/45 knockout parasite will therefore also lack surfacebound Pfs230. We have added a sentence to the Results clarifying this: “The mAbs were also tested for binding to Pfs48/45 knock-out female gametes, which lack surface-bound Pfs48/45 and Pfs230”.

Show the ELISA data used to calculate EC50 in Figure 3. 

ELISA binding curves are now shown as Figure S5.

Line 313-315 - what if you reverse, capture the Fab (peptide too small even if biotinylated?) 

As anticipated by the Reviewer, immobilizing the Fab and dipping into peptide did not yield appreciable signal for kinetic analysis and thus the experiment from this setup is not reported. 

Line 341 - add crystal structure 

This has now been added.

There is a bit too much speculation in the discussion. For e.g. "The B1C5L and B1C5K mAbs were shown to recognize Domain 2 of Pfs48/45 and exhibited moderate potency, as previously described for Abs with such specificity (27). These 2 mAbs were isolated from the same well and shared the same heavy chain; their three similar characteristics thus suggest that their binding is primarily mediated by the heavy chain". Actual data will reinforce this statement. 

As B1C5L and B1C5K recognized domain 2 of Pfs48/45 with similar affinity, this strongly suggests that binding is mediated though the heavy chain. Structural analysis could confirm this statement, but this is out of the scope of this study.  

Reviewer #2 (Recommendations For The Authors): 

Figure 1: This figure provides a description of the workflow. To make it more relevant for the paper, the authors could add relevant numbers as the workflow proceeds. 

(a) For example, how many memory B cells were sorted, how many supernatants were positive, and then how many mAbs were produced? These numbers can be attached to the relevant images in the workflow. 

We modified the figure to include the numbers. 

(b) For the "Supernatant screening via gamete extract ELISA", please change to "Supernatant screening via gamete/gametocyte extract ELISA". 

We modified the statement as suggested. 

Line 155: The manuscript states that 84 wells reacted with gamete/gametocyte lysate. The following sentence states that "Out of the 21 supernatants that were positive...". Can the authors provide the summary of data for all 84 wells or why focus on only 21 supernatants? 

We screened all supernatants against gamete lysate, and only a subset against gametocyte lysate. In total, we found 84 positive supernatants that were reactive to at least one of the two lysates. 21 of those 84 positive were screened against both lysates. We have modified the text to clarify the numbers:

“After activation, single cell culture supernatants potentially containing secreted IgGs were screened in a high-throughput 384-well ELISA for their reactivity against a crude Pf gamete lysate (Fig. S1B). A subset of supernatants was also screened against gametocyte lysate (S1C). In total, supernatants from 84 wells reacted with gamete and/or gametocyte lysate proteins, representing 5.6% of the total memory B cells. Of the 21 supernatants that were screened against both gamete and gametocyte lysates, six recognized both, while nine appeared to recognize exclusively gamete proteins, and six exclusively gametocyte proteins.”

Please note that all 84 positive wells were taken forward for B cell sequencing and cloning. 

Line 171: SIFA is introduced for the first time and should be completely spelled out.

We have corrected this. 

Figure 2: 

(a) In Figure 2A, can you change the column title from "% pos KO GMT" to "% pos Pfs48/45 KO GMT"?

We have changed the column titles.  

(b) In Figure 2B, the SMFA results have been converted to %TRA. Can the authors please provide the raw data for the oocyst counts and number of mosquitoes infected in Supplementary Materials? 

We have added oocyst count data in Table S2, to which we refer in the figure legend. 

(c) For Figure 2F, the authors do have other domains to Pfs230 as described in Inklaar et al, NPJ Vaccines 2023. An ELISA/Western to the other domains could identify the binding site for B2C10L, though we appreciate this is not the central result of this manuscript. 

We thank the reviewer for this suggestion. We are indeed planning to identify the target domain of B2C10L using the previously described fragments, but agree with the reviewer that this not the focus of the current manuscript and decided to therefore not include it in the current report.

Line 116: The word sporozoites appears in subscript and should be corrected to be normal text. 

We have corrected this.

Line 216: Typo "B1E11K" 

We have corrected this.

Materials and Methods: 

(a) PBMC sampling: Please add the ethics approval codes in this section. 

Donor A visited the hospital with a clinical malaria infection and provided informed consent for collection of PBMCs. We have modified the method section to clarify this. 

“Donor A had lived in Central Africa for approximately 30 years and reported multiple malaria infections during that period. At the time of sampling PBMCs, Donor A had recently returned to the Netherlands and visited the hospital with a clinical malaria infection. After providing informed consent, PBMCs were collected, but gametocyte prevalence and density were not recorded.”

(b) Gamete/Gametocyte extract ELISA: Can the authors please provide the concentration of antibodies used for the positive and negative controls (TB31F, 2544, and 399) 

We have added the concentrations for these mAbs in the methods section.

Recombinant Pfs48/45 and Pfs230 ELISA: Please state the concentration or molarity used for the coating of recombinant Pfs48/45 and Pfs230CMB. 

We have added the concentrations, i.e. 0.5 µg/mL, to the methods section.

Western Blotting: The protocol states that DTT was added to gametocyte extracts (Line 594), but Western Blots in Figures 2 and 3 were performed in non-reducing conditions. Please confirm whether DTT was added or not. 

Thank you for noting this. We did not use DTT for the western blots and have removed this line from the methods section.

Reviewer #3 (Recommendations For The Authors): 

Below are a few minor comments to help improve the manuscript. 

(1) In Figure 4E, are the BLI data fit to a 1:1 binding model? The fits seem a bit off, and from ITC and X-ray studies it is known that 2 Fabs bind 1 peptide. The second Fab should presumably have higher affinity than the first Fab since the second Fab will make interactions with both the peptide and the first Fab. It may be better to fit the BLI data to a 2:1 binding model. 

The 2:1 (heterogeneous ligand) model assumes that there are two different independent binding sites. However, the second binding event described is dependent on the first binding event and thus this model also does not accurately reflect the system. Given that there is not an ideal model to fit, we instead are careful about the language used in the main text to describe these results. Additionally, we also include a sentence to the results section to ensure that the proper findings/interpretations are highlighted: “…our data all trend toward the same finding in which a stronger binding affinity is observed toward the longer RESA P2 (16AA) peptide.”

(2) The sidechain interactions shown in Figures 5C and D could probably be improved. The individual residues are just 'floating' in space, causing them to lack context and orientation. 

We added two panels (Fig. 5C-D) showcasing the binding interface that shows the peptide numbering in the context of the overall complex. We hope that this will help orient the reader.  

(3) The percentage of Ramachandran outliers should be listed in Table 2. Presumably, the value is 0.2%, but this is omitted in the current table. 

Table 2 has been modified to include the requested information explicitly.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

The work is well performed and thoroughly convincing. 

However, a few points could be improved, by adjusting the manuscript: 

(1) The wording of the abstract is confusing for the casual reader. The initial impression is that the 2-copy complexes contain the majority of the PSD95 copies. This is not the case, as shown in panel cii. It would be important for the authors to explain in the abstract the exact percentage of molecules found within 2-copy complexes. 

We have now amended the abstract, making it clear that it’s not most of the complexes.  

(2) Did the authors find a sizeable population of 2-copy complexes by investigating wild-type proteins, using nanobody labeling (Figure S2)? It would be important to quantify and discuss these data. 

It was not possible to perform this analysis on the wild-type proteins. The quantification would rely on all the PSD95 molecules being bound by the antibody, which we cannot guarantee. Furthermore, the nanobody labeling would need to be stoichiometric. 

(3) The authors quote the separation value of 12.7 nm throughout their text, including the abstract. This may be somewhat misleading since the authors investigate the PSD95-GFP molecules, labeled using anti-GFP nanobodies. The large size of the two GFP molecules (~3 nm), and that of the nanobodies, will influence the readout. Two groups have already reported a separation of ~7-8 nm between neighboring PSD95 molecules in synapses, using PSD95 nanobodies, to minimize the linkage

error: https://doi.org/10.1101/2022.08.03.502284 and https://doi.org/10.1101/2023.10.18.562 700  

The difference observed here is consistent with an effect of the additional GFP moieties; the authors should cite these works (albeit they are now only provided as biorXiv pre-prints) and should mention this discrepancy, and its potential tagging-related explanation. 

We have now referenced the work and referred to this in the discussion.

(4) The authors may want to re-check the manuscript; some minor problems should be corrected, such as the mislabeling of Figure 2 and "Figure 5". 

This has now been corrected.  

Reviewer #2 (Recommendations For The Authors): 

The authors suggest that the stability of the PSD95 dimeric complex correlates with memory formation. However, the turnover experiments were conducted only on three-month-old animals, which can be considered to be at a stage of lower synaptic functionality turnover. It would be appropriate to study dimer turnover during the memory formation period at three to four weeks of age, for example in comparison to the oldest mice. 

Alternatively, it might be interesting to study the turnover in the hippocampus following exposure to a memory test. 

Whilst potentially useful, these experiments are outside of the scope of this manuscript.   

It is not clear whether the different turnover identified in various brain areas is statistically significant, as apparently no statistical analysis has been conducted. 

The findings were significant, and the SI table containing the p-values has been emphasized further in the manuscript.  

Reviewer #3 (Recommendations For The Authors): 

(1) In the last paragraph of the Results section, it could be made clearer what the nature is of the correlation between PSD95 half-life and mixed supercomplexes to understand how to interpret this correlation. In the discussion, it is concluded that stable synapses have long protein lifetimes and slow replacement of scaffolding proteins. However, this is based on the correlation of protein lifetime and mixed supercomplexes in the cortex, which does not provide any evidence that this relation is true in single synapses or is specific for stable synapses. To make this statement, the authors could for instance directly correlate the stoichiometry of supercomplexes with the protein lifetime and size of individual synapses. 

Unfortunately, we can’t directly measure the lifetime of each complex, and so it’s only possible to compare region-to-region. In doing so, we found that there was a correlation between the protein lifetime and the “mixed” population.  

(2) Some essential parts seem missing: the materials and methods and Figure 2 are not included. Also, the numbering of figures is incorrect. Both in the figure legends and the text. 

This has been added. 

(3) Figure 1a could contain more details of the experimental procedures. For example, it could be made clearer how PSD95 supercomplexes are isolated from brain homogenate. 

This is now presents in the methods. 

(4) In Figure 1c, single molecules of PSD95 are identified using PALM with a resolution of 30 nm. However, in Figure 1d it is shown that PSD95 molecules reside on average 13 nm apart, indicating that a resolution of 30 nm is not sufficient to resolve single PSD95 molecules. In addition, it would be of interest to show the distribution of fluorophore separation (assessed with MINFLUX) of only the supercomplexes with two PSD95 molecules, since only these were used to calculate the average distance. 

The 13 nm distance was measured using MINFLUX, as stated in the text. The fluorophore separation distances are shown in Figure 1dii.

(5) In the introduction, the authors could be more explicit in their explanation of memory formation and storage and how the presented study contributes to that field. 

We thank the reviewer for the suggestion, but feel that such a discussion in the introduction would detract from the main points of the manuscript.  

(6) Throughout the manuscript the authors prominently cite their own work, but relevant literature on synaptic plasticity and synapse nanostructure (EM and super-resolution studies) is lacking. 

Further references have now been added.  

(7) The results depicted in Figure 4b would be easier to interpret if a stacked histogram (including error bars) was used. 

We agree that the data could be presented in such a way, but that would prevent the results from the biological repeats, along with the variation, being presented.

Author response:

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

Intro. 

47-48 rewrite sentence

This sentence has been rewritten as: Photoreceptor synapses are specialized with a vesicle-associated ribbon organelle and postsynaptic neurites of horizontal and bipolar cells that invaginate deep within the terminal

Results 

Major comment. Lines 100-103 

The new rod data presented here looks like an n = 1. Neither the Results section nor Supp Fig S1, describe the number of cells used. Nor do the authors offer a statistical description with averages, etc.. In addition, the single traces are much improved over their previous study (Maddox et al eLife 2020), but the authors have not described any new approach or trick that improved their rod Ica. Neither Methods section nor Supp section describes the procedure for patching rods (solutions, or Vh which is critical for assessing T-type currents). 

Suggestion, if more data exists, then present it. Otherwise, drop the argument. 

The recording methodology for recording rods was like that for cones and this has been clarified in the Methods section (lines 725-752). Averaged data (n= at least 5 per group) and statistical analyses have been added to Fig.S1 (renamed Figure 2-Figure Supplement 1), and clearly show that no Ca2+ currents are present in the KI rods.

Supp Fig S2. The legend needs to be fixed. Conversion to PDF file may have created these formatting errors. 

This has been corrected (renamed Figure 3-Figure Supplement 2).

Fig 8 a. The position of the light stimulus bar in the KO panel appears to be out of place, shifted too far to the left. 

This has been corrected.

Major comments. 219-221 

The use of Fluo3-AM is not properly stated here. The text reads "cone pedicles filled with the Ca2+ indicator Fluo3". The wording used could be wrongly interpreted as: whole-cell filling of the cones via patch electrode. However, the Methods section describes bathing the retina in Fluo3-AM, which presumably fills PRs, HCs tips, Mueller glia and bpc dendrites. The Results section should acknowledge that the retina was loaded with Fluo3-AM. 

The cell types, and their processes (Muellers, HCs, bpc, PRs), present in a cone pedicle ROI will likely contribute to the Fluo3 readout of Ca2+ in the OPL, because 1) the EM images in Fig 7 highlight how interdigitated the processes are with the presynapse, 2) all express Cav channels, and many if not all express L-Type Cavs in their processes (glia, HC, on-bcs and PRs), and 3) all are depolarized with the addition of high extracellular KCl. The inclusion of Isradipine will inhibit L-type Cavs on pre- and post-synaptic targets, failing to specifically isolate PR Ca2+. Furthermore, Glu Receptor blockers are used here, which would be a great idea if the cones were stimulated with light; however, KCl bypasses the excitatory synaptic pathway and depolarizes all processes within the ROI. Hence, all cellular parts in the ROI will potentially contribute to Fluo3-Ca2+ signals. 

Suggestions for presentation of these findings. Ultimately your conclusion is suitable " 233 to 234...... Taken together, our results suggest that Cav3 channels nominally support Ca2+ signals and synaptic transmission in cones of G369i KI mice". The dramatic reduction in Fluo3-Ca2+ signals in the OPL G369i retinas (Fig 9) is a valuable finding for the following reasons: 1) the results do not show a clear compensation from intracellular stores that could potentially supersede the T-type currents in the G369i (which is an argument you make), and 2) there is a massive loss of Ca2+ influx in the OPL of G369i retinas. Since G369i is specific to the PRs, and only cones are present in the mutant G369i, the loss of Fluo3-Ca2+ signal in the mutant ROI reflects in large part loss of cone Fluo3-Ca2+ signals. Your findings illustrate the severity of the mutation, which has also been addressed in the various electro-physio sections of the MS. 

Figure 9 also needs to be more clear about 1) the loading of the cells with AM-dye, and 2) the presence of glia, HCs and bc dendrites in the PNA demarcated ROIs. 

We regret that we did not make this more clear, but our Fluo 3 loading protocol of whole retina followed by vertical slicing allowed for loading primarily of photoreceptors in the portion of the outer retina that we imaged. We clarified this with the following edit to the text (lines 220-226):

“To test if the diminished HC light responses correlated with lower presynaptic Ca2+ signals in G369i KI cones, we performed 2-photon imaging of vertical slices prepared from whole retina that was incubated  with the Ca2+ indicator Fluo3-AM and  Alexa-568-conjugated peanut agglutinin (PNA) to demarcate regions of interest (ROIs) corresponding to cone pedicles. With this approach Fluo3 fluorescence was detected only in photoreceptors and ganglion cells and not inner retinal cell-types (e.g., horizontal cells, bipolar cells, Mueller cell soma). Thus, Ca2+ signals reported by Fluo3 fluorescence near PNA-labeling originated primarily from cones.”

We also note that given the considerably larger volume of the cone pedicle relative to the postsynaptic neurites of horizontal and bipolar cells, as well as neighboring glia, it seems unlikely that the latter would contribute significantly to the isradipine-sensitive Ca2+ signal measured in the ROI above the PNA labeling. Moreover, to our knowledge the contribution of Cav1 L-type channels to postsynaptic Ca2+ signals in the dendritic tips of horizontal cells and bipolar cells has not been demonstrated.

Author response:

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

Reviewer #1 (Public Review):

Major shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analyses for several experiments. Because of these omissions, it is difficult to conclude that the data justify the conclusions. The significance of the data presented is overstated, as many of the experiments presented confirm/support previously published work. The study provides a modest advance in the understanding of the complex issue of SHH membrane extraction.

Major shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analysis for several experiments.

This statement is not correct for the revised manuscript: The normalization strategies used are clearly described in the manuscript and are not unusual. Each experiment is now statistically analyzed.

The significance of the data presented is overstated, as many of the experiments presented confirm/support previously published work.

As reviewer 2 correctly points out, there are many competing models for Hedgehog release. Our study cannot possibly support them all - the reviewer's statement is therefore misleading. In fact, our careful biochemical analysis of the mechanistics of Dispatched- mediated Shh export supports only two of them: The model of proteolytic processing of Shh lipid anchors (shedding) and the model of lipoprotein-mediated Shh transport. In contrast, our study does not support the predominant model of Dispatched-mediated extraction of dual-lipidated Shh and delivery to Scube2, which is currently thought to act as a soluble Shh chaperone. We also do not support Dispatched function in Shh endocytic recycling and cytoneme loading, or any of the other models such as exosome-mediated or micelle Shh transport.

Reviewer #2 (Public Review):

A novel and surprising finding of the present study is the differential removal of Shh N- or C- terminal lipid anchors depending on the presence of HDL and/or Disp. In particular, the identification of a non-palmitoylated but cholesterol-modified Shh variant that associates with lipoproteins is potentially important. The authors use RP-HPLC and defined controls to assess the properties of processed forms of Shh, but their precise molecular identity remains to be defined. One caveat is the heavy reliance on overexpression of Shh in a single cell line. The authors detect Shh variants that are released independently of Disp and Scube2 in secretion assays, but these are excluded from interpretation as experimental artifacts. Therefore, it would be important to demonstrate key findings in cells that endogenously secrete Shh.

We would like to respond as follows:

The authors use RP-HPLC and defined controls to assess the properties of processed forms of Shh, but their precise molecular identity remains to be defined.

This is the original reviewers statement regarding our original manuscript submission. We believe that the biochemical and functional data presented in the VOR clearly describe the molecular identity of solubilized Shh: it is monolipidated, lipoprotein-associated, and highly biologically active in two established Shh bioassays.

One caveat is the heavy reliance on overexpression of Shh in a single cell line.

As stated by reviewer 1, the strength of our work is the use of a bicistronic SHH-Hhat system to consistently generate doubly lipidated ligand to determine the amount and lipidation status of SHH released into cell culture media. This unique system therefore eliminates the artifacts of protein overexpression. We have also added two other cell lines to our VOR that produce the same results (including Panc1 cells that endogenously produce Shh, Supplementary Figure 1).

The authors detect Shh variants that are released independently of Disp and Scube2 in secretion assays, but these are excluded from interpretation as experimental artifacts.

As the reviewer correctly points out, these variants are released independently of Disp and Scube2, both of which are known as essential release factors in vivo. These variants are therefore by definition experimental artifacts. The forms we have included in our analysis are the alternative forms that are clearly dependent on Dispatched and Scube2 for their release - as shown in the first figure in the manuscript, and in pretty much every other figure after that.

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

Reviewer #1 (Public Review):

Key shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analyses for several experiments.

In the updated version of the paper, we have addressed all of this reviewer's criticisms. Most importantly, we have performed several additional experiments to address the concern that unusual normalization strategies were used in our paper and that quantification and statistical analyses were lacking for several experiments. We have now analyzed the full set of release conditions for Shh and engineered proteins from Disp-expressing n.t. control cells and Disp-/- cells both in the presence and absence of Scube2 (Figure 1A'-D', Figure 2E added to the paper, Figure 3B'-D', Figure 5C and Figure S2F-H). Previously, we had only quantified protein release from n.t. controls and Disp-/- cells in the presence but not in the absence of Scube2 under serum-depleted conditions. Quantifications of serum-free protein release and Shh release under conditions ranging from 0.05% FCS to 10% FCS were completely missing from the earlier versions of the manuscript, but have now been added to our paper. In addition, we have reanalyzed all of the data sets in the above figures, as well as Figures 2C and S1B, to address the issue of "unusual normalization strategies": unlike previous assays in which the highest amount of protein detected in the media was set to 100% and all other proteins in that experiment were expressed relative to that value, we now directly compare the relative amounts of cellular and corresponding solubilized proteins as a method to quantify release without the need for data normalization (Figs. 1A'-D', 2C,E, 3B'-D', E, 5C, Fig. S1B, S2F-H).

We have also repeated the qPCR analyses in C3H10T1/2 cells and now show that the same Shh/C25AShh activities can be observed when using another Shh responsive cell line, NIH3T3 cells (Fig. 4B, 6B, fig. S5B).

We would like to point out that if the criticism refers to the presentation of our RP-HPLC and SEC data, the normalization of the strongest eluted protein signal to 100% for all proteins tested is necessary to put their behavior in a clearer relationship. This is because only the relative positions of protein elution, and not their amounts, are important in these experiments.

The significance of the data provided is overstated because many of the presented experiments confirm/support previously published work.

To mitigate the first reviewer's comment that the significance of the data presented is overstated, we now clearly distinguish between our novel results and the known aspect of Hh release on lipoproteins throughout our paper. We now clearly describe what is new and important in our paper: First, contrary to the general perception in the field, Disp and Scube2 are not sufficient to solubilize Shh, casting doubt on the currently accepted model that Scube2 accepts dual-lipidated Shh from Disp and transports it to the receptor Ptch. Second, lipoproteins shift dual Shh processing to N-terminal peptide processing only to generate different soluble Hh forms with different activities (as shown in Figure 4C). Third, and again contrary to popular belief, this new release mode does not inactivate Shh, as we now show in two established cellular assays for Hh biofunction (Figures 4A-C, 5B'', 6B and S5C-G). Fourth, and most importantly, we show that spatiotemporally controlled, Disp-, Scube2- and HDL-mediated Shh release absolutely requires dual lipidation of the membrane-associated Shh precursor prior to its release. This finding (as shown in Figures 1 and S2) changes the interpretation of previously published in vivo data that have long been interpreted as evidence for the requirement of dual Shh lipidation for full receptor binding and activation.

The study provides a modest advance in our understanding of the complex issue of Shh membrane extraction.

Although we agree that our results integrate our novel observations into previously established concepts of Hh release and trafficking, we also hope that our data cast well-founded doubt on the current view that the issue of Hh release and trafficking is largely resolved by the model of Disp-mediated Shh hand-over to Scube2 and then to Ptch, which requires interactions with both Shh lipids. Our data show that this is clearly not the case in the presence of lipoproteins. Thus, the significance of our data is that models of Shh lipid-regulated signaling to Ptch obtained using the dual-lipidated Shh precursor prior to its Disp- and Scube2-mediated conversion into a delipidated or monolipidated, HDL-associated soluble ligand are likely to describe a non-physiological interaction. Instead, our work describes a highly bioactive soluble ligand with only one lipid still attached, which has not been described before in the literature. The in vivo endpoint analyses presented in Fig. S8 suggest that this new protein variant is likely to play an important role during development.

Reviewer #2 (Public Review):

The precise molecular identity (of the released Shh) remains to be defined.

We would like to respond that the direct comparison of soluble proteins and their well-defined double-lipidated precursors side-by-side in the same experiment, as shown in our paper, determines all relevant molecular changes in the Shh release process. Most importantly, we show by SDS-PAGE and RP-HPLC that HDL restricts Shh processing to the N-terminus and that the absence of HDL results in double processing of Shh during its release. We also show by SEC that the C-terminus binds the protein to HDL. In addition, the fly experiments confirm the requirement for N-terminal Hh processing, but not for processing of the C-terminal peptide, and suggest that the N-terminal Cardin-Weintraub sequence replaced by the functionally blocking tag represents the physiological cleavage site.

It would be important to demonstrate key findings in cells that secrete Shh endogenously.

We now confirm the key findings of our study in Panc1 cells that endogenously produce and secrete Shh: As shown in Fig. S1D, we find that soluble proteins are processed but retain the C-cholesterol, which we now directly confirm by RP-HPLC (Fig. S4F-H). The in vivo analyses shown in Fig. S8 suggest that the key finding - that N-terminal but not C-terminal Hh shedding is required for release - can be supported, at least in the fly: here, Hh variants impaired in their ability to be processed N-terminally strongly repress the endogenous protein, whereas the same protein impaired in its ability to be processed C-terminally does not.

The authors detect Shh variants that are expressed independently of Disp and Scube2 in secretion assays, but are excluded from interpretation as experimental artifacts.

We agree with the reviewer's criticism that the amounts of Shh released independently of Disp and Scube2 in secretion assays were not quantified and analyzed statistically to justify their proposed status as not physiologically relevant. We now show that these forms are indeed secretion artifacts (Fig. 3E and Fig. S2F-H show quantification of the lower electrophoretic mobility protein fraction (i.e., the "top" band representing the double-lipidated soluble protein fraction)) because this fraction is released independently of Disp and Scube2.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This interesting study explores the mechanism behind an increased susceptibility of daf-18/PTEN mutant nematodes to paralyzing drugs that exacerbate cholinergic transmission. The authors use state-of-theart genetics and neurogenetics coupled with locomotor behavior monitoring and neuroanatomical observations using gene expression reporters to show that the susceptibility occurs due to low levels of DAF-18/PTEN in developing inhibitory GABAergic neurons early during larval development (specifically, during the larval L1 stage). DAF-18/PTEN is convincingly shown to act cell-autonomously in these cells upstream of the PI3K-PDK-1-AKT-DAF-16/FOXO pathway, consistent with its well-known role as an antagonist of this conserved signaling pathway. The authors exclude a role for the TOR pathway in this process and present evidence implicating selectivity towards developing GABAergic neurons. Finally, the authors show that a diet supplemented with a ketogenic body, β-hydroxybutyrate, which also counteracts the PI3K-PDK-1-AKT pathway, promoting DAF-16/FOXO activity, partially rescues the proper development (morphology and function) of GABAergic neurons in daf-18/PTEN mutants, but only if the diet is provided early during larval development. This strongly suggests that the critical function of DAF18/PTEN in developing inhibitory GABAergic neurons is to prevent excessive PI3K-PDK-1-AKT activity during this critical and particularly sensitive period of their development in juvenile L1 stage worms. Whether or not the sensitivity of GABAergic neurons to DAF-18/PTEN function is a defining and widespread characteristic of this class of neurons in C. elegans and other animals, or rather a particularity of the unique early-stage GABAergic neurons investigated remains to be determined.

Strengths:

The study reports interesting and important findings, advancing the knowledge of how daf-18/PTEN and the PI3K-PDK-1-AKT pathway can influence neurodevelopment, and providing a valuable paradigm to study the selectivity of gene activities towards certain neurons. It also defines a solid paradigm to study the potential of dietary interventions (such as ketogenic diets) or other drug treatments to counteract (prevent or revert?) neurodevelopment defects and stimulate DAF-16/FOXO activity.

Weaknesses:

(1) Insufficiently detailed methods and some inconsistencies between Figure 4 and the text undermine the full understanding of the work and its implications.

The incomplete methods presented, the imprecise display of Figure 4, and the inconsistency between this figure and the text, make it presently unclear what are the precise timings of observations and treatments around the L1 stage. What exactly do E-L1 and L1-L2 mean in the figure? The timing information is critical for the understanding of the implications of the findings because important changes take place with the whole inhibitory GABAergic neuronal system during the L1 stage into the L2 stage. The precise timing of the events such as neuronal births and remodelling events are welldescribed (e.g., Figure 2 in Hallam and Jin, Nature 1998; Fig 7 in Mulcahy et al., Curr Biol, 2022). Likewise, for proper interpretation of the implication of the findings, it is important to describe the nature of the defects observed in L1 larvae reported in Figure 1E - at present, a representative figure is shown of a branched commissure. What other types of defects, if any, are observed in early L1 larvae? The nature of the defects will be informative. Are they similar or not to the defects observed in older larvae?

We thank the reviewer for highlighting these areas for improvement. We have updated and clarified the timing of observation in the text, figures, and methodology section accordingly.

All experiments were conducted using age-synchronized animals. Gravid worms were placed on NGM plates and removed after two hours. The assays were then carried out on animals that hatched from the eggs laid during this specific timeframe.

Regarding the detailed timings outlined in the original Figure 4 (now Figure 5 in the revised version), we provided the following information in the revised version: For experiments involving continuous exposure to βHB throughout development, the gravid worms were placed on NGM plates containing the ketone body and removed after two hours. Therefore, this exposure covered the ex-utero embryonic development period up to the L4-Young adult stage when the experiments were conducted.

In experiments involving exposure at different developmental stages as those depicted in Figure 4 of the original version, (now Figure 5, revised version), animals were transferred between plates with and without βHB as required. We exposed daf-18/PTEN mutant animals to βHB-supplemented diets for 18-hour periods at different developmental stages (Figure 5A, revised version). The earliest exposure occurred during the 18 hours following egg laying, covering ex-utero embryonic development and the first 8-9 hours of the L1 stage. The second exposure period encompassed the latter part of the L1 stage, the entire L2 stage, and most of the L3 stage. The third exposure spanned the latter part of the L3 stage (~1-2 hours), the entire L4 stage, and the first 6-7 hours of the adult stage.

All this information has been conveniently included in Figure 5, text (Page13, lines 259-276), and in methodology (Page 4, Lines 85-90, Revised Methods and Supplementary information) of the revised manuscript.

In response to the reviewer's suggestion, we have also included photos of daf-18 worms at the L1 stage (30 min/1h post-hatching). Defects are already present at this early stage, such as handedness and abnormal branching commissures, which are also observed in adult worm neurons (see Supplementary Figure 4, revised version). 

These defects manifest in DD neurons shortly after larval birth. The prevalence of animals with errors is higher in L4 worms (when both VDs and DDs are formed) compared to early L1s (Figures 3 C-E and Supplementary Figure 4, revised version). This suggests that defects in VD neurons also occur in daf-18 mutants. Indeed, when we analyzed the neuronal morphology of several wild-type and daf-18 mutant animals, we found defects in the commissures corresponding to both DD and VD neurons (Supplementary Figure 3, revised version). 

These data are now included in the revised version (Results (Page 10, lines 177-196), Discussion (Pages 14-16), Main Figure 3, and Supplementary Figures 3, 4 and 7 revised version)

(2) The claim of proof of concept for a reversal of neurodevelopment defects is not fully substantiated by data.

The authors state that the work "constitutes a proof of concept of the ability to revert a neurodevelopmental defect with a dietary intervention" (Abstract, Line 56), however, the authors do not present sufficient evidence to distinguish between a "reversal" or prevention of the neurodevelopment defect by the dietary intervention. This clarification is critical for therapeutic purposes and claims of proof-of-concept. From the best of my understanding, reversal formally means the defect was present at the time of therapy, which is then reverted to a "normal" state with the therapy. On the other hand, prevention would imply an intervention that does not allow the defect to develop to begin with, i.e., the altered or defective state never arises. In the context of this study, the authors do not convincingly show reversal. This would require showing "embryonic" GABAergic neuron defects or showing convincing data in newly hatched L1 (0-1h), which is unclear if they do so or not, as I have failed to find this information in the manuscript. Again, the method description needs to be improved and the implications can be very different if the data presented in Figure 2D-E regard newly born L1 animals (0-1h) or L1 animals at say 5-7h after hatching. This is critical because the development of the embryonically-born GABAergic DD neurons, for instance, is not finalized embryonically. Their neurites still undergo outgrowth (albeit limited) upon L1 birth (see DataS2 in Mulcahy et al., Curr Biol 2022), hence they are susceptible to both committing developmental errors and to responding to nutritional interventions to prevent them. In contrast to embryonic GABAergic neurons, embryonic cholinergic neurons (DA/DB) do not undergo neurite outgrowth post-embryonically (Mulcahy et al., Curr Biol 2022), a fact which could provide some mechanistic insight considering the data presented. However, neurites from other post-embryonically-born neurons also undergo outgrowth postembryonically, but mostly during the second half of the L1 stage following their birth up to mid-L2, with significant growth occurring during the L1-L2 transition. These are the cholinergic (VA/VB and AS neurons) and GABAergic (VD) neurons. The fact that AS neurons undergo a similar amount of outgrowth as VD neurons is informative if VD neurons are or are not susceptible to daf-18/PTEN activity. Independently, DD neurons are still quite unique on other aspects (see below), which could also bring insight into their selective response.

Finally, even adjusting the claim to "constitutes a proof-of-concept of the ability of preventing a neurodevelpmental defect with a dietary intervention" would not be completely precise, because it is unclear how much this work "constitutes a proof of concept". This is because, unless I misunderstood something, dietary interventions are already applied to prevent neurodevelopment defects, such as when folic acid supplementation is recommended to pregnant women to prevent neural tube defects in newborns.

Thank you very much for pointing out this issue and highlighting the need to further investigate the ameliorative capacity of βHB on GABAergic defects in daf-18 mutants. In the revised version, we have included experiments to address this point.

Our microscopy analyses strongly indicate that the development of DD neurons is affected, with errors observed as early as one-hour post-hatching (Main Figure 3, and Supplementary Figures  4 and 7, revised version). Additionally, based on the position of the commissures in L4s, our results strongly suggest that VD neurons are also affected (Supplementary Figure 3, revised version). Both, the frequency of animals with errors and the number of errors per animal are higher in L4s compared to L1 larvae (Main Figures 3,  and Supplementary Figure 4 and 7, revised version). It is very likely that the errors in VD neurons, which are born in the late L1 stage, are responsible for the higher frequency of defects observed in L4 animals. 

As the reviewer noted, GABAergic DD neurons, which are born embryonically, do not complete their development during the embryonic stages. Some defects in DD neurons may arise during the postembryonic period. Following the reviewer's suggestion, we analyzed L1 larvae at different times before the appearance of VDs (1 hour post-hatching and 6 hours post-hatching). We did not observe an increase in error prevalence, suggesting that DD defects in daf-18 mutants are mostly embryonic (Supplementary Fig 4B, Revised Version). 

Our findings suggest that βHB's enhancement is not due to preventive effects in DDs, as defects persist in newly hatched larvae regardless of βHB presence (Supplementary Figure 7, revised version), and postembryonic DD growth does not introduce new errors (Supplementary Figure 4, revised version). This lack of preventive effect could be due to βHB's limited penetration into the embryonic environment. Unlike early L1s, significant improvement occurs in L4s upon βHB early exposure (Supplementary Figure 7, revised version). This could be explained by a reversing effect on malformed DD neurons and/or a protective influence on VD neuron development. While we cannot rule out the first option, even if all errors in DDs in L1 were repaired (which is very unlikely), it wouldn't explain the level of improvement in L4 (Supplementary Figure 7, revised version). Therefore, we speculate that VDs may be targeted by βHB. The notion that exposure to βHB during early L1 can ameliorate defects in neurons primarily emerging in late L1s (VDs) is intriguing. We may hypothesize that residual βHB or a metabolite from prior exposure could forestall these defects in VD neurons. Notably, βHB has demonstrated a capacity for long-lasting effects through epigenetic modifications (Reviewed in He et al, 2023, https://doi.org/10.1016%2Fj.heliyon.2023.e21098). More work is needed to elucidate the underlying fundamental mechanisms regarding the ameliorating effects of βHB supplementation. We have now discussed these possibilities under discussion (Page 17, lines 369-383, revised version).

We agree with the reviewer that the term "reversal" is not accurate, and we have avoided using this terminology throughout the text. Furthermore, in the title, we have decided to change the word "rescue" to "ameliorate," as our experiments support the latter term but not the former. Additionally, the reviewer is correct that folic acid administration to pregnant women is already a metabolic intervention to prevent neural tube defects. In light of this, we have avoided claiming this as proof of concept in the revised manuscript 

(3) The data presented do not warrant the dismissal of DD remodeling as a contributing factor to the daf-18/PTEN defects.

Inhibitory GABAergic DD neurons are quite unique cells. They are well-known for their very particular property of remodeling their synaptic polarity (DD neurons switch the nature of their pre- and postsynaptic targets without changing their wiring). This process is called DD remodeling. It starts in the second half of the L1 stage and finishes during the L2 stage. Unfortunately, the fact that the authors find a specific defect in early GABAergic neurons (which are very likely these unique DD neurons) is not explored in sufficient detail and depth. The facts that these neurons are not fully developed at L1, that they still undergo limited neurite growth, and that they are poised for striking synaptic plasticity in a few hours set them apart from the other explored neurons, such as early cholinergic neurons, which show a more stable dynamics and connectivity at L1 (see Mulcahy et al., Curr Biol 2022).

The authors use their observation that daf-18/PTEN mutants present morphological defects in GABAergic neurons prior to DD remodeling to dismiss the possibility that the DAF-18/PTEN-dependent effects are "not a consequence of deficient rearrangement during the early larval stages". However, DD remodeling is just another cell-fate-determined process and as such, its timing, for instance, can be affected by mutations in genes that affect cell fates and developmental decisions, such as daf-18 and daf-16, which affect developmental fates such as those related with the dauer fate. Specifically, the authors do not exclude the possibility that the defects observed in the absence of either gene could be explained by precocious DD remodeling. Precocious DD remodeling can occur when certain pathways, such as the lin-14 heterochronic pathway, are affected. Interestingly, lin-14 has been linked with daf16/FOXO in at least two ways: during lifespan determination (Boehm and Slack, Science 2005) and in the

L1/L2 stages via the direct negative regulation of an insulin-like peptide gene ins-33 (Hristova et al., Mol Cell Bio 2005). It is likely that the prevention of DD dysfunction requires keeping insulin signaling in check (downregulated) in DD neurons in early larval stages, which seems to coincide with the critical timing and function of daf-18/PTEN. Hence, it will be interesting to test the involvement of these genes in the daf-18/daf-16 effects observed by the authors.

This is another interesting point raised by the reviewer. We have demonstrated that defects manifest in early L1 (30 min-1 hour post-hatching) which corresponds to a pre-remodeling time in wild-type worms.

We acknowledge the possibility of early remodeling in specific mutants as pointed out by the reviewer.

However, the following points suggest that the effects of these mutations may extend beyond the particularity of DD remodeling: i) Our experiments also show defects in VD neurons in daf-18 mutants (Supplementary Figure 3, revised version), as discussed in our previous response. These neurons do not undergo significant remodeling during their development. ii) DAF-18 and DAF-16 deficiencies produce neurodevelopmental alteration on other Non-Remodeling Neurons: Severe neurite defects in neurons that are nearly fully formed at larval hatching, such as AIY in daf-18 and daf-16 mutants, have been previously reported (Christensen et al., 2011). Additionally, the migration of another neuron, HSN, is severely affected in these mutants (Kennedy et al., 2013). iii) To the best of our knowledge, DD remodeling only alters synaptic polarity without forming new commissures or significant altering the trajectory of the formed ones. Thus, it is unlikely (though not impossible) for remodeling defects to cause the observed commissural branching and handedness abnormalities in DD neurons. Therefore, we think that the impact of daf-18 mutations on GABAergic neurons is not primarily linked to DD remodeling but extends to various neuron types. It is intriguing and requires further exploration in the future, the apparent resilience of cholinergic motor neurons to these mutations. This resilience is not limited to daf18/PTEN animals since mutants in certain genes expressed in both neuron types (such as neuronal integrin ina-1 or eel-1, the C. elegans ortholog of HUWE1) alter the function or morphology of GABAergic neurons but not cholinergic motor neurons (Kowalski, J. R. et al. Mol Cell Neurosci 2014; Oliver, D. et al. J Dev Biol (2019); Opperman, K. J. et al. Cell Rep 2017). These points are discussed in the manuscript (Discussion, page 15, lines 311-322, revised version) and reveal the existence of compensatory or redundant mechanisms in these excitatory neurons, rendering them much more resistant to both morphological and functional abnormalities.

Discussion on the impact of the work on the field and beyond:

The authors significantly advance the field by bringing insight into how DAF-18/PTEN affects neurodevelopment, but fall short of understanding the mechanism of selectivity towards GABAergic neurons, and most importantly, of properly contextualizing their findings within the state-of-the-art C. elegans biology.

For instance, the authors do not pinpoint which type of GABAergic neuron is affected, despite the fact that there are two very well-described populations of ventral nerve cord inhibitory GABAergic neurons with clear temporal and cell fate differences: the embryonically-born DD neurons and the postembryonically-born VD neurons. The time point of the critical period apparently defined by the authors (pending clarifications of methods, presentation of all data, and confirmation of inconsistencies between the text and figures in the submitted manuscript) could suggest that DAF-18/PTEN is required in either or both populations, which would have important and different implications. An effect on DD neurons seems more likely because an image is presented (Figure 2D) of a defect in an L1 daf-18/PTEN mutant larva with 6 neurons (which means the larva was processed at a time when VD neurons were not yet born or expressing pUnc-47, so supposedly it is an image of a larva in the first half of the L1 stage (0-~7h?)). DD neurons are also likely the critical cells here because the neurodevelopment errors are partially suppressed when the ketogenic diet is provided at an "early" L1 stage, but not later (e.g., from L2-L3, according to the text, L2-L4 according to the figure? ).

Thank you for this insightful input. As previously mentioned, we conducted experiments in this revision to clarify the specificity of GABAergic errors in daf-18/PTEN mutants, in particular, whether they affect DDs, VDs, or both. Our results suggest that commissural defects are not limited to DD neurons but also occur in VD neurons (Supplementary Figure 3). Regarding the effect of βHB, our findings suggest that VD neurons are targets of βHB action. As mentioned in the previous response and the discussion section (Page 17, lines 369-383, revised version), we might speculate that lingering βHB or a metabolite from prior exposure could mitigate these defects in VD neurons that are born in Late L1s-Early L2s. Additionally, βHB has been noted for its capacity to induce long-term epigenetic changes. Therefore, it could act on precursor cells of VD neurons, with the resulting changes manifesting during VD development independently of whether exposure has ceased. All these possibilities are now discussed in the manuscript.

Acknowledging that our work raises several questions that we aim to address in the future, we believe our manuscript provides valuable information regarding how the PI3K pathway modulates neuronal development and how dietary interventions can influence this process.

This study brings important contributions to the understanding of GABAergic neuron development in C. elegans, but unfortunately, it is justified and contextualized mostly in distantly-related fields - where the study has a dubious impact at this stage rather than in the central field of the work (post-embryonic development of C. elegans inhibitory circuits) where the study has stronger impact. This study is fundamentally about a cell fate determination event that occurs in a nutritionally-sensitive

developmental stage (post-embryonic L1 larval stage) yet the introduction and discussion are focused on more distantly related problems such as excitatory/inhibitory (E/I) balance, pathophysiology of human diseases, and treatments for them. Whereas speculation is warranted in the discussion, the reduced indepth consideration of the known biology of these neurons and organisms weakens the impact of the study as redacted. For instance, the critical role of DAF-18/PTEN seems to occur at the early L1 larval stage, a stage that is particularly sensitive to nutritional conditions. The developmental progression of L1 larvae is well-known to be sensitive to nutrition - eg, L1 larvae arrest development in the absence of food, something that is explored in nematode labs to synchronize animals at the L1 stage by allowing embryos to hatch into starvation conditions (water). Development resumes when they are exposed to food. Hence, the extensive postembryonic developmental trajectory that GABAergic neurons need to complete is expected to be highly susceptible to nutrition. Is it? The sensitivity towards the ketogenic diet intervention seems to favor this. In this sense, the attribution of the findings to issues with the nutrition-sensitive insulin-like signaling pathway seems quite plausible, yet this possibility seems insufficiently considered and discussed.

We greatly appreciate the reviewer's emphasis on the sensitivity of the L1 stage to nutritional status. As the reviewer points out, C. elegans adjusts its development based on food availability, potentially arresting development in L1 in the absence of food. It is therefore reasonable that both the completion of DD neuron trajectories and the initial development steps of VD neurons are particularly sensitive to dietary modulation of the insulin pathway, in which both DAF-18 and DAF-16 play roles. This important point has also been included in the discussion (Page 18, lines 384-407, revised version).

Finally, the fact that imbalances in excitatory/inhibitory (E/I) inputs are linked to Autism Spectrum Disorders (ASD) is used to justify the relevance of the study and its findings. Maybe at this stage, the speculation would be more appropriate if restricted to the discussion. In order to be relevant to ASD, for instance, the selectivity of PTEN towards inhibitory neurons should occur in humans too. However, at present, the E/I balance alteration caused by the absence of daf-18/PTEN in C. elegans could simply be a coincidence due to the uniqueness of the post-embryonic developmental program of GABAergic neurons in C. elegans. To be relevant, human GABAergic neurons should also pass through a unique developmental stage that is critically susceptible to the PI3K-PDK1-AKT pathway in order for DAF18/PTEN to have any role in determining their function. Is this the case? Hence, even in the discussion, where the authors state that "this study provides universally relevant information on.... the mechanisms underlying the positive effects of ketogenic diets on neuronal disorders characterized by GABA dysfunction and altered E/I ratios", this claim seems unsubstantiated as written particularly without acknowledging/mentioning the criteria that would have to be fulfilled and demonstrated for this claim to be true.

Our results suggest that defects in GABAergic neurons are not limited to DDs, which, as the reviewer rightly notes, are quite unique in their post-embryonic development primarily due to the synaptic remodeling process they undergo. These defects also extend to VD neurons, which do not exhibit significant developmental peculiarities once they are born. Therefore, we think that the defects are not specific to the developmental program of DD neurons but are more related to all GABAergic motoneurons. Additionally, the observation of defects in non-GABAergic neurons in C. elegans daf-18 mutants supports the hypothesis that the role of daf-18 is not limited to DD neurons (Christensen et al., 2011; Kennedy et al., 2013).

In mammals, Pten conditional knockout (cKO) animals have been extensively studied for synaptic connectivity and plasticity, revealing an imbalance between synaptic excitation and inhibition (E/I balance) (Reviewed in Rademacher and Eickholt, 2019, Cold Spring Harbor Perspect Med, https://doi.org/10.1101%2Fcshperspect.a036780). This imbalance is now widely accepted as a key pathological mechanism linked to the development of ASD-related behavior (Lee et al, 2017; Biological Psychiatry, https://doi.org/10.1016/j.biopsych.2016.05.011) . The importance of PTEN in the development of GABAergic neurons in mammals is well-documented. For instance, embryonic PTEN deletion from inhibitory neurons impacts the establishment of appropriate numbers of parvalbumin and somatostatin-expressing interneurons, indicating a central role for PTEN in inhibitory cell development (Vogt et al, 2015, Cell Rep, https://doi.org/10.1016%2Fj.celrep.2015.04.019). Additionally, conditional PTEN knockout in GABAergic neurons is sufficient to generate mice with seizures and autism-related behavioral phenotypes (Shin et al, 2021, Molecular Brain, https://doi.org/10.1186%2Fs13041-02100731-8). Moreover, while mice in which PV GABAergic neurons lacked both copies of Pten experienced seizures and died, heterozygous animals (PV-Pten+/−) showed impaired formation of perisomatic inhibition (Baohan et al, 2016, Nature Comm, OI: 10.1038/ncomms12829). Therefore, there is substantial evidence in mammals linking PTEN mutations to neurodevelopmental disorders in general and affecting GABAergic neurons in particular. Hence, we believe that the role of daf-18/PTEN in GABAergic development could be a more widespread phenomenon across the animal kingdom rather than a specific process unique to C. elegans.

Beyond the points discussed, we have addressed the reviewer's comment regarding the last sentence of the abstract. We have revised it to more cautiously frame the relationship between our findings, ASD, and mammalian neurodevelopmental disorders.

Reviewer #2 (Public Review):

Summary:

Disruption of the excitatory/inhibitory (E/I) balance has been reported in Autism Spectrum Disorders

(ASD), with which PTEN mutations have been associated. Giunti et al choose to explore the impact of PTEN mutations on the balance between E/I signaling using as a platform the C. elegans neuromuscular system where both cholinergic (E) and GABAergic (I) motor neurons regulate muscle contraction and relaxation. Mutations in daf-18/PTEN specifically affect morphologically and functionally the GABAergic (I) system, while leaving the cholinergic (E) system unaffected. The study further reveals that the observed defects in the GABAergic system in daf-18/PTEN mutants are attributed to reduced activity of DAF-16/FOXO during development.

Moreover, ketogenic diets (KGDs), known for their effectiveness in disorders associated with E/I imbalances such as epilepsy and ASD, are found to induce DAF-16/FOXO during early development. Supplementation with β-hydroxybutyrate in the nematode at early developmental stages proves to be both necessary and sufficient to correct the effects on GABAergic signaling in daf-18/PTEN mutants.

Strengths:

The authors combined pharmacological, behavioral, and optogenetic experiments to show the

GABAergic signaling impairment at the C. elegans neuromuscular junction in DAF-18/PTEN and DAF-

16/FOXO mutants. Moreover, by studying the neuron morphology, they point towards

neurodevelopmental defects in the GABAergic motoneurons involved in locomotion. Using the same set of experiments, they demonstrate that a ketogenic diet can rescue the inhibitory defect in the daf18/PTEN mutant at an early stage.

Weaknesses:

The morphological experiments hint towards a pre-synaptic defect to explain the GABAergic signaling impairment, but it would have also been interesting to check the post-synaptic part of the inhibitory neuromuscular junctions such as the GABA receptor clusters to assess if the impairment is only presynaptic or both post and presynaptic.

Moreover, all observations done at the L4 stage and /or adult stage don't discriminate between the different GABAergic neurons of the ventral nerve cord, ie the DDs which are born embryonically and undergo remodeling at the late L1 stage, and VDs which are born post-embryonically at the end of the L1 stage. Those additional elements would provide information on the mechanism of action of the FOXO pathway and the ketone bodies.

Thank you for your insightful suggestions. 

This is an initial study that serves as a cornerstone, demonstrating the sensitivity of GABAergic neuron development to alterations in the PI3K pathway and how these alterations can be mitigated by a dietary intervention with a ketone body. While we have determined that the transcription factor DAF-16/FOXO is essential in the neurodevelopmental process and is the target of ketone bodies to alleviate defects, there are still underlying mechanisms to be elucidated. This is only the first step that opens many avenues for further investigation, including the study of post-synaptic partners.

While our current study primarily focuses on neuronal alterations without delving into potential postsynaptic effects, we do plan to investigate this aspect in future research. This includes examining GABAergic receptors as well as cholinergic receptors, as exacerbation of cholinergic signaling cannot be ruled out. To conduct a comprehensive study of post-synaptic structure and functionality, we would need strains with fluorescent markers for both pre- and post-synaptic components (such as rab-3, unc-49, unc29, acr-16 fusion to GFP or mCherry). Unfortunately, most of these strains are not currently available in our laboratory. Unlike the US or Europe, acquiring these strains from the C. elegans CGC repository in Argentina is challenging due to common customs delays, which require significant time and resources to navigate. Discussions at the Latin American C. elegans conference with CGC administrators, such as Ann Rougvie, have been initiated to address this issue, but a solution has not been reached yet.  Additionally, to analyze post-synaptic functionality in-depth, studying the response to perfusion with various agonists using electrophysiology would be beneficial. We are in the process of acquiring the capability to conduct electrophysiology experiments in our laboratory, but progress is slow due to limited funding.

While we believe these experiments are very informative, they will require a considerable amount of time due to our current circumstances. We consider them non-essential to the primary message of the paper, which focuses on neuronal developmental defects leading to functional alterations in daf-18/PTEN mutants and the novel finding that these can be mitigated by supplementing food with hydroxybutyrate. We will study the structure and functionality of the post-synapse in our future projects and also plan to extend this investigation to mutants with deficiencies in genes closely related to neurodevelopmental defects, such as neuroligin, neurexin, or shank-3, which have been implicated in synaptic architecture.

We also agree that discriminating between DD and VD neurons provides significant insights into the neurodevelopmental phenomena dependent on the FOXO pathway and the action of βHB. In this revised version, we present evidence that not only DD neurons are affected but also VD neurons (see

Supplementary Figure 3, revised version). This allows us to suggest that daf-18 affects the development of GABAergic neurons regardless of whether they are born embryonically (DDs) or post-embryonically (VDs) (see also our response to the previous reviewer). We hope to distinguish the defects observed in each type of neuron in future studies. For this, we would need to use strains specifically marked in one neuronal type or another, which, for the same reasons mentioned earlier, would take a considerable amount of time under current conditions. 

Conclusion:

Giunti et al provide fundamental insights into the connection between PTEN mutations and neurodevelopmental defects through DAF-16/FOXO and shed light on the mechanisms through which ketogenic diets positively impact neuronal disorders characterized by E/I imbalances.  

Reviewer #3 (Public Review):

Summary:

This is a conceptually appealing study by Giunti et al in which the authors identify a role for PTEN/daf-18 and daf-16/FOXO in the development of inhibitory GABA neurons, and then demonstrate that a diet rich in ketone body β-hydroxybutyrate partially suppresses the PTEN mutant phenotypes. The authors use three assays to assess their phenotypes: (1) pharmacological assays (with levamisole and aldicarb); (2) locomotory assays and (3) cell morphological assays. These assays are carefully performed and the article is clearly written. While neurodevelopmental phenotypes had been previously demonstrated for PTEN/daf-18 and daf-16/FOXO (in other neurons), and while KB β-hydroxybutyrate had been previously shown to increase daf-16/FOXO activity (in the context of aging), this study is significant because it demonstrates the importance of KB β-hydroxybutyrate and DAF-16 in the context of neurodevelopment. Conceptually, and to my knowledge, this is the first evidence I have seen of a rescue of a developmental defect with dietary metabolic intervention, linking, in an elegant way, the underpinning genetic mechanisms with novel metabolic pathways that could be used to circumvent the defects.

Strengths:

What their data clearly demonstrate, is conceptually appealing, and in my opinion, the biggest contribution of the study is the ability of reverting a neurodevelopmental defect with a dietary intervention that acts upstream or in parallel to DAF-16/FOXO.

Weaknesses:

The model shows AKT-1 as an inhibitor of DAF-16, yet their studies show no differences from wildtype in akt-1 and akt-2 mutants. AKT is not a major protein studied in this paper, and it can be removed from the model to avoid confusion, or the result can be discussed in the context of the model to clarify interpretation.

Thank you very much for the suggestion. We agree with the reviewer's appreciation that the study of AKT's action itself is too limited in this study to draw conclusions that would allow its inclusion in the proposed model. Therefore, following the reviewer's suggestion, we have removed this protein from our model

When testing additional genes in the DAF-18/FOXO pathway, there were no significant differences from wild-type in most cases. This should be discussed. Could there be an alternate pathway via DAF-18/DAF16, excluding the PI3K pathway or are there variations in activity of PI3K genes during a ketogenic diet that are hard to detect with current assays?

Thank you for bringing up this point. Our pharmacological experiments indeed demonstrate that all mutants associated with an exacerbation of the PI3K pathway, which typically inhibits nuclear translocation and activity of the transcription factor DAF-16, lead to imbalances in E/I

(excitation/inhibition) that manifest as hypersensitivity to cholinergic drugs. This includes the gain of function of pdk-1 and the loss of function of daf-18 and daf-16 itself. In our subsequent experiments, we demonstrate that this exacerbation of the PI3K pathway leads to errors in the neurodevelopment of GABAergic neurons, which explains the hypersensitivity to aldicarb and levamisole.

As the reviewer remarks, it is intriguing why mutants inhibiting this pathway do not show differences in their sensitivity to cholinergic drugs compared to wild-type animals. We can speculate, for instance, that during neurodevelopment, there is a critical period where the PI3K pathway must remain with very low activity (or even deactivated) for proper development of GABAergic neurons. This could explain why there are no differences in sensitivity to cholinergic drugs between mutants that inhibit the PI3K pathway and the wild type. The PI3K pathway depends on insulin-like signals, which are in turn positively modulated by molecules associated with the presence of food. Interestingly, larval stage 1 is particularly sensitive to nutritional status, being able to completely arrest development in the absence of food. Therefore, dietary intervention with BHB may generate a signal of dietary restriction (as seen in mammals) and, as a consequence of this dietary restriction, the PI3K pathway is inhibited, resulting in increased DAF-16 activity. This could restore the proper neurodevelopment of GABAergic neurons. However, this is mere speculation, and further deeper experiments (than the pharmacology ones we performed here) with mutants in different genes within the PI3K pathway may shed light on this point.

Following the reviewer's suggestion, this point has been discussed in the revised version of the manuscript. (Discussion Page 18, Lines 384-407).

The consequence of SOD-3 expression in the broader context of GABA neurons was not discussed. SOD3 was also measured in the pharynx but measuring it in neurons would bolster the claims.

SOD-3 is a known target of DAF-16. Previous studies have shown that βHB induces SOD-3 expression through the induction of DAF-16 (Edwards et al, 2014, Aging,

https://doi.org/10.18632%2Faging.100683). The highest levels of SOD-3 expression are typically observed in the pharynx or intestine (DeRosa et al, 2019 https://doi.org/10.1038/s41586-019-1524-5;  Zheng et al., 2021, PNAS, https://doi.org/10.1073/pnas.2021063118), and it is often used as a measure of general upregulation of DAF-16. Therefore, we used this parameter as a measure of βHB upregulating systemic DAF-16 activity.  While we agree with the reviewer that observing variations in SOD-3 expression in neurons would further support our conclusions, unfortunately, we did not detect measurable signals of SOD-3 in motor neurons in either the control condition or the daf-18 background even upon stress or BHB-exposure. This may be because SOD-3 is a minor target of DAF-16 in these neurons, or its modulation may not correspond to the timing of fluorescence measurements (L4-adults).

Despite this, our genetic experiments and neuron-specific rescue experiments lead us to conclude that DAF-16 must act autonomously in GABAergic neurons to ensure proper neurodevelopment.

If they want to include AKT-1, seeing its effect on SOD-3 expression could be meaningful to the model.

Thank you for this suggestion. We believe that even measuring SOD-3 levels in akt mutant backgrounds would still provide limited information to give it a predominant value in our work. Additionally, to have a complete understanding of the total role of AKT, it would be necessary to measure it in a double mutant background of akt-1; akt-2, and these double mutants generate 100 % dauers even at 15C (Oh et al., PNAS 2005, https://doi.org/10.1073/pnas.0500749102; Quevedo et al., Current Biology 2007, http://dx.doi.org/10.1016/j.cub.2006.12.038; Gatzi et al., PLOS ONE 2014,

https://doi.org/10.1371/journal.pone.0107671), greatly complicating the execution of these experiments. Therefore, following the first advice of this reviewer, we have decided to modify our model by excluding AKT.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

⁃ Please include earlier in the main text the rationale for using unc-25 as a control/reference already when mentioning Figure 1A.

Thank you for pointing out the need to reference this control earlier. We have included the following paragraph in the description of Figure 1 (Page 5, line 71, revised version):

“Hypersensitivity to cholinergic drugs is typical of animals with an increased E/I ratio in the neuromuscular system, such as mutants in unc-25 (the C. elegans orthologue for glutamic acid decarboxylase, an essential enzyme for synthesizing GABA). While daf-18/PTEN mutants become paralyzed earlier than wild-type animals, their hypersensitivity to cholinergic drugs is not as severe as that observed in animals completely deficient in GABA synthesis, such unc-25 null mutants (Figures 1B and 1C) indicating a less pronounced imbalance between excitatory and inhibitory signals.”

⁃ Please discuss the greater sensitivity of pdk-1(gf) animals to levamisole than to aldicarb.

Thank you for bringing up this subtle point.  We understand that the reviewer is referring to the paralysis curve in response to aldicarb in pdk-1(gf), which is closer to unc-25 than the curve for levamisole (in both cases, they are more sensitive than the wild type). Therefore, pdk-1(gf) animals seem to be more sensitive to aldicarb than to levamisole. These results are now shown in Figure 1D (revised version).

The PI3K pathway does not only act in neurons but also in muscles. Gain of function in pdk-1 has been shown to modulate muscle protein degradation (Szewczyk et al, EMBO Journal, 2008. https://doi.org/10.1038/sj.emboj.7601540). In contrast,  no effect on protein degradation has been reported for null mutants in this gene. Several studies have demonstrated that protein degradation levels can differentially affect receptor subunits, particularly acetylcholine receptors (Reviewed in Crespi et al, Br J Pharmacol, 2018). C. elegans is characterized by a wide repertoire of AChR subunits, and there are at least two subtypes of ACh receptors in muscles (one multimeric sensitive to levamisole and one homomeric (ACR-16) insensitive to levamisole) (Richmond et al, 1999 Nature Neuroscience http://dx.doi.org/10.1038/12160; Touroutine D, JBC 2005 https://doi.org/10.1074/jbc.M502818200).

Interestingly, acr-16 null mutants are hypersensitive to aldicarb (Zeng et al, JCB, 2023, https://doi.org/10.1083/jcb.202301117) while the electrophysiological response to levamisole in this mutant remains similar to that of wild-type (Tourorutine et al, 2005). Therefore, it may be that the gain of function in pdk-1 induces a change in the expression of AChR subtypes in muscle that differentially affect sensitivity to levamisole and ACh. This is purely speculative, and there may be many other explanations. While it would be interesting to explore this difference further, it goes far beyond the scope of this study. The cholinergic drug sensitivity assay is purely exploratory and allowed us to delve into the GABAergic and cholinergic signals in daf-18 mutants. In this sense, the hypersensitivity of pdk-1(gf) to both drugs supports the idea that an increase in PI3K signaling leads to an increased E/I ratio.

⁃ Please explain the rationale to perform akt-1 and akt-2 assays separated. Why not test doublemutants? Has their lack of redundancy been determined?.  

Our pharmacological assays are conducted at the L4 larval stage, making it impossible to analyze the potential redundancy of akt-1 and akt-2 in sensitivity to levamisole and aldicarb. This impossibility arises because the akt-1;akt-2 double mutant exhibits nearly 100% arrest as dauer even at 15°C, as reported in several prior studies (Oh et al., PNAS 2005, https://doi.org/10.1073/pnas.0500749102; Quevedo et al., Current Biology 2007, http://dx.doi.org/10.1016/j.cub.2006.12.038; Gatzi et al., PLOS ONE 2014, https://doi.org/10.1371/journal.pone.0107671). While the increased dauer arrest in the double mutant compared to the single mutants might suggest redundant functions in dauer entry, there are also reports indicating the absence of redundancy in other processes, such as vulval development (Nakdimon et al., PLOS Genetics 2012, https://doi.org/10.1371%2Fjournal.pgen.1002881).

The complete Dauer arrest likely underlies why other studies focusing on the role of the PI3K pathway in neurodevelopment utilize both mutants separately (Christensen et al, Development 2011,

https://doi.org/10.1242/dev.069062). While determining the potential redundancy of these genes is not feasible for this assay, we utilized various mutants of the pathway (age-1, pdk-1, daf-18, daf-16 and daf16;daf-18 in addition to the akt-s) that support the conclusion, which is that exacerbating the PI3K pathway activity makes animals hypersensitive to cholinergic drugs.

In response to the reviewer's concern, we have added a sentence in the text explaining the impossibility of performing the assay in the akt-1;akt-2 double mutant (Page 6, lines90-92) 

Figure 1C and D (This applies to all similarly presented bar figures). Please show data points and dispersion (preferably data, median+- 25-75% or average+-SD). 

Thank you. Done

⁃ Line 112 -maybe "and resumes"? 

Thank you. Done (Line 126, revised version)

⁃ Figure 1E and F. Please present mean +-SD (not SEM) of fluctuations. Please change slightly the tones so that the dispersion is easier to distinguish on the "blue light on" box.

Thank you for the suggestion. We have adjusted the tones as recommended to enhance the visualization of the "blue light on" box. For visualization purposes, we present the shading of the standard error of the mean (SEM), as is usual in these types of optogenetic experiments where traces of animal length variations are measured (Liewald et al, Nature Methods, 2008, doi: 10.1038/nmeth.1252; Schulstheis et al, J. Neurophysiology, 2011, doi: 10.1152/jn.00578.2010; Koopman et al, BMC Biology 2021, https://doi.org/10.1186/s12915-021-01085-2; Seidhenthal et al, Micro Publication Biology, 2022, https://doi.org/10.17912%2Fmicropub.biology.000607 ).

For the revised version, we have also included bar graphs for each optogenetic experiment, representing the mean of the length average of each worm measured from the first second after the blue light was turned on until the second before the light was turned off (in the graph, this corresponds to the period between seconds 6 and 9 of the traces). These graphs include the standard deviation and the corresponding significance levels. All of this has been included in the new legend (Figure 2D, 2E, 4E-J).

⁃ Figure 1A&1B & Supplementary Figure 1D x Supplementary Figure 1E&1F. What is the difference between these experiments? Whereas the unc-25 mutants paralyze in the same amount of time, the WT animals paralyze ~1 h later in Supplementary Figure 1E-1F in response to either drug. Please revise experimental conditions to see if anything can be learned eg, maybe this is a nutritional response from experiments done at different timepoints? Maybe different food recipes affected sensitivity to paralysis?

Thank you for pointing this out. While the experiments with daf-18 (in both alleles) and daf-16 were conducted at the beginning of this project (2019-2020), the assays with the other mutants in the PI3K and mTOR pathways were performed years later. Changes in the reagents used (agar, peptone, cholesterol, etc.) to grow the worms have occurred, potentially altering the animals' response directly or through the nutritional quality of the bacteria they grow on. In addition, the difference may be attributed to the fact that experiments at the project's outset were conducted by one author, while more recent experiments were carried out by another. The goal is to quantify paralysis in non-responsive worms after touch stimulation. The force of this probing or the thickness of the hair used for touching can be slightly operator-dependent and can lead to variable responses. In addition, always the presence of wild-type and unc-25 strain is included as internal control in every experiment. Nevertheless, despite this userdependent variation, the experiments were always conducted blindly (except for unc-25, whose uncoordinated phenotype is easily identifiable), thus we trust in the outcomes.

⁃ Supplementary Figure 1G - Length and Width appear to be switched in both left and right panels - please revise and include a description of N and of statistics depicted. 

Unfortunately, we don't see the switching error that the reviewer mentioned. In the left panel, we demonstrate that optogenetic activation of GABAergic neurons leads to an increase in length without modifying the width of the animal. Therefore, we conclude that the increase in area, as observed in our Fiji macro for optogenetic response analysis, is due to an increase in the animal's length. In the cholinergic activation shown in the right panel, the animal shortens (decreasing length) without modifying the width, resulting in the reduction of the total body area. 

We have included information about N (sample size) and the statistical test used in the legends as suggested. These graphs are now shown as Figures 2F and G, revised version.

⁃ Supplementary Figure 1G legend lines 779-780. Please describe the post-hoc test applied following ANOVA to obtain the denoted p values. This applies to all datasets where ANOVA or Krusal-Wallis tests were applied.

Following reviewer´s suggestion, all the post-hoc tests applied after ANOVA or Kruskal-Wallis analysis were included in the legend of each figure and Materials and Methods (statistical analysis section).

⁃ Line 174 maybe "arises *from* the hyperactivation" instead of *for*?.

Corrected. Thank you. Line 190, revised version.

⁃ Supplementary Figure 4. On line 816 it says n=40-90, but please check the n of the daf-18, daf-16 samples, which seem to have less than 40 animals.

We understand that the reviewer is referring to Supplementary Figure 3 from the original version (now Supplementary Figure 5 in the revised version). We have now included the number of observations below each data point cloud to clearly indicate the sample size for each condition

⁃ Supplementary Figure 4 - please state what are the bars on the graphs. Please state which post-hoc test was performed after Kruskal-Wallis and present at least the p values obtained between treated controls and each genotype. Alternatively, present the whole truth table in supplementary daita.

We understand that the reviewer is referring to Supplementary Figure 3 from the original version (now Supplementary Figure 5 in the revised version). There was an error in the original legend (thank you for bringing this to our attention) since the statistics were not performed using Kruskall-Wallis in this case, but rather each treated condition was compared to its own untreated control using Mann-Whitney test. We have now added the p-values to the graph. All raw data for this figure, as well as for all other figures, are available in Open Science Framework (https://osf.io/mdpgc/?view_only=3edb6edf2298421e94982268d9802050).

⁃ Please cite the figure panels in order: eg, Figure 3E is mentioned in the text after panels Figure 3F-K.

Done. We have rearranged the figures to adapt them to the text order (Figure 4, revised version)

⁃ Figure 4 - line 610 please revise "(n=20-30 (n: 20-25 animals per genotype/trial)."

Thank you. Corrected.

⁃ Figure 4 - there appears to be an inconsistency in the figure with the text (lines 223-225). In figures it says E-L1, but in the text, it says "solely in L1". Does E-L1 include the whole L1 stage? If not- E-L1 can be interpreted only as during the embryonic stage, hence, no exposure to betaHB due to the impermeable chitin eggshell. Then there is L1-L2, which should cover the L1 stage and the L2 or something else. Please revise. The text mentions L2-L3 or L3-L4 and these categories are not in the figures. This clarification is key for the interpretation of the results. The precise developmental time of the exposures is not defined either in the methods or in the figures. Please provide precise times relative to hours and/or molts and revise the text/figure for consistency.

The reviewer is entirely correct in pointing out the lack of relevant data regarding the exposure time to βHB. We have now clarified the information For the revised version, we have adjusted the nomenclature of each exposure period to precisely reflect the developmental stages involved.

For the experiments involving continuous exposure to βHB throughout development, the NGM plate contained the ketone body. Therefore, the exposure encompassed, in principle, the ex-utero embryonic development period up to L4-Young adults (E-L4/YA, in Figure 5A) when the experiments were conducted. Since it could be a restriction to drug penetration through the chitin shell of the eggs (see Supplementary Figure 7), we can ensure βHB exposure from hatching.

In experiments involving exposure at different developmental stages as those depicted in Figure 4 of the original version, (now Figure 5), animals were transferred between plates with and without βHB as required. We exposed daf-18/PTEN mutant animals to βHB-supplemented diets for 18-hour periods at different developmental stages (Figure 5A). The earliest exposure occurred during the 18 hours following egg laying, covering ex-utero embryonic development and the first 8-9 hours of the L1 stage (This period is called E-L1, in figure 5 revised version). The second exposure period encompassed the latter part of the L1 stage, the entire L2 stage, and most of the L3 stage (L1-L3). The third exposure spanned the latter part of the L3 stage (~1-2 hours), the entire L4 stage, and the first 6-7 hours of the adult stage (L3-YA).

All this information has been conveniently included in Figure 5 (and its legend), text (Page 13, lines 259276), and Material and Methods of the revised manuscript.

⁃ Some methods are not sufficiently well described. Specifically, how the animals were exposed to treatments and how stages were obtained for each experiment. Was synchronization involved? If so, in which experiments and how exactly was it performed?

As mentioned in previous responses all the experiments were performed in age-synchronized animals. We include the following sentence in Materials and Methods (C. elegans culture and maintenance section): “All experiments were conducted on age-synchronized animals. This was achieved by placing gravid worms on NGM plates and removing them after two hours. The assays were performed on the animals hatched from the eggs laid in these two hours”.

Reviewer #2 (Recommendations For The Authors):

Major points

(1) To complete the study on the GABAergic signaling at the NMJs, it would be interesting to assess the status of the post-synaptic part of the synapse such as the GABAR clustering. It would also tell if the impairment is only presynaptic or both post and presynaptic.

Thank you for your insightful suggestion. We agree that exploring post-synaptic elements can shed light on whether the impairment is solely presynaptic or involves both pre and post-synaptic components.

While our current study primarily focuses on neuronal alterations without delving into potential postsynaptic effects, we do plan to investigate this aspect in the future. This includes not only examining GABAergic receptors but also exploring cholinergic receptors, as exacerbation of cholinergic signaling cannot be ruled out. To conduct a comprehensive study of post-synaptic structure and functionality, we would need strains with fluorescent markers for both pre and post-synaptic components (rab-3, unc-49, unc-29, acr-16 driving GFP or mCherry). However, most of these strains are not currently available in our laboratory. Unlike the US or Europe, acquiring these strains from the C. elegans CGC repository in Argentina is challenging due to common customs delays, requiring significant time and resources to navigate. Discussions at the Latin American C. elegans conference with CGC administrators, such as Ann Rougvie, have been initiated to address this issue, but a solution has not been reached yet. 

Additionally, to analyze post-synaptic functionality in-depth, studying the response to perfusion with various agonists using electrophysiology would be beneficial. We are in the process of acquiring the capability to conduct electrophysiology experiments in our laboratory, but progress is slow due to limited funding.

While we believe these experiments are very informative, they will require a considerable amount of time due to our current circumstances. We consider them non-essential to the primary message of the paper, which focuses on neuronal morphological defects leading to functional alterations in daf-18/PTEN mutants.

We will include these experiments in our future projects, also planning to extend this investigation to mutants with deficiencies in genes closely related to neurodevelopmental defects, such as neuroligin, neurexin, or shank-3, which have been implicated in synaptic architecture.

(2) The author always referred to unc-47 promoter or unc-17 promoter, never specifying where those promoters are driving the expression (and in the Materials & Methods, no information on the corresponding sequence). Depending on the promoters they may not only be expressed in the motoneurons involved in locomotion (VA, VB, DA, DB, VD, and DD), but they could also be expressed in other neurons which could be of importance for the conclusions of the optogenetic assays but also the daf-18 expression in GABAergic neurons.

We appreciate the reviewer's insight regarding the broader expression patterns of the unc-17 and unc-47 promoters in all cholinergic and GABAergic neurons, respectively. The strains expressing constructs with these promoters were obtained from the CGC or other labs and have been widely used in previous papers (Liewald et al, Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008); Byrne, A. B. et al. Neuron 81, 561-573, doi:10.1016/j.neuron.2013.11.019 (2014).

Regarding the optogenetic assays, the readout utilized (body length elongation or contraction) is primarily associated with the activity of cholinergic and GABAergic motor neurons and has been used in numerous studies to measure motor neuron functionality (Liewald et al, Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008);Hwang, H. et al. Sci Rep 6, 19900, doi:10.1038/srep19900 (2016); Schultheis et al,  . J Neurophysiol 106, 817-827, doi:10.1152/jn.00578.2010 (2011); Koopman, M., Janssen, L. & Nollen, E. A. BMC Biol 19, 170, doi:10.1186/s12915-021-01085-2 (2021);). It has previously been established that the shortening observed after optogenetic activation of the unc-17 promoter, while active in various interneurons, depends on the activity of cholinergic motor neurons (Liewald et al., Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008)). This was demonstrated by examining transgenic worms expressing ChR2-YFP from another cholinergic, motoneuronspecific but weaker promoter, Punc-4. They observed contraction and coiling upon illumination, albeit to a milder degree.

In terms of GABAergic neurons, only 3 do not directly synapse to body wall muscles (AVL, PDV, and RIS) and are primarily involved in defecation. Of the 23 GABAergic motor neurons, 19 are Dtype motoneurons, while the remaining 4 innervate head muscles (Pereira et al, eLife 2015, https://doi.org/10.7554/eLife.12432). It is therefore expected that while there may be some contribution from these latter neurons to the elongation after optogenetic activation in animals containing punc-47::ChR2, the main contribution should be from the D-type neurons. Additionally, while there may be some influence on D-type neuron development due to daf-18 rescue in neurons like RME, DVB or AVL, the most direct explanation for the rescue is that daf-18 acts autonomously in D-type cells.  Additionally, we have pharmacological and behavioral assays that support the findings of optogenetics and enable us to reach final conclusions.

(3) DD neurons are born during embryogenesis and newborn L1s have neurites even though less than at a later stage. If possible, it would be interesting to take a look at them to see if βHB has an effect or not. It will corroborate the hypothesis that βHB action is prevented by the impermeable eggshell on a system that can respond at a later stage. Moreover, using a specific DD, DA, and DB promoter, it would be possible to check if there is a difference in the morphological defects between embryonic and post-embryonic neurons.

This is a very interesting point raised by the reviewer. We conducted experiments to analyze the morphology of GABAergic neurons in animals exposed to βHB only during the ex-utero embryonic development (in their laid egg state). We observed that this incubation was not sufficient to rescue the defects in GABAergic neurons (Supplementary Figure 7, revised version). As reported by other authors and discussed in our paper, the chitinous eggshell might act as an impermeable barrier to most drugs. However, we cannot rule out that incubation during this period is necessary but not sufficient to mitigate the defects. We have included these experiments in Supplementary Figure 7 and in the text (Page 13, lines 272-276)

Additionally, we analyzed confocal images where, based on their position, we could identify and assess errors in DD (embryonic) and VD (Post-embryonic) neurons (Supplementary Figure 3, revised version). These experiments show that the effects are observed in both types of neurons, and we did not observe any differential alterations in neuronal morphology between the two types of neurons.

Minor points

(1)   Expression of daf-18/PTEN in muscle or hypodermis, could it ensure a proper development? It could give insights into the action mechanism of βHB.

The reviewer's observation is indeed very intriguing. Previous studies from the Grishok lab (Kennedy et al, 2013) have demonstrated that the expression of daf-18 or daf-16 in extraneuronal tissues, specifically in the hypodermis, can rescue migratory defects in the serotoninergic neuron HSN in daf-18 or daf-16 null mutants of C. elegans. Clearly, this could also be an option for rescuing the morphological and functional defects of GABAergic motoneurons.

However, the fact that the expression of daf-18 in GABAergic neurons rescues these defects strongly suggests an autonomous effect. In this regard, autonomous effects of DAF-18 or DAF-16 on neurodevelopmental defects have also been reported in interneurons in C. elegans (Christensen et al, 2011). This is included in the discussion (Page 15, lines 330-335)

(2) Re-organise the introduction. The paragraph on ketogenic diets (lines 35-38) is not logically linked.

Following reviewer´s suggestion we have reorganized the introduction and changed the order of explanation regarding the significance of ketogenic diets, linking it with their proven effectiveness in alleviating symptoms of diseases with E/I imbalance (Lines 23-60, revised version)

(3) Incorporate titles in the result section to guide the reader.

Done. Thank you

(4) Systematically add PTEN or FOXO when daf-18 or daf-16 are mentioned (for example lines 69, 84, 85).

Done. Thank you  

(5) Strain lists: lines 646 to 653: some information is missing on the different transgenes used in this study (integrated (Is) or extrachromosomal (Ex) with their numbers).

Thank you for bringing this to our attention. We have now included all the information regarding the different transgenes used in this study, including whether they are integrated (Is) or extrachromosomal (Ex) and their respective numbers. This information can be found in the revised version of the manuscript (Materials and Methods, C. elegans culture and maintenance section highlighted in yellow).

Reviewer #3 (Recommendations For The Authors):

In Figure 1, some experiments were done with the unc-25 control while others, such as the optogenetic experiments, were done without those controls.

Thank you for pointing this out. In the optogenetic experiments, we waited for the worm to move forward for 5 seconds at a sustained speed before exposing it to blue light to standardize the experiment, as the response can vary if the animal is in reverse, going forward, or stationary. Due to the severity of the uncoordinated movement in unc-25 mutants, achieving this forward movement before exposure is very difficult. Additionally, this lack of coordination prevents these animals from performing the escape response tests, as they barely move. Therefore, we limited the use of this severe GABAergic-deficient control to pharmacological or post-prodding shortening experiments.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Additional experiments to characterize what this novel cell type becomes in older animals would be ideal to strengthen the manuscript, but the authors should at least address this in the Discussion.

The manuscript could be significantly improved if the authors included, for example, a timeline and/or cartoon contextualizing these cells relative to the formation of other CN neurons and their locations, perhaps as a summary figure at the end. Furthermore, the logic of each figure could be enhanced if the authors graphically show - again, perhaps with a schematic/cartoon - the question being tested for each figure. Furthermore, making the figure titles less descriptive and more explanatory would also help a reader follow the logic of the experiments.

These are indeed valid and important questions for our research, and understanding the distribution, fate, and connectivity of this new cell type in the cerebellar nuclei postnatally is a focus of ongoing investigation in our lab. To address these questions, we are currently utilizing SNCA-GFP mice, a project led by a PhD student in my lab. While this work will be the subject of a full-length research paper, we do add a sentence to the paper concerning a recent report about the presence of SNCA neurons in the adult CN.  We have included a reference to the postnatal expression of SNCA (“In adult mice, postnatal expression of SNCA has been reported in medial CN neurons. PMID: 32639229”.) on page 8 of our manuscript (highlighted in yellow). In addition, we have included a cartoon as a summary figure (Fig. 9) illustrating the origin of cerebellar nuclei from the caudal and rostral ends in both Atoh1+/+ and Atoh1-/- mice. Thank you once again, we have revised and improved the Fig. titles accordingly.

Reviewer #2 (Recommendations For The Authors):

Figure 3:

(1) If most SNCA+ cells are OTX2+ based on the IHCs, why are there so many SNCA+ Otx2- cells in the sort?

In each group, 350,000 cells were sorted. Due to the relatively small population size of this subset of cerebellar nuclei neurons, the sorting procedure could not perfectly mirror our immunohistochemistry results. In each group, 350,000 cells were sorted. Due to the relatively small population size of this subset of cerebellar nuclei neurons, the sorting procedure could not perfectly mirror our immunohistochemistry results. However, it is noteworthy that a portion of sorted cells expressed SNCA or Otx2 while a smaller population co-expressed both Otx2 and SNCA in the cerebellar primordium.

(2) Panel 3F: FACS graphs - the resolution of the figures is too poor on the PDF to read any of the text of these graphs. What are the axes?

We thank the reviewer for this comment. In the revision a high resolution of the FACS graph has replaced the lower quality graph in panel 3F. This clearly identifies the axes and text for this panel.

Figure 4:

(1) Arrowheads are making a subset of + cerebellar cells -Why? Not defined in the legend.

The population of cells indicated by the arrowheads are now defined in the legend. We have added the statement “Examples of Otx2 expressing cells are indicated by arrowheads in panels B, D, E, and F.”

(2) The orientation of panels E and F is unclear - please provide low mag panel insets.

An orientation marker (ie, (r-c and d-v; rostral caudal and dorsal ventral, respectively)) has been added to panel A, which applies to all panels, including panels E and F. Furthermore, the isthmus is noted with an “i” to provide further orientation.

(3) G - and throughout the paper - whisker plots (not simple box plots) are required. Also, it is unclear from the methods how Otx2+ cells were counted - how many embryos/age? The description of 10 sections across 3 slides is incomplete. Are these cells distributed equally across the mediolateral axis of the anlage? Where are comparable M/L sections compared across ages? Is the increase in # across time because these cells are proliferative or are more migrating into the anlage?

The plot has been replaced with whisker plots. A more detailed description of the Method used has been on page 15; “To assess the number of OTX2-positive cells, we conducted immunohistochemistry (IHC) labeling on slides containing serial sections from embryonic days 12, 13, 14, and 15 (n=3 at each timepoint). Under the microscope, we systematically counted OTX2-positive cells within the cerebellar primordium. This analysis encompassed a minimum of 10 sections, spread across at least 3 slides, ensuring comprehensive coverage of OTX2 expression along the mediolateral axis of the cerebellar primordium. For each slide, the counts of OTX2-positive cells from all sections were cumulatively calculated to determine the total number of positive cells per slide. Subsequently, statistical analysis was employed to compare the results obtained different developmental time points.”

Figure 5:

The use of confocal microscopy creates clear data re Otx2-GFP expression, but I cannot understand the origin of the panels. How do they relate to E/F and H/I? Different sections?

In Figure 5, panels A-D display Otx2 expressing cells in the cerebellar primordium of Otx2-GFP transgenic mice, whereas panels E-J depict RNAscope fluorescence in situ hybridization (FISH) for the Otx2 probe in wild type mice. These represent complementary approaches to map Otx2+ cells in the developing cerebellum. This is made clear in a revised legend in Fig 5.

Figure 6:

The justification for the in-culture experiments, particularly the long (4 and 21DIV) times is unclear and needs to be strengthened or the in vitro data should be removed.

Thank you for the respected reviewer’s comment. The E-H panels, show the co-expression of SNCA and p75NTR, highlight a significant role in the differentiation of specific neuronal populations during development. These findings validate our previous results (PMID: 31509576) and are consistent with the results of our current study. Therefore, we have chosen to keep these panels. However, in line with the suggestion from the reviewer, we have removed panels I-L from Fig. 6.

Figure 7:

SNCA expression in panels A and G is not specific nor is the Otx2 staining in panel B making the data in panels C and I uninterpretable and these panels need to be replaced. The Meis2 data however is much better and I agree this data shows that the dorsal RL-derived cells are deleted in Atoh1-/- while the SNCA+ cells remain. This is strong data supporting the dual origins of NTZ.

Thank you for the points, Panel A and G have been replaced with high-resolution images. In addition, panels A-C have been carefully cropped to enhance focus on the NTZ area, to improve the quality and visibility of panels.  To enhance clarity, we have included a summary fig. 9 for clarification.

Figure 8:

The diI experiments are a key addition to this paper and clearly show the direct movement of some cells from the mesencephalon into the developing cerebellum, but data presentation must be considerably strengthened.

(1) What is the inset in panel A? Low mag of embryo? Perhaps conversion of image to PDF degraded resolution - add a description in the legend. Arrowhead and arrow identities are reversed in the legend. The arrow points to the isthmus.

Thank you for the comment, for clarification we have included information in the Fig. legend (highlighted in yellow). In addition, the issues with the arrows have been addressed and corrected.

(2) Panels B and C are also shown in Supplementary Figure 2 with arrows indicating rostral and caudal movement - these arrows need to be added here. There is no need to replicate these same panels in the supplement.

Thanks, arrows have been added in panels B, C of Fig. 8.

(3) The text states that "almost all DiI cells migrated caudally into the cerebellum" and refers to Figure 8E and Suppementl 3 but there is no evidence/support shown for this, just a few + cells in 8E and some very difficult-to-see positive cells in sections in Supplement E-F. Given the importance of this data, I am surprised that the authors chose bright field/phase microscopy to show this. This section's data is not convincing data at all. I find it very difficult to see specific staining. These panels must be improved. This is key data for paper conclusions.

These are valid points, and we acknowledge that this experiment alone may not provide conclusive evidence regarding the subset of CN originating from mesencephalon. At this stage of the study, we do not claim definitively that the SNCA/OTX2/MEIS2 positive cells originate from the mesencephalon. As stated in our manuscript, "In conclusion, our study indicates that the SNCA+/ OTX2+/ MEIS2+/ p75NTR+/ LMX1A- rostroventral subset of CN neurons do not originate from the well-known distinct germinative zones of the cerebellar primordium. Instead, our findings suggest the existence of a previously unidentified extrinsic germinal zone, potentially the mesencephalon."  We have also discussed embryonic culture approaches in the manuscript, which could involve the use of other agents such as plasmid/viral vectors, hinting at the possibility of origin from the mesencephalon. While tracing the origin from the mesencephalon in vivo and in vitro is promising and on our to-do list, the data will not be available for this manuscript. To prevent confusion, we have eliminated redundant panels of Fig. 8 with Supplementary Fig. 2 and 3. However, if the reviewer deems it necessary to remove these panels, we are prepared to do so.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

The revised manuscript addressed my minor concerns adequately, and the manuscript is now further improved. I have no remaining criticisms.

Reviewer #2 (Recommendations For The Authors):

Abstract:

line 45 The abbreviation "SytI" should perhaps be introduced above.

done

Results:

line 139 "RRP kinetics" should perhaps read "RRP depletion kinetics" or "secretion kinetics".

We replaced “RRP kinetics” with “RRP secretion kinetics”

line 325ff and Figure 8

As far as I understand, SytI 875 R233Q ki cells shown in violet express wt CplxII. Perhaps this should be explicitly stated?

To accommodate this suggestion: We now state on page 13 line 302: “Overexpression of the CpxII DN mutant in SytI R233Q ki cells, which is expected to outcompete the function of endogenous CpxII in these cells (Dhara et al., 2014), further slowed down the rate of synchronized release and restored the EB size to the wt level (Figure 7C, D)”

line 332ff and Figure 8

What is plotted in Figure 8B bottom and in Figure 8D is not a "rate" but rather a "unitary rate", more commonly referred to as a "rate constant".

The y-axis label of Figures 8B and 8D should therefore better be changed to "rate constant". See also line 528 of the Discussion.

Figure (y-axis label) and text were changed accordingly

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Glaser et al present ExA-SPIM, a light-sheet microscope platform with large volumetric coverage (Field of view 85mm^2, working distance 35mm), designed to image expanded mouse brains in their entirety. The authors also present an expansion method optimized for whole mouse brains and an acquisition software suite. The microscope is employed in imaging an expanded mouse brain, the macaque motor cortex, and human brain slices of white matter. 

This is impressive work and represents a leap over existing light-sheet microscopes. As an example, it offers a fivefold higher resolution than mesoSPIM (https://mesospim.org/), a popular platform for imaging large cleared samples. Thus while this work is rooted in optical engineering, it manifests a huge step forward and has the potential to become an important tool in the neurosciences. 

Strengths: 

- ExA-SPIM features an exceptional combination of field of view, working distance, resolution, and throughput. 

- An expanded mouse brain can be acquired with only 15 tiles, lowering the burden on computational stitching. That the brain does not need to be mechanically sectioned is also seen as an important capability. 

- The image data is compelling, and tracing of neurons has been performed. This demonstrates the potential of the microscope platform. 

Weaknesses: 

- There is a general question about the scaling laws of lenses, and expansion microscopy, which in my opinion remained unanswered: In the context of whole brain imaging, a larger expansion factor requires a microscope system with larger volumetric coverage, which in turn will have lower resolution (Figure 1B). So what is optimal? Could one alternatively image a cleared (non-expanded) brain with a high-resolution ASLM system (Chakraborty, Tonmoy, Nature Methods 2019, potentially upgraded with custom objectives) and get a similar effective resolution as the authors get with expansion? This is not meant to diminish the achievement, but it was unclear if the gains in resolution from the expansion factor are traded off by the scaling laws of current optical systems. 

Paraphrasing the reviewer: Expanding the tissue requires imaging larger volumes and allows lower optical resolution. What has been gained?

The answer to the reviewer’s question is nuanced and contains four parts. 

First, optical engineering requirements are more forgiving for lenses with lower resolution. Lower resolution lenses can have much larger fields of view (in real terms: the number of resolvable elements, proportional to ‘etendue’) and much longer working distances. In other words, it is currently more feasible to engineer lower resolution lenses with larger volumetric coverage, even when accounting for the expansion factor. 

Second, these lenses are also much better corrected compared to higher resolution (NA) lenses. They have a flat field of view, negligible pincushion distortions, and constant resolution across the field of view. We are not aware of comparable performance for high NA objectives, even when correcting for expansion.

Third, although clearing and expansion render tissues ‘transparent’, there still exist refractive index inhomogeneities which deteriorate image quality, especially at larger imaging depths. These effects are more severe for higher optical resolutions (NA), because the rays entering the objective at higher angles have longer paths in the tissue and will see more aberrations. For lower NA systems, such as ExaSPIM, the differences in paths between the extreme and axial rays are relatively small and image formation is less sensitive to aberrations. 

Fourth, aberrations are proportional to the index of refraction inhomogeneities (dn/dx). Since the index of refraction is roughly proportional to density, scattering and aberration of light decreases as M^3, where M is the expansion factor. In contrast, the imaging path length through the tissue only increases as M. This produces a huge win for imaging larger samples with lower resolutions. 

To our knowledge there are no convincing demonstrations in the literature of diffraction-limited ASLM imaging at a depth of 1 cm in cleared mouse brain tissue, which would be equivalent to the ExA-SPIM imaging results presented in this manuscript.  

In the discussion of the revised manuscript we discuss these factors in more depth. 

- It was unclear if 300 nm lateral and 800 nm axial resolution is enough for many questions in neuroscience. Segmenting spines, distinguishing pre- and postsynaptic densities, or tracing densely labeled neurons might be challenging. A discussion about the necessary resolution levels in neuroscience would be appreciated. 

We have previously shown good results in tracing the thinnest (100 nm thick) axons over cm scales with 1.5 um axial resolution. It is the contrast (SNR) that matters, and the ExaSPIM contrast exceeds the block-face 2-photon contrast, not to mention imaging speed (> 10x).  

Indeed, for some questions, like distinguishing fluorescence in pre- and postsynaptic structures, higher resolutions will be required (0.2 um isotropic; Rah et al Frontiers Neurosci, 2013). This could be achieved with higher expansion factors.

This is not within the intended scope of the current manuscript. As mentioned in the discussion section, we are working towards ExA-SPIM-based concepts to achieve better resolution through the design and fabrication of a customized imaging lens that maintains a high volumetric coverage with increased numerical aperture.  

- Would it be possible to characterize the aberrations that might be still present after whole brain expansion? One approach could be to image small fluorescent nanospheres behind the expanded brain and recover the pupil function via phase retrieval. But even full width half maximum (FWHM) measurements of the nanospheres' images would give some idea of the magnitude of the aberrations. 

We now included a supplementary figure highlighting images of small axon segments within distal regions of the brain.  

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, Glaser et al. describe a new selective plane illumination microscope designed to image a large field of view that is optimized for expanded and cleared tissue samples. For the most part, the microscope design follows a standard formula that is common among many systems (e.g. Keller PJ et al Science 2008, Pitrone PG et al. Nature Methods 2013, Dean KM et al. Biophys J 2015, and Voigt FF et al. Nature Methods 2019). The primary conceptual and technical novelty is to use a detection objective from the metrology industry that has a large field of view and a large area camera. The authors characterize the system resolution, field curvature, and chromatic focal shift by measuring fluorescent beads in a hydrogel and then show example images of expanded samples from mouse, macaque, and human brain tissue. 

Strengths: 

I commend the authors for making all of the documentation, models, and acquisition software openly accessible and believe that this will help assist others who would like to replicate the instrument. I anticipate that the protocols for imaging large expanded tissues (such as an entire mouse brain) will also be useful to the community. 

Weaknesses: 

The characterization of the instrument needs to be improved to validate the claims. If the manuscript claims that the instrument allows for robust automated neuronal tracing, then this should be included in the data. 

The reviewer raises a valid concern. Our assertion that the resolution and contrast is sufficient for robust automated neuronal tracing is overstated based on the data in the paper. We are hard at work on automated tracing of datasets from the ExA-SPIM microscope. We have demonstrated full reconstruction of axonal arbors encompassing >20 cm of axonal length.  But including these methods and results is out of the scope of the current manuscript. 

The claims of robust automated neuronal tracing have been appropriately modified.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Smaller questions to the authors: 

- Would a multi-directional illumination and detection architecture help? Was there a particular reason the authors did not go that route?

Despite the clarity of the expanded tissue, and the lower numerical aperture of the ExA-SPIM microscope, image quality still degrades slightly towards the distal regions of the brain relative to both the excitation and detection objective. Therefore, multi-directional illumination and detection would be advantageous. Since the initial submission of the manuscript, we have undertaken re-designing the optics and mechanics of the system. This includes provisions for multi-directional illumination and detection. However, this new design is beyond the scope of this manuscript. We now mention this in L254-255 of the Discussion section.

- Why did the authors not use the same objective for illumination and detection, which would allow isotropic resolution in ASLM? 

The current implementation of ASLM requires an infinity corrected objective (i.e. conjugating the axial sweeping mechanism to the back focal plane). This is not possible due to the finite conjugate design of the ExA-SPIM detection lens.

More fundamentally, pushing the excitation NA higher would result in a shorter light sheet Rayleigh length, which would require a smaller detection slit (shorter exposure time, lower signal to noise ratio). For our purposes an excitation NA of 0.1 is an excellent compromise between axial resolution, signal to noise ratio, and imaging speed. 

For other potentially brighter biological structures, it may be possible to design a custom infinity corrected objective that enables ASLM with NA > 0.1.

- Have the authors made any attempt to characterize distortions of the brain tissue that can occur due to expansion? 

We have not systematically characterized the distortions of the brain tissue pre and post expansion. Imaged mouse brain volumes are registered to the Allen CCF regardless of whether or not the tissue was expanded. It is beyond the scope of this manuscript to include these results and processing methods, but we have confirmed that the ExA-SPIM mouse brain volumes contain only modest deformation that is easily accounted for during registration to the Allen CCF. 

- The authors state that a custom lens with NA 0.5-0.6 lens can be designed, featuring similar specifications. Is there a practical design? Wouldn't such a lens be more prone to Field curvature? 

This custom lens has already been designed and is currently being fabricated. The lens maintains a similar space bandwidth product as the current lens (increased numerical aperture but over a proportionally smaller field of view). Over the designed field of view, field curvature is <1 µm. However, including additional discussion or results of this customized lens is beyond the scope of this manuscript.

Reviewer #2 (Recommendations For The Authors): 

• System characterization: 

- Please state what wavelength was used for the resolution measurements in Figure 2.

An excitation wavelength of 561 nm was used. This has been added to the manuscript text.

- The manuscript highlights that a key advance for the microscope is the ability to image over a very large 13 mm diameter field of view. Can the authors clarify why they chose to characterize resolution over an 8diameter mm field rather than the full area? 

The 13 mm diameter field of view refers to the diagonal of the 10.6 x 8.0 mm field of view. The results presented in Figure 1c are with respect to the horizontal x direction and vertical y direction. A note indicating that the 13 mm is with respect to the diagonal of the rectangular imaging field has been added to the manuscript text. The results were presented in this way to present the axial and lateral resolution as a function of y (the axial sweeping direction).

- The resolution estimates seem lower than I would expect for a 0.30 NA lens (which should be closer to ~850 nm for 515 nm emission). Could the authors clarify the discrepancy? Is this predicted by the Zemax model and due to using the lens in immersion media, related to sampling size on the camera, or something else? It would be helpful if the authors could overlay the expected diffraction-limited performance together with the plots in Figure 2C. 

As mentioned previously, the resolution measurements were performed with 561 nm excitation and an emission bandpass of ~573 – 616 nm (595 nm average). Based on this we would expect the full width half maximum resolution to be ~975 nm. The resolution is in fact limited by sampling on the camera. The 3.76 µm pixel size, combined with the 5.0X magnification results in a sampling of 752 nm. Based on the Nyquist the resolution is limited to ~1.5 µm. We have added clarifying statements to the text.

- I'm confused about the characterization of light sheet thickness and how it relates to the measured detection field curvature. The authors state that they "deliver a light sheet with NA = 0.10 which has a width of 12.5 mm (FWHM)." If we estimate that light fills the 0.10 NA, it should have a beam waist (2wo) of ~3 microns (assuming Gaussian beam approximations). Although field curvature is described as "minimal" in the text, it is still ~10-15 microns at the edge of the field for the emission bands for GFP and RFP proteins. Given that this is 5X larger than the light sheet thickness, how do the authors deal with this? 

The generated light sheet is flat, with a thickness of ~ 3 µm. This flat light sheet will be captured in focus over the depth of focus of the detection objective. The stated field curvature is within 2.5X the depth of focus of the detection lens, which is equivalent to the “Plan” specification of standard microscope objectives.

- In Figure 2E, it would be helpful if the authors could list the exposure times as well as the total voxels/second for the two-camera comparison. It's also worth noting that the Sony chip used in the VP151MX camera was released last year whereas the Orca Flash V3 chosen for comparison is over a decade old now. I'm confused as to why the authors chose this camera for comparison when they appear to have a more recent Orca BT-Fusion that they show in a picture in the supplement (indicated as Figure S2 in the text, but I believe this is a typo and should be Figure S3). 

This is a useful addition, and we have added exposure times to the plot. We have also added a note that the Orca Flash V3 is an older generation sCMOS camera and that newer variants exist. Including the Orca BT-Fusion. The BT-Fusion has a read noise of 1.0 e- rms versus 1.6 e- rms, and a peak quantum efficiency of ~95% vs. 85%. Based on the discussion in Supplementary Note S1, we do not expect that these differences in specifications would dramatically change the data presented in the plot. In addition, the typo in Figure S2 has been corrected to Figure S3.

- In Table S1, the authors note that they only compare their work to prior modalities that are capable of providing <= 1 micron resolution. I'm a bit confused by this choice given that Figure 2 seems to show the resolution of ExA-SPIM as ~1.5 microns at 4 mm off center (1/2 their stated radial field of view). It also excludes a comparison with the mesoSPIM project which at least to me seems to be the most relevant prior to this manuscript. This system is designed for imaging large cleared tissues like the ones shown here. While the original publication in 2019 had a substantially lower lateral resolution, a newer variant, Nikita et al bioRxiv (which is cited in general terms in this manuscript, but not explicitly discussed) also provides 1.5-micron lateral resolution over a comparable field of view. 

We have updated the table to include the benchtop mesoSPIM from Nikita et al., Nature Communications, 2024. Based on this published version of the manuscript, the lateral resolution is 1.5 µm and axial resolution is 3.3 µm. Assuming the Iris 15 camera sensor, with the stated 2.5 fps, the volumetric rate (megavoxels/sec) is 37.41.

- The authors state that, "We systematically evaluated dehydration agents, including methanol, ethanol, and tetrahydrofuran (THF), followed by delipidation with commonly used protocols on 1 mm thick brain slices. Slices were expanded and examined for clarity under a macroscope." It would be useful to include some data from this evaluation in the manuscript to make it clear how the authors arrived at their final protocol. 

Additional details on the expansion protocol may be included in another manuscript.

General comments: 

• There is a tendency in the manuscript to use negative qualitative terms when describing prior work and positive qualitative terms when describing the work here. Examples include: 

- "Throughput is limited in part by cumbersome and error-prone microscopy methods". While I agree that performing single neuron reconstructions at a large scale is a difficult challenge, the terms cumbersome and error-prone are qualitative and lacking objective metrics.

We have revised this statement to be more precise, stating that throughput is limited in part by the speed and image quality of existing microscopy methods.

- The resolution of the system is described in several places as "near-isotropic" whereas prior methods were described as "highly anisotropic". I agree that the ~1:3 lateral to axial ratio here is more isotropic than the 1:6 ratio of the other cited publications. However, I'm not sure I'd consider 3-fold worse axial resolution than lateral to be considered "near" isotropic.

We agree that the term near-isotropic is ambiguous. We have modified the text accordingly, removing the term near-isotropic and where appropriate stating that the resolution is more isotropic than that of other cited publications.

- exposures (which in the caption is described as "modest"). I'd suggest removing these qualitative terms and just stating the values.

We agree and have changed the text accordingly.

• The results section for Figure 5 is titled "Tracing axons in human neocortex and white matter". Although this section states "larger axons (>1 um) are well separated... allowing for robust automated and manual tracing" there is no data for any tracing in the manuscript. Although I agree that the images are visually impressive, I'm not sure that this claim is backed by data.

We have now removed the text in this section referring to automated and manual tracing.

Author response:

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

eLife assessment

The paper investigates a potential cause of a type of severe epilepsy that develops in early life because of a defect in a gene called KCNQ2. The significance is fundamental because it substantially advances our understanding of a major research question. The strength of the evidence is convincing because appropriate methods are used that are in line with the state-of-the art, although there are some revisions/corrections that would strengthen the evidence further.

Thank you for the expert, thorough, and helpful review.  We believe that addressing the reviewers’ points has improved our paper greatly.   

Public Reviews:

Reviewer #1 (Public Review):

Abreo et al. performed a detailed multidisciplinary analysis of a pathogenic variant of the KCNQ2 ion channel subunit identified in a child with neonatal-onset epilepsy and neurodevelopmental disorders. These analyses revealed multiple molecular and cellular mechanisms associated with this variant and provided important insights into what distinguishes distinct pathogenic variants of KCNQ2 associated with self-limited familial neonatal epilepsy versus those leading to developmental and epileptic encephalopathy, and how they may mechanistically differ, to result in different extents of developmental impairment.

The authors first provide a detailed clinical description of the patient heterozygous for a novel pathogenic variant encoding KCNQ2 G256W. They then model the structure of the G256W variant based on recent cryo-EM structures of KCNQ2 and other ion channel subunits and find that while the affected position is quite distinct from the channel pore, it participates in a novel, evolutionarily conserved set of amino acids that form a network of hydrogen bonds that stabilize the structure of the pore domain.

They then undertake a series of rigorous and quantitative laboratory experiments in which the KCNQ2 G256W variant is coexpressed exogenously with WT KCNQ2 and KCNQ3 subunits in heterologous cells, and endogenously in novel gene-edited mice generated for this study. This includes detailed electrophysiological analyses in the transfected heterologous cells revealing the dominant-negative phenotype of KCNQ2 G256W. They found altered firing properties in hippocampal CA1 neurons in brain slices from the heterozygous KCNQ2 G256W mice.

They next showed that the expression and localization of KCNQ channels are altered in brain neurons from heterozygous KCNQ2 G256W mice, suggesting that this variant impacts KCNQ2 trafficking and stability.

Together, these laboratory studies reveal that the molecular and cellular mechanisms shaping KCNQ channel expression, localization, and function are impacted at multiple levels by the variant encoding KCNQ2 G256W, likely contributing to the clinical features of the child heterozygous for this variant relative to patients harboring distinct KCNQ2 pathogenic variants.

Thank you for the thorough summary and estimation of the initial submission, we are very glad that our approach, analytical methods, and conclusions were convincing.   

Reviewer #2 (Public Review):

Summary:

The paper entitled "Plural molecular and cellular mechanisms of pore domain KCNQ2 encephalopathy" by Abreo et al. is a complex and integrated paper that is well-written with a focus on a single gene variant that causes a severe developmental

encephalopathy. The paper collates clinical outcomes from 4 individuals and investigates a variant causing KCNQ2-DEE using a wide range of experimental techniques including structural biology, in vitro electrophysiology, generation of genetically modified animal models, immunofluorescence, and brain slice recordings. The overall results provide a plausible explanation of the pathophysiology of the G265W variant and provide important findings to the KCNQ2-DEE field as well as beginning to separate the understanding between seizures and encephalopathies.

Strengths:

(1) The authors describe in detail how the structural biology of the channel with a mutation changes the movement of the protein and adds insights into how one variant can change the function of the M-current. The proposed model linking this change to pathogenic consequences should help pave the way for additional studies to further support this type of approach.

(2) The multiple co-expression ratio experiments drill down to the complex nature of the assembly of channels in over-expression systems and help to move toward an understanding of heterozygosity. It might have been interesting if TEA was tested as a blocker to better understand the assembly of the transfected subunits or possibly use vectors to force desired configurations.

(3) The immunofluorescent approach to understanding re-distribution is another component of understanding the function of this critical current. The demonstration that Q2 and Q3 are diminished at the AIS is an important finding and a strength to the totality of the data presented in the paper.

(4) Brain slice work is an important component of studying genetically modified animals as it brings in the systems approach, and helps to explain seizure generation and EEG recordings. The finding that G265W/+ neurons were more sensitive to current injections is a critical component of the paper.

(5) The strength of this body of work is how the authors integrated different scientific approaches to knitting together a compelling set of experiments to better explain how a single variant, and likely extrapolation to other variants, can cause a severe neonatal developmental encephalopathy with a poor clinical outcome.

Thank you for the thorough and encouraging reading of our work and its strengths, we are very glad that, excepting the issues mentioned which we have addressed, our approach and conclusions were convincing.

Weaknesses:

(1) Minor comment: Under the clinical history it is unclear whether the mother was on Leviracetam for suspected in-utero seizures or if Leviracetam was given to individual 1.

The latter seems more likely, and if so this should be reworded.

We revised the results text to clarify that the drug was begun postnatally, after epilepsy was diagnosed in the child.   

(2) As described in the clinical history of patient 1, treatment with ezogabine was encouraging with rapid onset by a parental global impression with difficulty in weaning off the drug. When studying the genetically modified mice, it would have been beneficial to the paper to talk about any ezogabine effects on the genetically modified mice.

We agree this is of great interest, but sampling and metrics are challenging due to the very low frequency of seizures and delayed mortality in the heterozygous G256 mice.  Accordingly, we have not performed ezogabine treatment experiments in the mice described in this study, which model a human variant associated with a brief neonatal window of frequent seizures.  We hope to return this issue using other transgenic mice with higher seizure frequency, but such results are outside the current scope.

(3) It is a bit surprising that CA1 pyramidal neurons from the heterozygous G256W mice have no difference in resting membrane potential. The discussion section might explore this in a bit more detail.

Thank you for raising this issue. This combination of outcomes has been seen previously and is interpreted as an outcome of low somatodendritic surface expression of the channels.  Relatively higher expression within the AIS membrane, with its the relatively small surface area and electrical isolation from the soma, allow the KCNQ2/3 channels to influence AIS excitability with little or (in this instance) undetectable influence on the RMP (see e.g., Otto et al. 2006, PMID: 16481438; Singh et al. 2008, PMID 16481438  for KCNQ2 mutant mice.  See Hu and Bean, 2018, figure 2; PMID: 29526554 for explicit testing via focal AIS vs. somatic blocker perfusion).  Additionally, in previous work, we did not find any changes to the RMP of CA1 pyramidal neurons in either Kcnq2 knockout mice (PMID: 24719109) or mice expressing a Kcnq2 GOF variant (PMID: 37607817).  We modified the discussion including adding references to prior studies combining experimental and multicompartmental computational models.

(4) It was mentioned in the paper about a direct comparison between SLFNE and G256W.

However, in the slice recordings, there was no comparison. Having these data comparing

SLFNE to G256W would have been a more fulsome story and would have added to the concept around susceptibility to action potential firing.

Thank you for this point. We agree that such side-by-side recordings would be interesting.  However, slice recordings were not performed on the SLFNE mice. The study design was based on the fact that extensive prior studies of both haploinsufficient and missense human SLFNE variant mice have been published (Otto et al. 2006 J Neuroscience, PMID: 16481438; Singh et al. 2008, PMID 16481438; Kim et al 2020 PMID: 31283873) and show good agreement, but DEE missense variants have not been previously studied. We revised the discussion, to place the current DEE model results in the context of the prior SNFLE model slice work. We contrast the similarity of the CA1 cellular hyperexcitability phenotype ex vivo (at least in CA1 pyramidal cells) across models to the differences in electrographic and behavioral seizures (i.e., network level physiology).  

Reviewer #3 (Public Review):

Summary:

This manuscript describes the symptoms of patients harboring KCNQ2 mutation G256W, functional changes of the mutant channel in exogenous expression, and phenotypes of G256W/+ mice. The patients presented seizures, the mutation reduced currents of the channel, and the G256W/+ mice showed seizures, increased firing frequency in neurons, reduced KCNQ2 expression, and altered subcellular distribution.

Strengths:

This is a large amount of work and all results corroborated the pathogenicity of the mutation in KCNQ2, providing an interesting example of KCNQ2-associated neurological disorder's impact on functions at all levels including molecular, cellular, tissue, animal model, and patients.

Weaknesses:

The manuscript described observations of changes in association with the mutation at molecular cellular functions and animal phenotype, but the results in some aspects are not as strong as in others. Nevertheless, the manuscript made overarching conclusions even when the evidence was not sufficiently strong.

Thank you for your review.  In our revision (as listed in the recommendations to authors section) we have attempted to better justify the conclusions you mention there.

Recommendations for the authors: 

Reviewer #1 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data, or analyses.

Page 7: the authors' statement that G256 could be intolerant to substitution would be strengthened by a straightforward analysis of available genome- and exome-wide sequencing data to determine the level of genic intolerance at this position in the human population, as has been used previously to highlight critical residues including those impacted by pathogenic variants in many other proteins including ion channels (e.g., Genome Biology 17:9, 2016; Am J Hum Genet 99:1261, 2016; Biochim Biophys Acta Biomemb 1862:183058, 2020).

Thank you for this suggestion, we have revised the opening of this section to point out the low ratio of benign to pathogenic variants in the region surrounding G256 shown by prior work. We have added citations to the papers describing the MTR and gnomAD tools that highlight these data and calculations.   

The overall interpretation of the CHO cell results would be enhanced by the authors including in their discussion an explicit statement that they did not attempt to evaluate the overall and plasma membrane expression levels of the exogenously expressed WT and mutant KCNQ2 subunits, nor that of KCNQ3, in the transfected CHO cells. They could also highlight that this is an important future experiment to determine whether the dominant negative effects are due to impaired expression/trafficking or impaired function of plasma membrane channels, as this may be an important consideration for designing therapeutic strategies.

We agree.  We revised the discussion to explicitly mention this additional direction.  We agree this topic has therapeutic implications, especially given our in vivo protein localization results.  We added a mention that combinations of molecules enhancing surface localization with channel openers could be a therapeutic strategy, analogous to approved therapies for cystic fibrosis.  

The authors conclude that the impact of ezogabine treatment is reduced in the cells expressing G256+/W versus those expressing WT KCNQ2. However, the delta pA/pF graph in panel 3G expresses the effects of ezogabine as absolute increases in current density. Determining the relative increase (i.e., fold change) in current density in ezogabine-treated versus control conditions is a more valid way to analyze these data. This provides a better reflection of the impact of ezogabine as the control currents already have a much larger amplitude than the G256+/W currents. By eye the impact of ezogabine looks comparable or even larger for the G256+/W condition than for WT, fundamentally changing the interpretation of these results.

Thank you for this helpful comment.  The reviewer calls attention to the fact that although G256W/+ mean whole cell currents from are less than WT, before and after application of ezogabine, it appeared from Fig. 3G that ezogabine enhanced currents to a “proportionally equivalent extent” in G256W/+ and WT cells.  We revised panel 3G to try to make this more clear.  It now shows WT currents +/- ezogabine currents normalized to (WT, no ezogabine at +40 mV), along with G256W/+ cells +/- ezogabine currents, normalized to (G256W/+, no ezogabine at +40 mV).  This normalization shows that the mixed population of channels expressed by G256W/+ cells are equally augmented (with a trend toward greater augmentation), compared to controls.  This is a striking result given that channels lacking WT KCNQ2 subunits do not respond to ezogabine (i.e., the “homozygous heteromer” condition, Fig. 3F) do not respond to ezogabine.  Although the underlying data are unchanged, we agree with the reviewers’ conclusion about emphasizing the effect “per channel”.  This reframing is mechanistically and clinically important.  We have made changes to the results text and discussion to highlight related issues.   

Figure 7: it is not clear from the information presented whether the qPCR would only measure WT KCNQ2 mRNA levels or detect levels of both WT and E254fs transcripts. The authors assume nonsense-mediated decay, but they did [not] determine experimentally that this occurred. The sequencing in the supplemental figure shows the presence of E254fs transcripts but does not allow for insights into their abundance. It should be straightforward to develop primer sets that could then be used to selectively amplify WT and E254fs transcripts for quantitation. 

Thank you for this helpful suggestion.  The assay used in the initial submission measures total Kcnq2 mRNA. We developed and performed a new assay where the probe binding site is the WT sequence, centered on the mutations. New Figure 7-Figure supplement 1, panel A is a cartoon showing the differences between the assays.  Using the WT alleleselective RT-qPCR assay, both  G256W/+ and E254fs/+ samples showed a 50% loss of WT Kcnq2.   We now can conclude that NMD is absent for G256W and incomplete for E254fs mRNA. Neither mutant heterozygous line shows a compensatory increase in WT Kcnq2 expression.  These conclusions are much more specific than previously, and documenting incomplete NMD of KCNQ2 is novel and of potential clinical significance.  The KCNQ2 protein (western blot) and WT mRNA (qPCR) results now agree, both showing ~50% loss.   

For reporting transparency, the authors should provide the sequences of each of the primers used. Perhaps this is in the "key reagents" section, but this was missing from the manuscript. I note the authors use NMD in this section without defining it. and added a reference to a review where “incomplete NMD” is discussed.

We have added the assay catalogue numbers to the key reagents table.  We eliminated the use of the NMD abbreviation. We added citations to the “incomplete NMD” literature including an excellent recent review and a directly relevant primary paper.  These show how NMD efficiency may differ: between genes, transcripts, cells, tissues and, remarkably, between human individuals (see doi: 10.1093/hmg/ddz028, cited in the review—caffeine inhibits NMD!).  The revised discussion mentions this, and relevance to future studies of novel KCNQ2 variant pathogenicity and severity prediction.  

Recommendations for improving the writing and presentation.

I found the presentation of the IHC images deficient in terms of accessibility and transparency. While the movies provided are also useful, it is important the authors also provide conventional static merged images of each of their multiplex labeling images in the body of the paper. This allows a reader to see the labeling with the different antibodies in the context of each other (one of the major advantages of multiplex labeling), instead of trying to remember the pattern each label gave in prior sections of the movie.

[We queried the reviewer via the eLife editorial staff]: To clarify my suggestion to improve Figure 8, the authors should generate from their movies static images that are basically what they already did in Fig8S3 for the G256W Het panel of the Fig8 movie. This involves revising Fig8S3 to include WT panels, and adding two new supplemental figures that show WT/Het panels with the separate antibodies and then a merged image from Fig8S1 and Fig8S2, just like they did in Fig8S3 for the mutant part of the Fig8 movie.

Thank you for this comment. As suggested by the reviewer, for each IHC movie (Fig. 8, Fig. 8-figure supplement 1 and Fig. 8-figure supplement 2), we added a new supplementary  figure showing WT and mutant animal static images corresponding to the movies.  For main Figure 8 (CA1, G256W/+ comparison), the new static images enable evaluating the patterns of colocalization by providing selected portions of the images at the highest useful magnification.  These show  each individual antibody in greyscale (best for comparing) and 4 different green-red merged images to show overlap (yellow) vs non-overlap.  The merged images demonstrate colocalization of KCNQ2 and KCNQ3 at the distal portions of AnkG-labelled CA1 pyramidal cell AISs, in agreement with prior publications.  In G256W/+ but not E254fs/+ images, KCNQ2 and KCNQ3 show reduced relative labeling of AISs and increased relative labeling of somata in the pyramidal cell layer.   For CA3, the merged views show the redistributed relative labeling of KCNQ2 and KCNQ3 between stratum lucidum and stratum pyramidale.  

We also revised Fig. 8 supplement 3 (CA1) to include WT panels, On reexamination, all WT interneurons  in the small sample lacked somatic KCNQ2 and KCNQ3 labeling.  Some s. oriens and radiatum AISs of both WT and G256W/+ sections showed KCNQ2 and KCNQ3 labeling, as shown in the revised figure.  Counting statistics are included in the supporting data.  Importantly, our belief that the images shown are representative is supported by the blinded analysis of a much larger sample (Figure 9, unchanged in revision).  

Dragging the movie viewer “slider” allows the viewer to move  back and forth between color channels.  It works well in eLife if used in that way.   This is a way of seeing the “representativeness” of the merges shown in the CA1 conventional static images, which necessarily include a smaller x-y area and include only a few AISs.   We also added a KCNQ2/KCNQ3 merge to the movies. 

Western blot results in Figure 9 - Supplement 1: for transparency, the authors need to show the entire blot, as they did in Figure 4 - Supplement 2. This is required in many journals, and in the case of KCNQ2 it provides crucial information as to the different forms of KCNQ2 present on SDS gels in these samples that contain different KCNQ2 isoforms. Given the surprising decrease in levels of KCNQ2 monomer in the G256+/W mice, it is important to present and analyze the levels of the monomer, dimer, and higher oligomeric forms of KCNQ in these samples, to determine whether protein "missing" in the monomeric form is not present in the dimeric or higher oligomeric form. This is especially important as the G256W mutant could lead to misfolding and aggregation leading to a higher proportion of both WT and G256W subunits being present in a higher-order oligomeric form. I note that it is odd that the figure legend states "Images of entire filter used for western blot of lysates, probed for KCNQ2 and KCNQ3.", even though only selected portions are shown.

Thank you for this suggestion. We agree that the wording of the legend needed improvement.  

In revision, the western blots are renumbered as Figure 10, and Figure 10-Figure supplement 1. In the main figure, monomer bands and densitometry are shown, as previously.  In the new Figure 10-Figure supplement 1,  we show (1) the ECL image of the entire filter probed with rabbit anti-KCNQ2, (2) the same blot, stripped, and reprobed with guinea pig KCNQ3, (3) the lower portion, probed with mouse anti-tubulin. The revised Fig. 10-fig supplement 1 shows 3 genotypes x 3 individual (male) p21 mice, with all steps performed in parallel from homogenization to ECL detection.  As suggested, we performed new analysis of the immunoreactive bands corresponding to (apparent) monomer, dimer, and higher oligomeric forms of KCNQ2. Analysis of the sum of those bands showed loss of KCNQ2 protein in both mutant lines.  

The methods are sufficiently detailed with the exception that there is inconsistent inclusion of catalog numbers and RRIDs. Having these would improve transparency as to specific reagents used and would allow for enhanced reproducibility of the lab research performed here.

The revised submission includes the key resources table, which we understood was not requested from eLife at initial submission. 

Minor corrections to the text and figures.

Typos/mistakes as to antibodies used in the IHC methods section "anti-AnkG36 N106/36 " should be "anti-AnkG N106/36", and "mouse anti-PanNav IgG1 supernatant" should be mouse anti-PanNav IgG1 purified antibody". 

Thank you, corrections made.

It would facilitate a reader's interpretation of the IHC results if the authors explicitly stated in the IHC results section that the KCNQ2 antibody used is against the N-terminus and therefore should recognize both mutant isoforms as the mutations are downstream of this.

We added this point to the results section in relation to Figure 4-figure supplement 2 (western), and in IHC methods.

PV is not defined when used in the discussion, nor is why knowing that somatic KCNQ2 immunolabeling is present in both PV and non- PV interneurons of WT mice of value to the reader.

We revised these sentences for clarity.

The IHC methods state that "mice were transcardially perfused with....ice cold 2% paraformaldehyde in PBS, freshly prepared from a 20% stock (Electron Microscopy Sciences).". The authors presumably mean "formaldehyde" as paraformaldehyde is the inert polymeric storage form of active depolymerized monomeric formaldehyde that is a fixative.

The reviewer is correct regarding the chemistry; the manufacturer’s product name is “Paraformaldehyde 20% aqueous solution”.  We revised accordingly.

Reviewer #3 (Recommendations For The Authors):

Some comments regarding the presentation are as follows.

(1) The section "G256W lies atop a dome-shaped hydrogen bond network linking helix S5 to the turret and selectivity filter" is entirely based on structural observations without functional validation. This may be more appropriate in Discussion. The emphasis on the "turret arch" bonding should be tuned down due to the lack of functional support.

We understand and agree with this concern about the distinction between structural analysis and implied function.  However, we believe that the structural model reinterpretation and phylogenetic sequence analysis in our submission are results.  Structures as complex as those of KCNQ channels necessarily cannot be fully shown or analyzed in an initial publication. To our knowledge, the word “turret” has not appeared in a KCNQ channel cryoEM paper to date.  Bringing clinical motivation to prioritize study of an overlooked spot on the channel is creditworthy. The comprehensive heterologous patch clamp results in our study (including absence of effects on voltage-dependence, evidence of partial functional activity of channels containing one mutant subunit per channel shown for KCNQ2 homomers, KCNQ2/3 heteromers, and via acute ezogabine rescue experiments in the biologically most relevant heteromers) are functional evidence consistent with G256W acting through disruption of the SF.  

However, we agree that more support is needed. The words “dome” and “arch”, though accurate for describing shape, tend to imply a mechanical “load bearing and distributing” function --our study does not prove this. Accordingly, we have toned down the emphasis by removing the words “keystone”, “turret dome bonding”, and  “as a structural novelty” from the abstract.   The revised discussion section replaces arch with “arch-shaped”, calls the idea that the turret functions as a stabilizing arch a “novel hypothesis”, and proposes next experiments (with relevant citations).

Section title "Heterozygous G256W mice have neonatal seizures" does not seem to match the results since there was only one mouse that showed neonatal seizures.

Thank you, we have revised the section title.  The text is transparent regarding sample size. The discussion highlights that these seizures are rare (indeed, not previously shown for any heterozygous missense model, to our knowledge).

(2) It will be nice for the non-expert readers if the observations of "discrete seizures", "clusters", "diffuse bilateral onset", "unilateral onset" etc. are marked in Figure 1.

Thank you for making this point. Figure 1 shows key excerpts of one bilateral onset seizure; a unilateral onset example isn’t shown since previous KCNQ2 DEE papers we cite have emphasized and illustrated focal onset seizures (Weckhuysen et al., 2013; Numis et al., 2014).    We revised the results section (p. 4) and Figure 1 and supplement captions to improve clarity for all readers including non-specialists.  

(3) Figure 5 and page 10 first paragraph. Please specify the number of cells and the number of mice that were studied.

Thank you, this information has been added to legend.

Author response:

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

Reviewer #1 (Public Review):

[…]

(1) The authors claim that the negative frequency dependence that maintains polymorphism in their model results from a non-linear relationship between the display trait and sexual success [...] Maybe I missed something, but the authors do not provide support for their claim about the negative frequency-dependence of sexual selection in their simulations. To do so they could (1) extract the relationship between the relative mating success of the two male types from the simulations and (2) demonstrate that polymorphism is not maintained if the relationship between male display trait and mating success is linear.

We believe that there is a confusion of terminology here. We agree that for the two alleles at a locus impacting male display in our model, the allele conferring inferior display quality will have a fitness that increases as its frequency increases, so this allele displays positive frequency dependent fitness. And, the alternate, display-favoring allele at the locus does display negative frequency dependence. Our use of the terminology ‘negative frequency dependence’ was meant to refer to the negative dependence of the fitness of the display-favoring allele with respect to its own frequency. However, a significant body of literature instead discusses models in which both an allele and its alternate(s) are beneficial when at low frequency and deleterious when at high frequency under the same selective challenge, entailing negative frequency dependence of fitness for all alleles involved. This benefit-when-rare model of a single trait is often described simply as negative frequency dependence, and generates balancing selection at the locus, but is not the model we are presenting here, and does not encompass all models involving negative frequency dependent fitness. This lexical expectation may make the interpretation of our work more difficult, and we have amended the manuscript to make our model clearer (lines 227-231). In this model, we have a negative frequency dependence for the fitness of the display-favoring allele in mate competition, but the net selective disadvantage of this allele at high frequency is due to a cost in another, pleiotropic, fitness challenge: the constant survival effect. So, the alleles are under balancing selection where alternate alleles are favored by selection when rare, but not due solely to selection during mate competition. Instead, our model relies on pleiotropy for an emergent form of frequency-dependent balancing selection (in the sense that each allele is predicted to be beneficial on balance when rare).

In the reviewer’s model of the success of two alleles at one locus, the ratio of success is vaguely linear with allele frequency for n=3, though it starts quite convex and has an inflection point between convex and concave segments (for the disfavored allele) at p≈0.532. This is visualized easily by plotting the function and its derivatives in Wolfram-Alpha. For n>=4, the fitness function with respect to the display-favoring/disfavoring allele becomes increasingly concave/convex respectively, and this specific nonlinearity is needed to act along with the antagonistic pleiotropy to maintain balancing selection, rather than being maintained by a model that favors any rare allele on the basis of its rarity in some manner. In an attempt to make the importance of the encounter number parameter clearer, we’ve generated new panels for Figure S1 which simulate encounter numbers 2, 3, and 4, and we have updated corresponding text and figure references in lines 335-338.

For (1-2), it is not clear how to modify the simulation such that the relationship between the trait value and mating success can be perfectly linear - either linear with respect to allele frequency in a one locus model or linear with respect to trait value at a specific population composition, without removing the simulation of mate competition altogether. While it may be of interest to explore a more comprehensive range of biological trade-offs in future studies, we are not able to meaningfully do so within the context of the present manuscript.

(2) The authors only explore versions of the model where the survival costs are paid by females or by both sexes. We do not know if polymorphism would be maintained or not if the survival cost only affected males, and thus if sexual antagonism is crucial.

We now present simulations with male costs only as added panels to Figure S1 and mention these results in the main text (lines 334-335). Maintenance of the polymorphism is significantly reduced or completely absent in such simulations.

(3) The authors assume no cost to aneuploidy, with no justification. Biologically, investment in aneuploid eggs would not be recoverable by Drosophila females and thus would potentially act against inversions when they are rare.

We did offer some discussion and justification of our decision to model no inherent fitness of the inversion mutation itself, specifically aneuploidy, in lines 36-39 and 78-80 of the original reviewed preprint. Previous research suggests that D. melanogaster females may not actually invest in aneuploid eggs generated from crossover within paracentric inversions. While surprising, and potentially limited to a subset of clades, many ‘r-selected’ taxa or those in which maternal investment is spread out over time may have some degree of reproductive compensation for non-viable offspring, which can reduce the costs of generating aneuploids significantly (for example, t-haplotypes in mice). We have added this example and citation to lines 34ff in the current draft.

(4) The authors appear to define balanced polymorphism as a situation in which the average allele frequency from multiple simulation runs is intermediate between zero and one (e.g., Figure 3). However, a situation where 50% of simulation runs end up with the fixation of allele A and the rest with the fixation of allele B (average frequency of 0.5) is not a balanced polymorphism. The conditions for balanced polymorphism require that selection favors either variant when it is rare.

We originally chose mean final frequency for presenting the single locus simulations based on the ease of generating a visual plot that included information on fixation vs loss and equilibrium frequency. Figure 3 and related supplemental images have been changed to now also represent the proportion of simulations retaining polymorphism at the locus in the final generation.

(5) Possibly the most striking result of the experiment is the fact that for 14 out of 16 combinations of inversion x maternal background, the changes in allele frequencies between embryo and adult appear greater in magnitude in females than in males irrespective of the direction of change, being the same in the remaining two combinations. The authors interpret this as consistent with sexually antagonistic pleiotropy in the case of In(3L)Ok and In(3R)K. The frequencies of adult inversion frequencies were, however, measured at the age of 2 months, at which point 80% of flies had died. For all we know, this may have been 90% of females and 70% of males that died at this point. If so, it might well be that the effects of inversion on longevity do not systematically differ between the ages and the difference in Figure 9B results from the fact that the sample includes 30% longest-lived males and 10% longest-lived females.

This critique deserves some consideration. The aging adults were separated by sex during aging, but while we recorded the number of survivors, we did not record the numbers of eclosed adults and their sexes initially collected out of an interest in maintaining high throughput collection. We therefore cannot directly calculate the associated survival proportions, but we can estimate them. We collected 1960 females and 3156 males, and we can very roughly estimate survival if we assume that equal numbers of each sex eclosed, and that the survivors represent 20% of the original population. That gives 12790 individuals per sex, or 84.7% female mortality and 75.3% male mortality.

So, we have added a qualification discussing the possibility of stronger selection on females and its influence on observed sex-specific frequency changes, on lines 602-605.

(6) Irrespective of the above problem, survival until the age of 2 months is arguably irrelevant from the viewpoint of fitness consequences and thus maintenance of inversion polymorphism in nature. It would seem that trade-offs in egg-to-adult survival (as assumed in the model), female fecundity, and possibly traits such as females resistance to male harm would be much more relevant to the maintenance of inversion polymorphisms.

Adult Drosophila will continue to reproduce in good conditions until mortality, and the estimated age of a mean reproductive event for a Drosophila melanogaster individual is 24 days (Pool 2015), and likewise for D. simulans (Turelli and Hoffman 1995). Given that reproduction is centered around 24 days, we expect sampling at 2 months of age to still be relevant to fitness. In seasonally varying climates, either temperate or with long dry season, survival through challenging conditions is expected to require several months. In many such cases, females are in reproductive diapause, and so longevity is the main selective pressure. See lines 931-936 in the revised manuscript.

As we agreed above, it would of interest to investigate a wider range of trade-offs in future studies. We focused here on the balanced between survival and male reproductive success because the latter trait generates negative frequency dependence for display-favoring alleles and a disproportionate skew towards higher quality competitors, whereas many other fitness-relevant traits lack that property.

(7) The experiment is rather minimalistic in size, with four cages in total; given that each cage contains a different female strain, it essentially means N=1. The lack of replication makes statements like " In(2L)t and In(2R)NS each showed elevated survival with all maternal strains except ZI418N" (l. 493) unsubstantiated because the claimed special effect of ZI418N is based on a single cage subject to genetic drift and sampling error. The same applies to statements on inversion x female background interac7on (e.g., l. 550), as this is inseparable from residual variation. It is fortunate that the most interesting effects appear largely consistent across the cages/female backgrounds. Still, I am wondering why more replicates had not been included.

Our experimental approach might be described as “diversity replication”. Essentially, the four maternal genetic backgrounds are serving dual purposes – both to assess experimental consistency and to ensure that our conclusions are not solely driven by a single non-representative genotype (which in so many published studies, can not be ruled out). It would indeed be interesting if we could have quadrupled the size of our experiment by having four replicates per maternal background. However, we suspect the reviewer may not recognize the substantial effort involved in our four existing experiments. Each of these involved collecting 500+ virgin females, hand-picking thousands of embryos during the duration of egg-laying, and repeatedly transferring offspring to maintain conditions during aging, such that cages had to be staggered by more than a month. These four cages took a year of benchwork just to collect frozen samples, before any preparation and quality control of the associated amplicon libraries for sequencing. Adding a further multiplier would take it well beyond the scope of a single PhD thesis.  Fortunately, we were able to obtain the key results of interest without that additional effort, even if clearer insights into the role of maternal background would also be of strong interest.

We do agree that no firm conclusions about maternal background can be reached without further replication, and so we have qualified or removed relevant statements accordingly (lines 568ff, 620-622).

Reviewer #1 (Recommendations For The Authors):

The description of the model is confusing and incomplete, e.g., the values of several parameters used to obtain the numerical results are not given. It is first stated (l. 223) that the model is haploid, but text elsewhere talks about homozygotes and heterozygotes. If the model is diploid (this in itself is not clear), what is assumed about dominance?

We are not presenting results for a mathematical model estimated numerically. We have now clarified our transition from a conceptual depiction of our model, in which we use haploid representations for simplified presentation, to our forward population genetic simulations, which are entirely diploid. More broadly, we have improved our communication of the assumptions and parameters used in our simulations. The scenarios we investigate involve purely additive trait effects within and between loci (except that survival probabilities are multiplicative to avoid negative values). We think that considering other dominance scenarios would be a worthy subject for a follow-up study, whereas the present manuscript is already covering a great deal of ground.   

Similarly, it is hard to understand the design (l.442ff). I was confused as to whether a population was set up for each inversion or for all of them and what the unit or replication was. I found the description in Methods (l. 763-771) much clearer and only slightly longer; I suggest the authors transfer it to the Results. Also, Figure 8 should contain the entire crossing scheme; the current version is misleading in that it implies males with only two genotypes.

All four tested inversions were segregating within the same karyotypically diverse population of males, and were assayed from the same experiments. We have attempted to improve the relevant description. For Figure 8, we had trouble conceiving a graphic update that contained a more complete cross scheme without seeming much more confused and cluttered. We have tried to clarify in the relevant text and the figure caption instead.

There are a number of small issues that should be addressed:

- No epistasis for viability assumed - what would be the consequence?

We explored a model in which we intentionally included no terms for epistatic effects on phenotype. All epistasis with regard to fitness is emergent from competition between individuals with phenotypes composed of non-epistatic, non-dominant genetic effects. So, the simplest model of antagonism would have no epistasis for viability whatsoever. One could explore a model that has emergent viability epistasis in a similar way, by implementing stabilizing selection on a quantitative trait with a gaussian or similar non-linear phenotype-to-fitness map, but that might be better served as a topic for a future study. We have, however, tried to make this intent clearer in the text.

l. 750 implies that aneuploidy generated by the inversion has no cost (aneuploid games are resampled)

Yes, as addressed in public review item (3). Alternately see lines 34ff, 293, 369, 392 for in-text edits.

l. 24-25: unclear; is this to mean that there is haplotype x sex interaction for survival?

l. 25: success in what? (I assume this will be explained in the paper, but the abstract should stand on its own).

l. 193-4: "producing among most competitive males": something missing or a word too much?? Figure 1B,C: a tiny detail, but the plots would be more intuitive if the blue (average) bars were ager (i.e., to the right) of the male and female ones, given that the average is derived from the two sex-specific values.

Each of the above have been edited or implemented as suggested

l. 205. It is convex function, but I do not understand what the authors mean by "convex distribution".

Hopefully the updated text is clearer: “yielding a distribution of male reproductive output that follows a relatively convex trend”.

l. 223ff: some references to Fig 1 panels in this paragraph seem off by one letter (i.e., A should be B, etc.).

l. 231 "fitness...are equally fit": rephrase 

l. 260: maybe "thrown out" is not the most fortunate term, maybe "eliminated" would be better?

Each of the above have been edited or implemented as suggested

Figure 3: I do not understand the meaning of "additive" and "multiplicative" in the case of a single locus haploid model

All presented simulations are diploid, and these refer to the interactions between the two alleles at the locus. Hopefully the language is overall clearer in this draft.

l. 274: "Mutation of new nucleotide" meaning what? Or is it mutation _to_ a new nucleotide?

Hopefully the revised text is clearer.

Figure 5. The right panel of figure 5A implies that, with the inversion, the population evolves to an extreme display trait that is so costly that it fills 95% of all individuals (or of all females?

What is assumed about this here?). Apart from the biological realism of this result, what does it say about the accumulation of polymorphism and maintenance of the inversion? The graphs in fig 5B do plot a divergence between haplotypes, but it is not clear how they relate to those in panel A - the parameter values used to generate these plots are again not listed. Furthermore, from the viewpoint of the polymorphism, it would be good to report the frequencies at the steady-state.

We have now clarified the figure description, including the parameter values used. The distribution of frequencies at the end of the simulation is represented in figure 6. Given that we set up the simulation with assumptions that are otherwise common to population models, what biological process would prevent this extreme? Why isn’t this extreme observed in natural populations? One possible explanation is that they become sex chromosomes, with increasing likelihood as the cost increases. Or other compensatory changes may occur that we don’t simulate, like regulatory evolution giving a complementary phenotype. Maybe genetic constraints in natural populations prevent the mutation of the kind of pleiotropic mutations that drive this dynamic. The populations still survive, though they are parameterized by relative fitness. What would an absolute fitness population function be? Would it go extinct or not? It would be of interest to explore a wider range of models, but it is the purpose of this paper to establish that this is a viable model for the maintenance of sexually antagonistic polymorphism and association with inversions. We have added a paragraph motivated by this comment to the Discussion starting on line 765.

l. 401-2: Z-like, W-like : please specify you are talking about patterns resembling sex chromosomes. 

l. 738: "population calculates"?

l. 743-4 and 746-7: is this the same thing said twice, or are there two components of noise?  l. 357: there is no figure 5C.

Each of the above have been addressed with text edits.

L. 473-5: Yes, the offspring did not contain inversion homozygotes, but the sire pool did, didn't it? So homozygous inversions may have affected male reproductive success. Anyway, most of this paragraph (from line 473) seems to belong in Discussion rather than Results.

We have revised this sentence to focus on offspring survival. 

We can understand the reviewer’s suggestion about Results vs. Discussion text. While this can often be a challenging balance, we find that papers are often clearer if some initial interpretation is offered within the Results text. However, we moved the portion of this paragraph relating our findings to the published literature to the Discussion.

l. 516: " In(3L)Ok favored male survival": this is misleading/confusing given the data, " In(3L)Ok reduced female survival more strongly than male survival..."

Hopefully the phrasing is clearer now.

l. 663ff: I did not have an impression that this section added anything new and could safely be cut.

We have done some editing to make this more concise and emphasize what we think is essential, but we believe that the model of an autosomal, sexually antagonistic inversion differentiating before contributing to the origin of a sex chromosome is novel and interesting. And, that this additional emphasis is worthwhile to encourage thought and consideration of this idea in future research and among interested researchers.

l. 751: "flat probability per locus": do the authors mean a constant probability?

Edited.

Reviewer #2 (Public Review):

The manuscript lacks clarity of writing. It is impossible to fully grasp what the authors did in this study and how they reached their conclusions. Therefore, I will highlight some cases that I found problematic.

Hopefully the revised manuscript improves writing clarity. 

Although this is an interesting idea, it clearly cannot explain the apparent influence of seasonal and clinal variation on inversion frequencies.

We do not believe that our model predicts a non-existence of temporal and spatial dependence of the fitness of inverted haplotypes, nor do we seek to identify the manner in which seasonal and clinal differences affect fitness of inverted haplotypes. Rather, we argued that the influence of seasonal and clinal selection on inversions does not on its own predict the observed maintenance of inversions at low to intermediate frequencies across such a diverse geographic range, along with the higher frequencies of many derived inversions in more ancestral environments. 

We might imagine that trade-offs between life history traits such as mate competition and survival should be universal across the range of an organism. But in practice, the fitness benefits and costs of a pleiotropic variant (or haplotype) may be heavily dependent on the environment. A harsh environment such as a temperate winter may both reduce the number of females that a male encounters (decreasing the benefit of display-enhancing variants) and also increase the likelihood that survival-costly variants lead to mortality (thus increasing their survival penalty). In light of such dynamics, our model would predict that equilibrium inversion frequencies should be spatially and temporally variable, in agreement with a number of empirical observations regarding D. melanogaster inversions.

We have edited the introduction to emphasize that inversion frequencies vary temporally as well as seasonally, on lines 144ff. We also note relevant discussion of the potential interplay between the environment and trade-offs such as those we investigate, on lines 153-155.

The simulations are highly specific and make very strong assumptions, which are not well-justified.

We respond to all specific concerns expressed in the Recommendations For The Authors section below. We also note that we have made further clarifications throughout the text regarding the assumptions made in our analysis and their justification.  

Reviewer #2 (Recommendations For The Authors):

I think that the manuscript would greatly benefit from a major rewrite and probably also a reanalysis of the empirical data.

In particular, a genome-wide analysis of differences in SNP frequencies between sexes and developmental stages would help the reader to appreciate that inversions are special.

[moved up within this section for clarity] We are lacking a genomic null model-how often do the authors see similar allele frequency differences when looking at the entire genome? This could be easily done with whole genome Pool-Seq and would tell us whether inversions are really different from the genomic background. I think that this information would be essential given the many uncertainties about the statistical tests performed. 

We expect that autosome-wide SNP frequencies will be heavily influenced by the frequencies of inversions, which occur on all four major autosomal chromosome arms. These inversions often show moderate disequilibrium with distant variants (e.g. Corbett-Detig & Hartl 2012).

Furthermore, the limited number of haplotypes present, given that the paternal population was founded from 10 inbred lines, would further enhance associations between inversions and distant variants. Therefore, we do not expect that whole-genome Pool-Seq data would provide an appropriate empirical null distribution for frequency changes. Instead, we have generated appropriate null predictions by accounting for both sampling effects and experimental variance, and we have aimed to make this methodology clearer in the current draft. 

Some basic questions:

why start at a frequency of 50% (line 287)?

Isn't it obvious that in this scenario strong alleles with sexually antagonistic effects can survive?

The initial goal of the associated Figure 4 was not to show that a strongly antagonistic variant could persist. Instead, we wanted to test the linkage conditions in which a second, relatively weaker antagonistic variant survived – which did not occur in the absence of strong linkage. 

We have now added simulations with relatively lower initial frequencies, in which the weaker variant and the inversion both start at 0.05 frequency, while the stronger variant is still initialized at 0.5 to reflect the initial presence of one balanced locus with a strongly antagonistic variant. Here, the weaker antagonistic variant is still usually maintained when it is close to the stronger variant, and while the inversion-mediated maintenance of the weaker variant at greater distance from the stronger variant because less frequent than the original investigated case, it still happens often enough to hypothetically allow for such outcomes over evolutionary time-scales.

Still, we should also emphasize that the goals of this proof-of-concept analysis are to establish and convey some basic elements of our model. Subsequently, analyses such as those presented in Figures 5 and 6 provide clearer evidence that the hypothesized dynamics of inversions facilitating the accumulation of sexual antagonism actually occur in our simulations.

The experiments seem to be conducted in replicate (which is of course essential), but I could not find a clear statement of how many replicates were done for each maternal line cross.

How did the authors arrive at 16 binomial trials (line 473)? 4 inversions, 4 maternal genotypes?

How were replicates dealt with?

In Figure 9, it would be important to visualize the variation among replicates.

Unfortunately, we did not have the bandwidth to perform replicates of each maternal line. Instead, we use four maternal backgrounds to simultaneously establish consistency across independent experiments and genetic backgrounds (see our response to Reviewer 1, point 7). We’ve edited the draft to make this clearer and more clearly delineate what is supported and not supported by our data. Replicate variation for the control replicates of the extraction and sequencing process, and the exact read counts of the experiment, are available in Supplemental Tables S5, S6, and S7.

The statistical analysis of trade-off is not clear: which null model was tested? No frequency change? In my opinion, two significances are needed: a significant difference between parental and embryo and then embryo and adult offspring. The issue with this is, however, that the embryo data are used twice and an error in estimating the frequency of the embryos could be easily mistaken as antagonistic selection.

Hopefully the description of our null model is clearer in the text, now starting around line 967 in the Methods. We are aware of the positive dependence when performing tests comparing the paternal to embryo and then embryo to offspring frequencies, and this is accounted for by our analysis strategy - see lines 1009-1012.

It was not clear how the authors adjusted their chi-squared test expectations. Were they reinventing the wheel? There is an improved version of the chi-squared test, which accounts for sampling variation.

We did not actually perform chi-square tests. Instead, we used the chi statistic from the chi-squared test as a quantitative summary of the differences in read counts between samples. We compared an observed value of chi to values for this statistic obtained from simulated replicates of the experiment. Sampling from this simulation generated our ‘expected’ distribution of read counts, sampled to match sources of variance introduced in the experimental procedure, but without any effect of natural selection, per lines 825ff in the original submission. Hence, we are approximating the likelihood of observing an empirical chi statistic by generating random draws from a model of the experiment and comparing values calculated from each draw to the experimental value: a Monte Carlo method of approximating a p-value for our data. We have attempted to make the structure of these simulations and their use as a null-model clearer in this draft.

It is not sufficiently motivated why the authors model differences in the extraction procedure with a binomial distribution.

Adding a source of variance here seemed necessary as running control sequencing replicates revealed that there was residual variance not fully recapitulated by sample-size-dependent resampling. Given that we were still sampling a number of draws from a binomial outcome (the read being from the inverted or standard arrangement), a binomial distribution seemed a reasonable model, and we fit the level of this additional noise source to an experiment-wide constant, read-count or genome-count independent parameter that best fit the variance observed in the controls (lines 830ff in the original draft). Clarification is made in this manuscript draft, lines 979-989.

How many reads were obtained from each amplicon? It looks like the authors tried to mimic differences between technical replicates by a binomial distribution, which matches the noise for a given sample size, but this depends on the sequence coverage of the technical replicates.

We provide read counts in Supplemental Tables S6 and S7. The relevant paragraph in the methods has been edited for clarity, lines 972ff. Accounting for sampling differences between replicates used a hypergeometric distribution for paternal samples to account for paternal mortality before collection, and the rest were resampled with a binomial distribution. There were two additional binomial samplings, to account for resampling the read counts and to capture further residual variance in the library prep that did not seem to depend on either allele or read counts.

It would be good to see an estimate for the strength of selection: 10% difference in a single generation appears rather high to me.

Estimates of selection strength based on solving for a Wright-Fisher selection coefficient for each tested comparison can now be found in Table S8, mentioned in text on lines 589-590. The mean magnitude of selection coefficients for all paternal to embryo comparisons was 0.322, and for embryo to all adult offspring it was 0.648. For In(3L)Ok the mean selection coefficients were 0.479 and -0.53, and for In(3R)K they were -0.189 and 1.28, respectively. Some are of quite large magnitude, but we emphasize that the coefficients for embryo to adult are based on survival to old age, rather than developmental viability. That factor, in addition to the laboratory environment, makes these estimates distinct from selection coefficients that might be experienced in natural populations.

Reviewer #3 (Public Review):

Strengths:

(1) …the authors developed and used a new simulator (although it was not 100% clear as to why SLiM could not have been used as SLiM has been used to study inversions).

Before SLiM 3.7 or so (and including when we did the bulk of our simulation work), we do not think it would have been feasible to use SLiM to model the mutation of inversions with random breakpoints and recombination between without altering the SLiM internals. Separately, needing to script custom selection, mutation, and recombination functions in Eidos would have slowed SLiM down significantly. Given our greater familiarity with python and numpy, and the ability to implement a similar efficiency simulator more quickly than through learning C++ and Eidos, we chose to write our own.

It should be a fair bit easier to implement comparable simulations in SLiM now, but it will still require scripting custom mutation, selection, and recombination functions and would still result in a similarly slow runtime. The current script recipe recommended by SLiM for simulating inversions uses constants to specify the breakpoints of a single inversion, without the ability to draw multiple inversions from a mutational distribution, or model recombination between more complicated karyotypes. Hence, our simulator still seems to be a more versatile and functional option for the purposes of this study.

Weaknesses:

[Comments 1 through 4 on Weaknesses included numerous citation suggestions, and some discussion recommendations as well. In our revised manuscript, we have substantially implemented these suggestions. In particular, we have deepened our introduction of mechanisms of balancing selection and prior work on inversion polymorphism, integrating many

suggested references. While especially helpful, these suggestions are too extensive to completely quote and respond to in this already-copious document. Therefore, we focus our response on two select topics from these comments, and then proceed to comment 5 thereafter.]

(2) The general reduction principle and inversion polymorphism. In Section 1.2., the authors state that "there has not been a proposed mechanism whereby alleles at multiple linked loci would directly benefit from linkage and thereby maintain an associated inversion polymorphism under indirect selection." Perhaps I am misunderstanding something, but in my reading, this statement is factually incorrect. In fact, the simplest version of Dobzhansky's epistatic coadaptation model

(see Charlesworth 1974; also see Charlesworth and Charlesworth 1973 and discussion in Charlesworth & Flatt 2021; Berdan et al. 2023) seems to be an example of exactly what the authors seem to have in mind here: two loci experiencing overdominance, with the double heterozygote possessing the highest fitness (i.,e., 2 loci under epistatic selection, inducing some degree of LD between these loci), with subsequent capture by an inversion; in such a situation, a new inversion might capture a haplotype that is present in excess of random expectation (and which is thus filer than average)…

We agree that the quoted statement could be misleading and have rewritten it. We intended to point out that we are presenting a model in which all loci contribute additively (with respect to display) or multiplicatively (with respect to survival probability), without any dominance relationships or genetic interaction terms. And yet, the model generates epistatic balancing selection in a panmictic population under a constant environment. This represents a novel mechanism by which (the life-history characteristics of) a population would generate epistatic balancing selection as an emergent property, instead of assuming a priori that there is some balancing mechanism and representing frequency dependence, dominance effects, or epistatic interactions directly using model parameters. We have therefore refined the scope of the statement in question (lines 155-158). 

(4) Hearn et al. 2022 on Littorina saxatilis snails. 

A good reference. There is considerable work on ecotype-associated inversions in L. saxatalis, but we previously cut some discussion of this and of other populations with high gene flow but identifiable spatial structure for inversion-associated phenotypes (e.g. butterfly mimicry polymorphisms, Mimulus, etc.). Due to the spatially discrete environmental preferences and sampled ranges of the inversions in these populations, we considered these examples to be somewhat distinct from explaining inversion polymorphism in a potentially homogenous and panmictic environment. 

(4) cont. A very interesting paper that may be worth discussing is Connallon & Chenoweth (2019) about dominance reversals of antagonistically selected alleles (even though C&C do not discuss inversions): AP alleles (with dominance reversals) affecting two or more life-history traits provide one example of such antagonistically selected alleles (also see Rose 1982, 1985; Curtsinger et al. 1994) and sexually antagonistically selected alleles provide another. The two are of course not necessarily mutually exclusive, thus making a conceptual connection to what the authors model here.

We had removed a previously drafted discussion of dominance reversal for brevity’s sake, but this topic is once again represented in the updated draft of the manuscript with a short reference in the introduction, lines 76-80. We also mention ‘segregation lift’ (Wittmann et al. 2017) involving a similar reversal of dominance for fitness between temporally fluctuating conditions, as opposed to between sexes or life history stages. 

(5) The model. In general, the description of the model and of the simulation results was somewhat hard to follow and vague. There are several aspects that could be improved:  [5](1) it would help the reader if the terminology and distinction of inverted vs. standard arrangements and of the three karyotypes would be used throughout, wherever appropriate.

We have attempted to do so, using the suggested heterokaryotypic/homokaryotypic terminology.

[5](2) The mention of haploid populations/situations and haploid loci (e.g., legend to Figure 1) is somewhat confusing: the mechanism modelled here, of course, requires suppressed recombination in the inversion/standard heterokaryotype; and thus, while it may make sense to speak of haplotypes, we're dealing with an inherently diploid situation. 

While eukaryotes with haploid-dominant life history may still experience similar dynamics, we do expect that most male display competition is in diploid animals, and we are only simulating diploid fitnesses and experimenting with diploid Drosophila. We have tried to minimize the discussion of haploids in this draft.

[5](3) The authors have a situation in mind where the 2 karyotypes (INV vs. STD) in the heterokaryotype carry distinct sets of loci in LD with each other, with one karyotype/haplotype carrying antagonistic variants favoring high male display success and with the other karyotype/haplotype carrying non-antagonistic alternative alleles at these loci and which favor survival. Thus, at each of the linked loci, we have antagonistic alleles and non-antagonistic alleles - however, the authors don't mention or discuss the degree of dominance of these alleles. The degree of dominance of the alleles could be an important consideration, and I found it curious that this was not mentioned (or, for that matter, examined). 

In this study, our goal was to show that the investigated model could produce balanced and increasing antagonism without the need to invoke dominance. We think there would be a strong case for a follow-up study that more investigates how dominance and other variables impact the parameter space of balanced antagonism, but this goal is beyond our capacity to pursue in this initial study. We’ve added several lines clarifying the absence of dominance from our investigated models, and pointing out that dominance could modulate the predictions of these models (lines 211-213, 278-282).  

[5](4) In many cases, the authors do not provide sufficient detail (in the main text and the main figures) about which parameter values they used for simulations; the same is true for the Materials & Methods section that describes the simulations. Conversely, when the text does mention specific values (e.g., 20N generations, 0.22-0.25M, etc.), little or no clear context or justification is being provided. 

We have sought to clarify in this draft that 20N was chosen as an ample time frame to establish equilibrium levels and frequencies of genetic variation under neutrality. We present a time sequence in Figure 5, and these results indicate that that antagonism has stabilized in models without inversions or with higher recombination rates, whereas its rate of increase has slowed in a model with inversions and lower levels of crossing over. 

The inversion breakpoints and the position of the locus with stronger antagonistic effects in Figure 4 were chosen arbitrarily for this simple proof of concept demonstration, with the intent that this locus was close to one breakpoint. Hopefully these and other parameters are clearer in the revised manuscript.

[5](5) The authors sometimes refer to "inversion mutation(s)" - the meaning of this terminology is rather ambiguous.

Edited, hopefully the wording is clearer now. The quoted phrase had uniformly referred to the origin of new inversions by a mutagenic process. 

(6) Throughout the manuscript, especially in the description and the discussion of the model and simulations, a clearer conceptual distinction between initial "capture" and subsequent accumulation / "gain" of variants by an inversion should be made. This distinction is important in terms of understanding the initial establishment of an inversion polymorphism and its subsequent short- as well as long-term fate. For example, it is clear from the model/simulations that an inversion accumulates (sexually) antagonistic variants over time - but barely anything is said about the initial capture of such loci by a new inversion.

We do not have a good method of assessing a transition between these two phases for the simulations in which both antagonistic alleles and inversions arise stochastically by a mutagenic process. However, we have tried to be clearer on the distinction in this draft: we have included simulations in Figure 4 with variants starting at lower frequencies, and we have tried to better contextualize the temporal trajectories in Figure 5 as (in part) modeling the accumulation of variants after such an origin.

Reviewer #3 (Recommendations For The Authors):

- In general: the whole paper is quite long, and I felt that many parts could be written more clearly and succinctly - the whole manuscript would benefit from shortening, polishing, and making the wording maximally precise. Especially the Introduction (> 8 pages) and Discussion (7.5 pages) sections are quite long, and the description of the model and model results was quite hard to follow.

We have attempted to condense some portions of the manuscript, but inevitably added to others based on important reviewer suggestions. Regarding the length Introduction and Discussion, we are covering a lot of intellectual territory in this study, and we aim to make it accessible to readers with less prior familiarity. At this point, we have well over 100 citations – far more than a typical primary research paper – in part thanks to the relevant sources provided by this reviewer. We are therefore optimistic that our text will provide a valuable reference point for future studies. We have also made significant efforts to clarify the Results and Methods text in this draft without notably expanding these sections.

- In general: the conceptual parts of the paper (introduction, discussion) could be better connected to previous work - this concerns e.g. the theoretical mechanisms of balancing selection that might be involved in maintaining inversions; the general, theoretical role of antagonistic pleiotropy (AP) and trade-offs in maintaining polymorphisms; previously made empirical connections between inversions and AP/trade-offs; previously made empirical connections between inversions and sexual antagonism.

In the revised manuscript, we have improved the connection of these topics to prior work.

- L3: "accumulate". A clearer distinction could be made, throughout, between initial capture of alleles/haplotypes by an inversion vs. subsequent gain.

Please see point 6 in the response to the Public Review, above.

- L29: I basically agree about the enigma, however, there are quite many empirical examples in D. melanogaster / D. pseudoobscura and other species where we do know something about the nature of selection involved, e.g., cases of NFDS, spatially and temporally varying selection, fitness trade-offs, etc.

At least for our focal species, we have emphasized that geographic (and now temporal) associations have been found for some inversions. For the sake of length and focus, we probably should not go down the road of documenting each phenotypic association that has been reported for these inversions, or say too much about specific inversions found in other species. As indicated in our response to reviewer 2, some previously documented inversion-associated trade-offs may be compatible with the model presented here. However, we did locate and add to our Discussion one report of frequency-dependent selection on a D. melanogaster inversion (Nassar et al. 1973).

- L43: it is actually rather unlikely, though not impossible, that new inversions are ever completely neutral (see the review by Berdan et al. 2023).

This line was intended to convey that, in line with Said et al. 2018’s results, the structural alterations involved in common segregating inversions are not expected to contribute significantly to the phenotype and fitness (as indicated by lack of strong regulatory effects), and that their phenotypic consequences are instead due to linked variation. We have rewritten this passage to better communicate this point, now lines 44-52. Interpreting Section 2 and Figure 1 of Berdan et al. 2023, the linked variation may be what is in mind when saying that inversions are almost never neutral. We have also added a line referencing the expected linked variation of a new inversion (lines 49-52).

- L51-73: I felt this overview should be more comprehensive. The model by Kirkpatrick & Barton (2016 ) is in many ways less generic than the one of Charlesworth (1974) which essentially represents one way of modeling Dobzhansky's epistatic coadaptation. Also, the AOD mechanism is perhaps given too much weight here as this mechanism is very unlikely to be able to explain the establishment of a balanced inversion polymorphism (see Charlesworth 2023 preprint on bioRxiv). NFDS, spatially varying selection and temporally varying selection (for all of which there is quite good empirical evidence) should all be mentioned here, including the classical study of Wright and Dobzhansky (1946) which found evidence for NFDS (also see Chevin et al. 2021 in Evol. Lett.)

On reflection, we agree that we put too much emphasis on AOD and have edited the section to be more representative.

- L57. Two earlier Dobzhansky references, about epistatic coadaptation, would be: Dobzhansky, T. (1949). Observations and experiments on natural selection in Drosophila. Hereditas, 35(S1), 210-224. hlps://doi.org/10.1111/j.1601-5223.1949.tb033 34.xM; Dobzhansky, T. (1950). Genetics of natural populations. XIX. Origin of heterosis through natural selection in populations of Drosophila pseudoobscura. Genetics, 35, 288-302.hlps://doi.org/10.1093/gene7cs/35.3.288 - In general, in the introduction, the classical chapter by Lemeunier and Aulard (1992) should be cited as the primary reference and most comprehensive review of D. melanogaster inversion polymorphisms.

- L101: this is of course true, though there are some exceptions, such as In(3R)Mo.

- L110: the papers by Knibb, the chapter by Lemeunier and Aulard (1992), and the meta-analysis of INV frequencies by Kapun & Flatt (2019) could be cited here as well.

Citation suggestions integrated.

- L123 and elsewhere: the common D. melanogaster inversions are old but perhaps not THAT old - if we take the Corbett-Detig & Hartl (2012) es7mates, then most of them do not really exceed an age of Ne generations, or at least not by much. I mean: yes, they are somewhat old but not super-old (cf. discussion in Andolfatto et al. 2001).

Edited to curb any hyperbole. We agree that there are much more ancient polymorphisms in populations.

- L133-135. This needs to be rewritten: this claim is incorrect, to my mind (Charlesworth 1974; also see Charlesworth and Charlesworth 1973; discussion in Charlesworth & Flatt 2021).

Edited. See public review response (2).

- L154: the example of inversion polymorphism is actually explicitly discussed in Altenberg's and Feldman's (1987) paper on the reduction principle.

Edited to mention this. Inversions are also mentioned in Feldman et al. 1980, Feldman and Balkau 1973, Feldman 1972, and have been in discussion since the origins of the idea.

- L162ff: see Connallon & Chenoweth (2019).

Citation suggestion integrated, along with Cox & Calsbeek 2009 which seems more directly applicable, now line 185ff.

- L169: why? There is much evidence for other important trade-offs in this system.

Reworded.

- L178-179: other studies have found that trade-offs/AP contribute to the maintenance of inversion polymorphisms, e.g. Mérot et al. 2020 and Betrán et al. 1998, etc.

Added Betrán et al. 1998 - a good reference. Moved up mention of Mérot et al. 2020 from later in the text and directed readers to the Discussion, lines 202-205.

- L198. "alternate inversion karyotypes" - you mean INV vs. STD? It would be good to adopt a maximally clear, uniform terminology throughout.

Edited to communicate this better.

- L215-217: this is a theoretically well-known result due to Hazel (1943); Dickerson (1955); Robertson (1955); e.g., see the discussion in the quantative genetics book by Roff (1997) or in the review of Flatt (2020).

Citations integrated, now lines 232ff.

- L223 and L245: "haploid" - somewhat confusing (see public review). 

- L259-260: This may need some explanation. 

- L261-262: simply state that there is no recombination in D. melanogaster males.

Edited for increased clarity.

- L274 (and elsewhere): the meaning of "mutation...of new..inversion polymorphisms" is ambiguous - do you mean a polymorphic inversion and hence a new inversion polymorphism or do you mean polymorphisms/variants accumulating in an inversion?

- L275: maybe better heterokaryotypic instead of heterozygous? (note that INV homokaryotypes or STD homokaryotypes can be homo- or heterozygous, so when referring to chromosomal heterozygotes instead of heterozygous chromosomes it may be best to refer to heterokaryotypes).

Per [5](1) and [5](5) in the public review, we have edited our terminology.

- L276: referral to M&M - I found the description of the model/simulation details there to be somewhat vague, e.g. in terms of parameter settings, etc.

Further described.

- L281-282: would SLiM not have worked?

See public review response.

- L286-287: why these parameters?

Further described.

- L296ff: it is not immediately clear that the loci under consideration are polymorphic for antagonistic alleles vs. non-antagonistic alternative alleles - maybe this could be made clear very explicitly.

Edited to be explicit as suggested.

- L341, 343: "inversion mutation" - meaning ambiguous.

- L348, 352: "specified rate" - vague.

- L354-357: initial capture and/or accumulation/gain? 

- L401, 402, 404: Z-, W- and Y- are brought up here without sufficient context/explanation.

The above have been addressed by edits in the text.

- L523, 557, 639, 646, and elsewhere: not the first evidence - see the paper by Mérot et al. (2020) (and e.g. also by Yifan Pei et al. (2023)). 

Citations integrated in the introduction and discussion. Mérot et al. (2020) was cited (L486 in original) but discussion was curtailed in the previous draft. 

- L558-559. I agree but it is clear that there are many mechanisms of balancing selection that can achieve this, at least in principle; for some of them (NFDS, etc.) we have pretty good evidence. 

- L576-577. This is correct but for In(3R)C that study did find a differential hot vs. cold selection response.

Addressed with text edit. 

- L584-L586: cf. Betrán et al. (1998), Mérot et al. (2020), Pei et al. (2023), etc.

- L591. "other forms of balancing selection": yes! This should be stressed throughout. Multiple forms of balancing selection exist and they are not mutually exclusive. 

- L593: consider adding Dobzhansky (1943), Machado et al. (2021) 

- L596-597: this is rather unlikely, at least in terms of inversion establishment (see Charlesworth 2023; hlps://www.biorxiv.org/content/10.1101/2023.10.16.562579v1).

- L608: consider adding Kapun & Flal (2019). 

- L611-612: see studies by Mukai & Yamaguchi, 1974; and Watanabe et al., 1976. 

- L639, 646: AP - see general literature on AP as a factor in maintaining polymorphism (Rose

1982, 1985; Curtsinger et al. 1994; Charlesworth & Hughes 2000 chapter in Lewontin Festschrift; Conallon & Chenoweth 2019 - this latter paper is par7cularly relevant in terms of AP effects in the context of sexual antagonism) 

Citation suggestions integrated.

- L657: inversion polymorphism is explicitly discussed in Altenberg's and Feldman's (1987) paper on the reduction principle.

Hopefully this is better communicated.

- L724-755: I felt that this section generally lacks sufficient details, especially in terms of parameter choices and settings for the simula7ons. 

- L732L: why not state these rates?

Parameter values are now given a fuller description in figure legends and in the methods.  

- L746: but we know that mutational effect sizes are not uniformly distributed (?).

We made this choice for simplicity and to avoid invoking seemingly arbitrary distribution, but one could instead simulate trait effects with some gamma distribution. Display values would still have variable fitness effects that fluctuate with population composition, but we agree that distribution shifted toward small effects would be more realistic.

- L765: In(3R)P is not mentioned elsewhere - is this really correct?

That was incorrect, fixed.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Malaria parasites detoxify free heme molecules released from digested host hemoglobins by biomineralizing them into inert hemozoin. Thus, why malaria parasites retain PfHO, a dead enzyme that loses the capacity of catabolizing heme, is an outstanding question that has puzzled researchers for more than a decade. In the current manuscript, the authors addressed this question by first solving the crystal structure of PfHO and aligning it with structures of other heme oxygenase (HO) proteins. They found that the N-terminal 95 residues of PfHO, which failed to crystalize due to their disordered nature, may serve as signal and transit peptides for PfHO subcellular localization. This was confirmed by subsequent microscopic analysis with episomally expressed PfHO-GFP and a GFP reporter fused to the first 83 residues of PfHO (PfHO N-term-GFP). To investigate the functional importance of PfHO, the authors generated an anhydrotetracycline (aTC) controlled PfHO knockdown strain. Strikingly, the parasites lacking PfHO failed to grow and lost their apicoplast. Finally, by chromatin immunoprecipitation (ChIP), quantitative PCR/RT-PCR, and growth assays, the authors showed that both the cognate N-terminus and HO-like domain were required for PfHO function as an apicoplast DNA interacting protein.

The authors systemically performed multidisciplinary approaches to address this difficult question: what is the function of this enzymatically dead PfHO? I enjoyed reading this manuscript and its thoughtful discussion. This study is not of clinical importance for antimalarial treatments but also deepens our understanding of protein function evolution. While I understand these experiments are challenging to conduct in malaria parasites, the data quality of some of the experiments could be improved. For example, most of the Western blots and Southern blots are not of high quality.

We thank the reviewer for the positive comments but are a bit puzzled by the final statement about western and Southern blot quality. We agree that the two anti-PfHO western blots probed with custom antibody (Fig. 3- source data 2 and 8) have substantial background signal in the higher molecular mass region >75 kDa. However, we note that the critical region <50 kDa is clear in both cases and readily enables target band visualization. All other western blots probing GFP or HA epitopes are of high quality with minimal off-target background. We present two Southern blot images. We agree that the signal is somewhat faint for the Southern blot demonstrating on-target integration of the aptamer/TetR-DOZI plasmid (Fig. 3- fig. supplement 4), although we note that the correct band pattern for integration is visible. We also note that the accompanying genomic PCR data is unambiguous. The Southern blot for GFP-DHFRDD incorporation into the PfHO locus (Fig. 3- fig. supplement 1) has clear signal and strongly supports on-target integration. The minor background signal in the lower left region of the image does not extend into nor impact interpretation of correct clonal integration.

Reviewer #2 (Public Review):

Summary:

Blackwell et al. investigated the structure, localization, and physiological function of Plasmodium falciparum (Pf) heme oxygenase (HO). Pf and other malaria parasites scavenge and digest large amounts of hemoglobin from red cells for sustenance. To counter the potentially cytotoxic effects of heme, it is biomineralized into hemozoin and stored in the food vacuole. Another mechanism to counteract heme toxicity is through its enzymatic degradation via heme oxygenases. However, it was previously found by the authors that PfHO lacks the ability to catalyze heme degradation, raising the intriguing question of what the physiological function of PfHO is. In the current contribution, the authors determine that PfHO localizes to the apicoplast, determine its targeting sequence, establish the essentiality of PfHO for parasite viability, and determine that PfHO is required for proper maintenance of apicoplasts and apicoplast gene expression. In sum, the authors establish an essential physiological function for PfHO, thereby providing new insights into the role of PfHO in plasmodium metabolism.

Strengths:

The studies are rigorously conducted and the results of the experiments unambiguously support a role for PfHO as being an apicoplast-targeted protein required for parasite viability and maintenance of apicoplasts.

Weaknesses:

While the studies conducted are rigorous and support the primary conclusions, the lack of experiments probing the molecular function of PfHO limits the impact of the work. Nevertheless, the knowledge that PfHO is required for parasite viability and plays a role in the maintenance of apicoplasts is still an important advance.

We appreciate the positive assessment. We agree that further mechanistic understanding of PfHO function remains a key future challenge. Indeed, we made extensive efforts to unravel PfHO interactions that underpin its critical function. We elucidated key interactions with the apicoplast genome, reliance on the electropositive N-terminus, association with DNA-binding proteins, and a specific defect in apicoplast mRNA levels. The major limitation we faced in further defining PfHO function is the general lack of understanding of apicoplast transcription and broader gene expression. That limitation and the challenges to overcome it go well beyond our study and will require concerted efforts across several manuscripts (likely by multiple groups) to define the mechanistic features of apicoplast gene expression. We look forward to contributing further molecular understanding of PfHO function as broader understanding of apicoplast transcription emerges.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper investigates the effects of the explicit recognition of statistical structure and sleep consolidation on the transfer of learned structure to novel stimuli. The results show a striking dissociation in transfer ability between explicit and implicit learning of structure, finding that only explicit learners transfer structure immediately. Implicit learners, on the other hand, show an intriguing immediate structural interference effect (better learning of novel structure) followed by successful transfer only after a period of sleep.

Strengths:

This paper is very well written and motivated, and the data are presented clearly with a logical flow. There are several replications and control experiments and analyses that make the pattern of results very compelling. The results are novel and intriguing, providing important constraints on theories of consolidation. The discussion of relevant literature is thorough. In summary, this work makes an exciting and important contribution to the literature.

Weaknesses:

There have been several recent papers that have identified issues with alternative forced choice (AFC) tests as a method of assessing statistical learning (e.g. Isbilen et al. 2020, Cognitive Science). A key argument is that while statistical learning is typically implicit, AFC involves explicit deliberation and therefore does not match the learning process well. The use of AFC in this study thus leaves open the question of whether the AFC measure benefits the explicit learners in particular, given the congruence between knowledge and testing format, and whether, more generally, the results would have been different had the method of assessing generalization been implicit. Prior work has shown that explicit and implicit measures of statistical learning do not always produce the same results (eg. Kiai & Melloni, 2021, bioRxiv; Liu et al. 2023, Cognition).

We agree that numerous papers in the Statistical Learning literature discuss how different test measures can lead to different results and, in principle, using a different measure could have led to varying results in our study. In addition, we believe there are numerous additional factors relevant to this issue including the dichotomous vs. continuous nature of implicit vs. explicit learning and the complexity of the interactions between the (degree of) explicitness of the participants' knowledge and the applied test method that transcend a simple labeling of tests as implicit or explicit and that strongly constrains the type of variations the results of  different test would produce. Therefore, running the same experiments with different learning measures in future studies could provide additional interesting data with potentially different results.

However, the most important aspect of our reply concerning the reviewer's comment is that although quantitative differences between the learning rate of explicit and implicit learners are reported in our study, they are not of central importance to our interpretations. What is central are the different qualitative patterns of performance shown by the explicit and the implicit learners, i.e., the opposite directions of learning differences for “novel” and “same” structure pairs, which are seen in comparisons within the explicit group vs. within the implicit group and in the reported interaction. Following the reviewer's concern, any advantage an explicit participant might have in responding to 2AFC trials using “novel” structure pairs should also be present in the replies of 2AFC trials using the “same” structure pairs and this effect, at best, could modulate the overall magnitude of the across groups (Expl/Impl.) effect but not the relative magnitudes within one group. Therefore, we see no parsimonious reason to believe that any additional interaction between the explicitness level of participants and the chosen test type would impede our results and their interpretation. We will make a note of this argument in the revised manuscript.

Given that the explicit/implicit classification was based on an exit survey, it is unclear when participants who are labeled "explicit" gained that explicit knowledge. This might have occurred during or after either of the sessions, which could impact the interpretation of the effects.

We agree that this is a shortcoming of the current design, and obtaining the information about participants’ learning immediately after Phase 1 would have been preferred. However, we made this choice deliberately as the disadvantage of assessing the level of learning at the end of the experiment is far less damaging than the alternative of exposing the participants to the exit survey question earlier and thereby letting them achieve explicitness or influence their mindset otherwise through contemplating the survey questions before Phase 2. Our Experiment 5 shows how realistic this danger of unwanted influence is: with a single sentence alluding to pairs in the instructions of Exp 5, we  could completely change participants' quantitative performance and qualitative response pattern. Unfortunately, there is no implicit assessment of explicitness we could use in our experimental setup. We also note that given the cumulative nature of statistical learning, we expect that the effect of using an exit survey for this assessment only shifts absolute magnitudes (i.e. the fraction of people who would fall into the explicit vs. implicit groups) but not aspects of the results that would influence our conclusions.

Reviewer #2 (Public Review):

Summary:

Sleep has not only been shown to support the strengthening of memory traces but also their transformation. A special form of such transformation is the abstraction of general rules from the presentation of individual exemplars. The current work used large online experiments with hundreds of participants to shed further light on this question. In the training phase, participants saw composite items (scenes) that were made up of pairs of spatially coupled (i.e., they were next to each other) abstract shapes. In the initial training, they saw scenes made up of six horizontally structured pairs, and in the second training phase, which took place after a retention phase (2 min awake, 12 h incl. sleep, 12 h only wake, 24 h incl.

sleep), they saw pairs that were horizontally or vertically coupled. After the second training phase, a two-alternatives-forced-choice (2-AFC) paradigm, where participants had to identify true pairs versus randomly assembled foils, was used to measure the performance of all pairs. Finally, participants were asked five questions to identify, if they had insight into the pair structure, and post-hoc groups were assigned based on this. Mainly the authors find that participants in the 2-minute retention experiment without explicit knowledge of the task structure were at chance level performance for the same structure in the second training phase, but had above chance performance for the vertical structure. The opposite was true for both sleep conditions. In the 12 h wake condition these participants showed no ability to discriminate the pairs from the second training phase at all.

Strengths:

All in all, the study was performed to a high standard and the sample size in the implicit condition was large enough to draw robust conclusions. The authors make several important statistical comparisons and also report an interesting resampling approach. There is also a lot of supplemental data regarding robustness.

Weaknesses:

My main concern regards the small sample size in the explicit group and the lack of experimental control.  

The sample sizes of the explicit participants in our experiments are, indeed, much smaller than those of the implicit participants due to the process of how we obtain the members of the two groups. However, these sample sizes of the explicit groups are not small at all compared to typical experiments reported in Visual Statistical Learning studies, rather they tend to be average to large sizes. It is the sizes of the implicit subgroups that are unusually high due to the aforementioned data collecting process. Moreover, the explicit subgroups have significantly larger effect sizes than the implicit subgroup, bolstering the achieved power that is also confirmed by the reported Bayes Factors that support the “effect” or the “no effect” conclusions in the various tests ranging in value from substantial to very strong.  Based on these statistical measures,  we think the sample sizes of the explicit participants in our studies are adequate.

However, we do agree that the unbalanced nature of the sample and effect sizes can be problematic for the between-group comparisons. We aim to replace the student’s t-tests that directly compares explicit and implicit participants with Welch’s t-tests that are better suited for unequal sample sizes and variances.

As for the lack of experimental control, indeed, we could not fully randomize consolidation condition assignment. Instead, the assignment was a product of when the study was made available on the online platform Prolific. This method could, in theory, lead to an unobserved covariate, such as morningness, being unbalanced between conditions. We do not have any reasons to believe that such a condition would critically alter the effects reported in our study, but as it follows from the nature of unobserved variables, we obviously cannot state this with certainty. Therefore, we will explicitly discuss these potential pitfalls in the revised version of the manuscript.  

Reviewer #3 (Public Review):

In this project, Garber and Fiser examined how the structure of incidentally learned regularities influences subsequent learning of regularities, that either have the same structure or a different one. Over a series of six online experiments, it was found that the structure (spatial arrangement) of the first set of regularities affected the learning of the second set, indicating that it has indeed been abstracted away from the specific items that have been learned. The effect was found to depend on the explicitness of the original learning: Participants who noticed regularities in the stimuli were better at learning subsequent regularities of the same structure than of a different one. On the other hand, participants whose learning was only implicit had an opposite pattern: they were better in learning regularities of a novel structure than of the same one. This opposite effect was reversed and came to match the pattern of the explicit group when an overnight sleep separated the first and second learning phases, suggesting that the abstraction and transfer in the implicit case were aided by memory consolidation.

These results are interesting and can bridge several open gaps between different areas of study in learning and memory. However, I feel that a few issues in the manuscript need addressing for the results to be completely convincing:

(1) The reported studies have a wonderful and complex design. The complexity is warranted, as it aims to address several questions at once, and the data is robust enough to support such an endeavor. However, this work would benefit from more statistical rigor. First, the authors base their results on multiple t-tests conducted on different variables in the data. Analysis of a complex design should begin with a large model incorporating all variables of interest. Only then, significant findings would warrant further follow-up investigation into simple effects (e.g., first find an interaction effect between group and novelty, and only then dive into what drives that interaction). Furthermore, regardless of the statistical strategy used, a correction for multiple comparisons is needed here. Otherwise, it is hard to be convinced that none of these effects are spurious. Last, there is considerable variation in sample size between experiments. As the authors have conducted a power analysis, it would be good to report that information per each experiment, so readers know what power to expect in each.

Answering the questions we were interested in required us to investigate two related but separate types of effects within our data: general above-chance performance in learning, and within- and across-group differences.

Above-chance performance: As typical in SL studies, we needed to assess whether learning happened at all and which types of items were learned. For this, a comparison to the chance level is crucial and, therefore, one-sample t-test is the statistical test of choice. Note that all our t-tests were subject to experiment-wise correction for multiple comparisons using the Holm-Bonferroni procedure, as reported in the Supplementary Materials.

Within- and across-group differences: To obtain our results regarding group and partype differences and their interactions, we used mixed ANOVAs and appropriate post-hoc tests as the reviewer suggested. These results are reported in the method section.

Concerning power analysis, we will add the requested information on achieved power by experiment to the revised version of the manuscript.  

(2) Some methodological details in this manuscript I found murky, which makes it hard to interpret results. For example, the secondary results section of Exp1 (under Methods) states that phase 2 foils for one structure were made of items of the other structure. This is an important detail, as it may make testing in phase 2 easier, and tie learning of one structure to the other. As a result, the authors infer a "consistency effect", and only 8 test trials are said to be used in all subsequent analyses of all experiments. I found the details, interpretation, and decision in this paragraph to lack sufficient detail, justification, and visibility. I could not find either of these important design and analysis decisions reflected in the main text of the manuscript or in the design figure. I would also expect to see a report of results when using all the data as originally planned.  

We thank the reviewer for pointing out these critical open questions our manuscript that need further clarification. The inferred “consistency effect” is based on patterns found in the data, which show an increase in negative correlation between test types during the test phase. As this is apparently an effect of the design of the test phase and not an effect of the training phase, which we were interested in, we decided to minimize this effect as far as possible by focusing on the early test trials. For the revised version of the manuscript, we will revamp and expand how this issue was handled and also add a short comment in the main text, mentioning the use of only a subset of test trials and pointing the interested reader to the details.

Similarly, the matched sample analysis is a great addition, but details are missing. Most importantly, it was not clear to me why the same matching method should be used for all experiments instead of choosing the best matching subgroup (regardless of how it was arrived at), and why the nearest-neighbor method with replacement was chosen, as it is not evident from the numbers in Supplementary Table 1 that it was indeed the best-performing method overall. Such omissions hinder interpreting the work.

Since our approach provided four different balanced metrics (see Supp. Tables 1-4) for each matching method, it is not completely straightforward to make a principled decision across the methods. In addition, selecting the best method for each experiment separately carries the suspicion of cherry-picking the most suitable results for our purposes. For the revised version, we will expand on our description of the matching and decision process and add additional descriptive plots showing what our data looks like under each matching method for each experiment. These plots highlight that the matching techniques produce qualitatively roughly identical results and picking one of them over the other does not alter the conclusions of the test.  The plots will give the interested reader all the necessary information to assess the extent our design decisions influence our results.

(3) To me, the most surprising result in this work relates to the performance of implicit participants when phase 2 followed phase 1 almost immediately (Experiment 1 and Supplementary Experiment 1). These participants had a deficit in learning the same structure but a benefit in learning the novel one. The first part is easier to reconcile, as primacy effects have been reported in statistical learning literature, and so new learning in this second phase could be expected to be worse. However, a simultaneous benefit in learning pairs of a new structure ("structural novelty effect") is harder to explain, and I could not find a satisfactory explanation in the manuscript.  

Although we might not have worded it clearly, we do not claim that our "structural novelty effect" comes from a “benefit” in learning pairs of the novel structure. Rather, we used the term “interference” and lack of this interference. In other words, we believe that one possible explanation is that there is no actual benefit for learning pairs of the novel structure but simply unhindered learning for pairs of the novel structure and simultaneous inference for learning pairs of the same structure. Stronger interference for the same compared to the novel structure items seems as a reasonable interpretation as similarity-based interference is well established in the general (not SL-specific) literature under the label of proactive interference. We will clarify these ideas in the revised manuscript.

After possible design and statistical confounds (my previous comments) are ruled out, a deeper treatment of this finding would be warranted, both empirically (e.g., do explicit participants collapse across Experiments 1 and Supplementary Experiment 1 show the same effect?) and theoretically (e.g., why would this phenomenon be unique only to implicit learning, and why would it dissipate after a long awake break?).

Across all experiments, the explicit participants showed the same pattern of results but no significant difference between pair types, probably due to insufficiency of the available  sample sizes. We already included in the main text the collapsed explicit results across Experiments 1-4 and Supplementary Experiment 1 (p. 16).  This analysis confirmed that, indeed, there was a significant generalization for explicit participants across the two learning phases. We could re-run the same analysis for only Experiment 1 and

Supplementary Experiment 1, but due to the small sample of  N=12 in Suppl. Exp. 1, this test will be likely completely underpowered. Obtaining the sufficient sample size for this one test would require an excessive number (several hundreds) of new participants.  

In terms of theoretical treatment, we already presented our interpretation of our results in the discussion section, which we can expand on in the revised manuscript.

Author response:

eLife assessment

This study presents valuable findings on the role of a well-studied signal transduction pathway, the Slit/Robo system, in the context of the assembly of the hematopoietic niche in the Drosophila embryo. The evidence supporting the claims of the authors is solid. However, one aspect that needs attention is whether the cells are migrating and not being pushed to a more dorsal position through dorsal closure and/or other similar large-scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis and will interest developmental biologists working on molecular mechanisms of tissue morphogenesis.

We appreciate the thoughtful and quite useful comments provided by each of the referees. Our responses are noted below each referee’s comment.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study by Nelson et al. is focused on the formation of the Drosophila Posterior Signaling Center (PSC) which ultimately acts as a niche to support hematopoietic stem cells of the lymph gland (LG). Using a combination of genetics and live imaging, the authors show that PSC cells migrate as a tight collective and associate with multiple tissues during a trajectory that positions them at the posterior of the LG.

This is an important study that identifies Slit-Robo signaling as a regulator of PSC morphogenesis, and highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM), and cardioblasts (CBs) - in the coordinated development of these three tissues during organ development. However, one point requiring clarification is the idea that PSC cells exhibit a collective cell migration; it is not clear that the cells are migrating rather than being pushed to a more dorsal position through dorsal closure and/or other similar large-scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis as presented.

Since each referee asked for clarification concerning collective cell migration, we present a combined response further below, placed after the comments from Reviewer #3.

Strengths:

(1) Using the expression of Hid or Grim to ablate associated tissues, they find evidence that the VM and CB of the dorsal vessel affect PSC migration/morphology whereas the alary muscles do not. Slit is expressed by both VM and CBs, and therefore Slit-Robo signaling was investigated as PSCs express Robo.

(2) Using a combination of approaches, the authors convincingly demonstrate that Slit expression in the CBs and VM acts to support PSC positioning. A strength is the ability to knockdown slit levels in particular tissue types using the Gal4 system and RNAi.

(3) Although in the analysis of robo mutants, the PSC positioning phenotype is weaker in the individual mutants (robo1 and robo2) with only the double mutant (robo1,robo2) exhibiting a phenotype comparable to the slit RNAi. The authors make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs because PSCs show a phenotype even when CBs do not (Figure 4G).

(4) New insight into dorsal vessel formation by VM is presented in Figure 4A, B, as loss of the VM can affect dorsal vessel morphogenesis. This result additionally points to the VM as important.

Weaknesses:

(1) The authors are cautioned to temper the result that Slit-Robo signaling is intrinsic to PSC since the loss of robo may affect other cell types (besides CBs and PSCs) to indirectly affect PSC migration/morphogenesis. In fact, in the robo2, robo1 mutant, the VM appears to be incorrectly positioned (Figure 4G).

We have reexamined our wording in the relevant Results section and, given that this referee agrees that we, “make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs because PSCs show a phenotype even when CBs do not (Figure 4G)”, it was not clear how we might temper our conclusions more. Given that PSC cells express Robo1 and Robo2, and that the Vm does not contact the PSC, our ‘reasonable argument’ appears fair and parsimonious. Since we agree with the referee that a reader should be made as aware as possible of alternatives, we will add a comment to the Discussion, reminding the reader of the possibility of a secondary defect.

(2) If possible, the authors should use RNAi to knockdown Robo1 and Robo2 levels specifically in the PSCs if a Gal4 is available; might Antp.Gal4 (Fig 1K) be useful? Even if knockdown is achieved in PSCs+CBs, this would be a better/complementary experiment to support the approach outlined in Figure 4D.

While we agree that PSC-specific knockdown of Robo1 and Robo2 simultaneously would be ideal, this is not possible. First, the most-effective UAS-RNAi transgenes (that is, those in a Valium 20 backbone) are both integrated at the same chromosomal position; these cannot be simultaneously crossed with a GAL4 transgenic line to attempt double knock down. Additionally, as with all RNAi approaches that must rely on efficient knockdown over the rapid embryonic period, even having facile access to the above does not ensure the RNAi approach will cause as effective depletion as the genetic null condition that we use. Second, as the referee concedes, there is no embryonic PSC-specific GAL4. The proposed use of Antp-GAL4 would cause knockdown in many tissues (PSC, CB, Vm, epidermis and amnioserosa). This would lead to a reservation similar to that caused by our use of the straight genetic double mutant, as regards potential indirect requirement for Robo function.

(3) Movies are hard to interpret, as it seems unclear that the PSCs actively migrate rather than being pushed/moved indirectly due to association with VM and CBs/dorsal vessel.

First, the Vm does not directly contact the PSC, so it cannot be pushing the PSC dorsally. We will re-examine our text to be certain to make this clear. Second, in our analysis of bin mutants, which lack Vm, LGs and PSCs are able to reach the dorsal midline region in the absence of Vm. Finally, please see our response to Reviewer #3, point 2, for why we maintain that PSC cells are “migrating” even though some PSC cells are attached to CBs.

Reviewer #2 (Public Review):

The paper by Nelson KA, et al. explored the collective migration, coalescence, and positioning of the posterior signaling center (PSC) cells in Drosophila embryo. With live imaging, the authors observed the dynamic progress of PSC migration. Throughout this process, visceral mesoderm (VM), alary muscles (Ams), and cardioblasts (CBs) are in proximity to PSC. Genetic ablation of these tissues reveals the requirement for VM and CBs, but not AMs in this process. Genetic manipulations further demonstrated that Slit-Robo signaling was critical during PSC migration and positioning. While the genetic mechanisms of positioning the PSC were explored in much detail, including using live imaging, the functional consequence of mispositioning or (partial) absence of PSC cells has not been addressed, but would much increase the relevance of their findings. A few additional issues need to be addressed as well in this otherwise well-done study.

Major points:

(1) The only readout in their experiments is the relative correctness of PSC positioning. Importantly, what is the functional consequence if PSC is not properly positioned? This would be particularly important with robo-sli manipulations, where the PSC is present but some cells are misplaced. What is the consequence? Are the LGs affected, like the specification of their cell types, structure, and function? To address this for at least the robo-slit requirement in the PSC, it may be important to manipulate them directly in the PSC with a split Gal4 system, using Antp and Odd promoters.

We agree that the functional consequence of PSC mis-positioning is important and a relevant question to eventually address. However, virtually all markers and reagents used to assess the effect of the PSC on progenitor cells and their differentiated descendants are restricted to analyses carried out on the third larval instar - some three days after the experiments reported here. Most of the manipulated conditions in our work are no longer viable at this phase and, thus, addressing the functional consequences of a malformed PSC will require the field to develop new tools. 

As we noted in the Introduction, the consistency with which the wildtype PSC forms as a coalesced collective at the posterior of the LG strongly suggests importance of its specific positioning and shape, as has now been found for other niches (citations in manuscript). Additionally, in the Discussion we mention the existence of a gap junction-dependent calcium signaling network in the PSC that is important for progenitor maintenance. Without continuity of this network amongst all PSC cells (under conditions of PSC mis-positioning), we strongly anticipate that the balance of progenitors to differentiated hemocytes will be mis-managed, either constitutively, and / or under immune challenge conditions. 

Finally, to our knowledge, the tools do not exist to build a “split Gal4 system using Antp and Odd promoters”. The expression pattern observed using the genomic Antp-GAL4 line must be driven by endogenous enhancers–none of which have been defined by the field, and thus cannot be used in constructing second order drivers. Similarly, for odd skipped, in the embryo the extant Odd-GAL4 driver expresses only in the epidermis, with no expression in the embryonic LG. Thus, the cis regulatory element controlling Odd expression in the embryonic LG is unknown. In the future, the discovery of an embryonic PSC-specific driver will aid in addressing the specific functional consequences of PSC mis-positioning.

(2) The densely, parallel aligned fibers in the part of Figure 1J seemed to be visceral mesoderm, but further up (dorsally) that may be epidermis. It is possible that the PSC migrate together with the epidermis? This should be addressed.

See response to Reviewer #3.

(3) Although the authors described the standards of assessing PSC positioning as "normal" or "abnormal", it is rather subtle at times and variable in the mutant or KD/OE examples. The criteria should be more clearly delineated and analyzed double-blind, also since this is the only readout. Further examples of abnormal positioning in supplementary figures would also help.

We appreciate the Reviewer’s concern and acknowledge that the phenotypes we observed were indeed variable, and, at times subtle. As we show and discuss in the paper, our results revealed that the signaling requirements for proper PSC positioning are complex; this was favorably commented upon by Reviewer #1 (“...highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM), and cardioblasts (CBs) - in the coordinated development of these three tissues during organ development.…”). We suspect the phenotypic variability is attributable to any number of biological differences such as heterogeneity of PSC cells and an accompanying difference in the timing of their competence to receive and respond to Slit-Robo signaling, the timing of release of Slit from CBs and Vm, number of cells in a given PSC, which PSC cells in the cluster respond to too little or too much signaling, and/or typical variability between organisms. Furthermore, PSC positioning analyses were conducted by two of the authors, who independently came to the same conclusions. For many of the manipulations double blinding was not possible since the genotype of the embryo was discernible due to the obvious phenotype of the manipulated tissue.

(4) The Discussion is very lengthy and should [be] shortened.

We will re-examine the prose and emphasize more conciseness, while maintaining clarity for the reader.

Reviewer #3 (Public Review):

Summary:

This work is a detailed and thorough analysis of the morphogenesis of the posterior signaling center (PSC), a hematopoietic niche in the Drosophila larva. Live imaging is performed from the stage of PSC determination until the appearance of a compact lymph gland and PSC in the stage 16 embryo. This analysis is combined with genetic studies that clarify the involvement of adjacent tissue, including the visceral mesoderm, alary muscle, and cardioblasts/dorsal vessels. Lastly, the Slit/Robo signaling system is clearly implicated in the normal formation of the PSC.

Strengths:

The data are clearly presented, well documented, and fully support the conclusions drawn from the different experiments. The manuscript differs in character from the mainstay of "big data" papers (for example, no sets of single-cell RNAseq data of, for instance, PSC cells with more or less Slit input, are offered), but what it lacks in this regard, it makes up in carefully planned and executed visualizations and genetic manipulations.

Weaknesses:

A few suggestions concerning improvement of the way the story is told and contextualized.

(1) The minute cluster of PSC progenitors (5 or so cells per side) is embedded (as known before and shown nicely in this study) in other "migrating" cell pools, like the cardioblasts, pericardial cells, lymph gland progenitors, alary muscle progenitors. These all appear to move more or less synchronously. What should also be mentioned is another tissue, the dorsal epidermis, which also "moves" (better: stretches?) towards the dorsal midline during dorsal closure. Would it be reasonable to speculate (based on previously published data) that without the force of dorsal closure, operating in the epidermis, at least the lateral>medial component of the "migration" of the PSC (and neighboring tissues) would be missing? If dorsal closure is blocked, do essential components of PSC and lymph gland morphogenesis (except for the coming-together of the left and right halves) still occur? Are there any published data on this?

Each of the Reviewers is interested in our response to this very relevant question, and, thus, we will address the issue en bloc here. First, we will add a Supplementary Figure showing that LG and CBs are still able to progress medially towards the dorsal midline when dorsal closure stalls.  This rules out any major effect for the most prominent “large-scale embryo cell sheet movement” in positioning the PSC. Second, published work by Haack et. al. and Balaghi et. al. shows that CBs and leading edge epidermal cells are independently migratory, and we will add this context to the manuscript for the reader.

(2) Along similar lines: the process of PSC formation is characterized as "migration". To be fair: the authors bring up the possibility that some of the phenotypes they observe could be "passive"/secondary: "Thus, it became important to test whether all PSC phenotypes might be 'passive', explained by PSC attachment to a malforming dorsal vessel. Alternatively, the PSC defects could reflect a requirement for Robo activation directly in PSC cells." And the issue is resolved satisfactorily. But more generally, "cell migration" implies active displacement (by cytoskeletal forces) of cells relative to a substrate or to their neighbors (like for example migration of hemocytes). This to me doesn't seem really clearly to happen here for the dorsal mesodermal structures. Couldn't one rather characterize the assembly of PSC, lymph gland, pericardial cells, and dorsal vessel in terms of differential adhesion, on top of a more general adhesion of cells to each other and the epidermis, and then dorsal closure as a driving force for cell displacement? The authors should bring in the published literature to provide a background that does (or does not) justify the term "migration".

Before addressing this specifically, we remind readers of our response above that states the rationale ruling out large, embryo-scale movements, such as epidermal dorsal closure, in driving PSC positioning. So, how are PSC cells arriving at their reproducible position? This manuscript reports the first live-imaging of the PSC as it comes to be positioned in the embryo. We interpret these movies to suggest strongly that these cells are a ‘collective’ that migrates. Neither the data, nor we, are asserting that each PSC cell is ‘individually’ migrating to its final position. Rather, our data suggest that the PSC migrates as a collective. The most paradigmatic example of directed, collective cell migration, is of Drosophila ovarian border cells. That cell cluster is surrounded at all times by other cells (nurse cells, in that case), and for the collective to traverse through the tissue, the process requires constant remodeling of associations amongst the migrating cells in the collective (the border cells), as well as between cells in the collective and those outside of it (the nurse cells). In fact, the nurse cells are considered the substrate upon which border cells migrate. Note also that in collective border cell migration cells within the collective can switch neighbors, suggesting dynamic changes to cell associations and adhesions. 

In our analysis, the PSC cells exhibit qualities reminiscent of the border cells, and thus we infer that the PSC constitutes a migratory cell collective.  We also show in Figure 1H that PSC cells exhibit cellular extensions, and thus have a very active, intrinsic actin-based cytoskeleton. In fact, in Figure 1I, we point out that PSC cells shift position within the collective, which is not only a direct feature of migration, but also occurs within the border cell collective as that collective migrates. Additionally, the fact that the lateral-most PSC cells shift position in the collective while remaining a part of the collective–and they do this while executing net directional movement–makes a strong argument that the PSC is migratory, as no cell types other than PSCs are contacting the surfaces of those shifting PSC cells. Lastly, the Reviewer’s supposition that, rather than migration, dorsal mesoderm structures form via “differential adhesion, on top of a more general adhesion of cells to each other” is, actually, precisely an inherent aspect of collective cell migration as summarized above for the ovarian border collective.

In our resubmission we will adjust text citing the existing literature to better put into context the reasoning for why PSC formation based on our data is an example of collective cell migration.

(3) That brings up the mechanistic centerpiece of this story, the Slit/Robo system. First: I suggest adding more detailed data from the study by Morin-Poulard et al 2016, in the Introduction, since these authors had already implicated Slit-Robo in PSC function and offered a concrete molecular mechanism: "vascular cells produce Slit that activates Robo receptors in the PSC. Robo activation controls proliferation and clustering of PSC cells by regulating Myc, and small GTPase and DE-cadherin activity, respectively". As stated in the Discussion: the mechanism of Slit/Robo action on the PSC in the embryo is likely different, since DE-cadherin is not expressed in the embryonic PSC; however, it maybe not be THAT different: it could also act on adhesion between PSC cells themselves and their neighbors. What are other adhesion proteins that appear in the late lateral mesodermal structures? Could DN-cadherin or Fasciclins be involved?

We agree with the Reviewer that Slit-Robo signaling likely acts in part on the PSC by affecting PSC cell adhesion to each other and/or to CBs (lines 428-435). As stated in the Discussion, we do not observe Fasciclin III expression in the PSC until late stages when the PSC has already been positioned, suggesting that Fasciclin III is not an active player in PSC formation. Assessing whether the PSC expresses any other of the suite of potential cell adhesion molecules such as DN-Cadherin or other Fasciclins, and then study their potential involvement in the Slit-Robo pathway in PSC cells, would be part of a follow-up study.

Author response:

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

eLife assessment

The authors develop a self-returning self-avoiding polymer model of chromosome organization and show that their framework can recapitulate at the same time local density and large-scale contact structural properties observed experimentally by various technologies. The presented theoretical framework and the results are valuable for the community of modelers working on 3D genomics. The work provides solid evidence that such a framework can be used, is reliable in describing chromatin organization at multiple scales, and could represent an interesting alternative to standard molecular dynamics simulations of chromatin polymer models.

We appreciate the editor for an accurate description of the scope of the paper.

Public Reviews:

Reviewer #1 (Public Review):

Carignano et al propose an extension of the self-returning random walk (SRRW) model for chromatin to include excluded volume aspects and use it to investigate generic local and global properties of the chromosome 3D organization inside eukaryotic nuclei. In particular, they focus on chromatin volumic density, contact probability, and domain size and suggest that their framework can recapitulate several experimental observations and predict the effect of some perturbations.

We thanks the reviewer for the attention paid to the manuscript and all the relevant comments.

Strengths:

- The developed methodology is convincing and may offer an alternative - less computationally demanding - framework to investigate the single-cell and population structural properties of 3D genome organization at multiple scales.

- Compared to the previous SRRW model, it allows for investigation of the role of excluded volume locally.

Excluded volume is accounted for everywhere, not locally. We emphasized this on page 3, line 182:

“The method that we employ to remove overlaps is a low-temperature-controlled molecular dynamics simulation using a soft repulsive interaction potential between initially overlapping beads, that is terminated as soon as all overlaps have been resolved, as described in the Appendix 3.”


- They perform some experiments to compare with model predictions and show consistency between the two.

Weaknesses:

- The model is a homopolymer model and currently cannot fully account for specific mechanisms that may shape the heterogeneous, complex organization of chromosomes (TAD at specific positions, A/B compartmentalization, promoter-enhancer loops, etc.).

The SR-EV model is definitely not a homo-polymer, as it is not a regular concatenation of a single monomeric unit.

The model includes loops, which may happen in two ways: 1) As in the SRRW, branching structures emerging from the configuration backbone can be interpreted as nested loops and 2) A relatively long forward step followed by a return is a single loop. The model induces the formation of packing domains, which are not TADs, and are quantitatively in agreement with ChromSTEM experiments.

We consider convenient to add a new figure that will further clarify the structures obtained with the SR-EV model. The following paragraph and figure has been added in page 5:

“The density heterogeneity displayed by the SR-EV configurations can be analyzed in terms of the accessibility. One way to reveal this accessibility is by calculating the coordinations number (CN) for each nucleosome, using a coordination radius of 11.5 nm, along the SR-EV configuration. CN values range from 0 for an isolated nucleosome to 12 for a nucleosome immersed in a packing domain. In Figure 3 we show the SR-EV configuration showed in Figure 2, but colored according to CN. CN can be also considered as a measure to discriminate heterochromatin (red) and euchromatin (blue). Figure 3-A shows how the density inhomogeneity is coupled to different CN, with high CN represented in red and low CN represented in blue. Figure 3-B show a 50 nm thick slab obtained from the same configuration that clearly show the nucleosomes at the center of each packing domains are almost completely inaccesible, while those outside are open and accessible. It is also clear that the surface of the packing domains are characterized by nearly white nucleosomes, i.e. coordinated towards the center of the domain and open in the opposite direction.”

- By construction of their framework, the effect of excluded volume is only local and larger-scale properties for which excluded volume could be a main actor (formation of chromosome territories [Rosa & Everaers, PLoS CB 2009], bottle-brush effects due to loop extrusion [Polovnikov et al, PRX 2023], etc.) cannot be captured.

Excluded volume is considered for all nucleosomes, including overlapping beads distant along the polymer chain. Chromosome territories can be treated, but it is not in this case because we look at a single model chromosome.

- Apart from being a computationally interesting approach to generating realistic 3D chromosome organization, the method offers fewer possibilities than standard polymer models (eg, MD simulations) of chromatin (no dynamics, no specific mechanisms, etc.) with likely the same predictive power under the same hypotheses. In particular, authors often claim the superiority of their approach to describing the local chromatin compaction compared to previous polymer models without showing it or citing any relevant references that would show it.

We apologize if the text transmit an idea of superiority over other methods that was not intended. SR-EV is an alternative tool that may give a different, even complementary point of view, to standard polymer models.

- Comparisons with experiments are solid but are not quantified.

The comparisons that we have presented are quantitative. We do not have so far a way to characterize alpha or phi, a priori, for a particular system.

Impact:

Building on the presented framework in the future to incorporate TAD and compartments may offer an interesting model to study the single-cell heterogeneity of chromatin organization. But currently, in this reviewer's opinion, standard polymer modeling frameworks may offer more possibilities.

We thank the reviewer for the positive opinion on the potential of the presented method. The incorporation of TADs and compartments is left for a future evolution of the model as its complexity will make this work extremely long.

Reviewer #2 (Public Review):

Summary:

The authors introduce a simple Self Returning Excluded Volume (SR-EV) model to investigate the 3D organization of chromatin. This is a random walk with a probability to self-return accounting for the excluded volume effects. The authors use this method to study the statistical properties of chromatin organization in 3D. They compute contact probabilities, 3D distances, and packing properties of chromatin and compare them with a set of experimental data.

We thank the reviewer for the attention paid to our manuscript.

Strengths:

(1) Typically, to generate a polymer with excluded volume interactions, one needs to run long simulations with computationally expensive repulsive potentials like the WeeksChanlder-Anderson potential. However, here, instead of performing long simulations, the authors have devised a method where they can grow polymer, enabling quick generation of configurations.

(2) Authors show that the chromatin configurations generated from their models do satisfy many of the experimentally known statistical properties of chromatin. Contact probability scalings and packing properties are comparable with Chromatin Scanning Transmission Electron Microscopy (ChromSTEM)  experimental data from some of the cell types.

Weaknesses:

This can only generate broad statistical distributions. This method cannot generate sequence-dependent effects, specific TAD structures, or compartments without a prior model for the folding parameter alpha. It cannot generate a 3D distance between specific sets of genes. This is an interesting soft-matter physics study. However, the output is only as good as the alpha value one provides as input.

We proposed a model to create realistic chromatin configuration that we have contrasted with specific single cell experiments, and also reproducing ensemble average properties. 3D distances between genes can be calculated after mapping the genome to the SR-EV configuration. The future incorporation of the genome sequence will also allow us to describe TADs and A/B compartments. See added paragraph in the Discussion section:

“The incorporation of genomic character to the SR-EV model will allow us to study all individual single chromosomes properties, and also topological associated domains and A/B compartmentalization from ensemble of configurations as in HiC experiments. “

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major:

- In the introduction and along the text, the authors are often making strong criticisms of previous works (mostly polymer simulation-based) to emphasize the need for an alternative approach or to emphasize the outcomes of their model. Most of these statements (see below) are incomplete if not wrong. I would suggest tuning down or completely removing them unless they are explicitly demonstrated (eg, by explicit quantitative comparisons). There is no need to claim any - fake - superiority over other approaches to demonstrate the usefulness of an approach. Complementarity or redundance in the approaches could also be beneficial.

We regret if we unintentionally transmitted a claim of superiority. We have made several small edits to change that.

- Line 42-43: at least there exist many works towards that direction (including polymer modeling, but also statistical modeling). For eg, see the recent review of Franck Alber.

Line removed. Citation to Franck Alber included below in the text.

- Line 54-57: Point 1 is correct but is it a fair limitation? These models can predict TADs & compartments while SR-EV no. Point 2 is wrong, it depends on the resolution of the model and computer capacity but it is not an intrinsic limitation. Point 3 is wrong, such models can predict very well single-cell properties, and again it is not an intrinsic limitation of the model. Point 4 is incorrect. The space-filling/fractal organization was an (unfortunate) picture to emphasize the typical organization of chromosomes in the early times (2009), but crumpled polymers which are a more realistic description are not space-filling (see Halverson et al, 2013).

Text involving points 1 to 4 removed. It was unnecessary and does not change the line of the paper.

- L400-402 + 409-411: in such a model, the biphasic structure may emerge from loop extrusion but also naturally from the crumpled polymer organization. Simple crumpled polymer without loop extrusion and phase separation would also produce biphasic structures.

Yes, we agree. Also SR-EV leads to biphasic structures.

- L 448-449: any data to show that existing polymer modeling would predict a strong dependency of C_p(n) on the volumic fraction (in the range studied here)?

No, I don’t know a work predicting that.

- Fig. 4:

- Large-scale structural properties (R^2(n) and C_p(n)) are not dependent on phi. Is it surprising that by construction, SR-EV only relaxes the system locally after SRRW application?

Excluded volume is considered at all length scales. However, as the decreasing C_p curves observed in theories and experiments imply, the fraction of overlap (or contacts) is more important at small separations (local) than at large separations. Yet, it was a surprise for us to observed negligible effect on phi.

- Why not make a quantitative comparison between predicted and measured C_p(n)? Or at least plotting them on the same panel.

Panels B and C are in the same scale and show a good agreement between SR-EV and experiments. However, it is not perfectly quantitative agreement. SR-EV represents the generic structure of chromatin and perfect agreement should not be expected.

- Comparison with an average C_p(n) over all the chromosomes would be better.

Possibly, but we don’t think it adds anything to the paper.

- In Figure 5,6,7 (and related text): authors often describe some parameter values that are 'closest to experiment findings'. Can the authors quantify/justify this? The various 'closest' parameters are different. Can the authors comment?

The folding parameter and average volume fraction are chose so that the agreement is best with the displayed experimental system, different cell for each case.

- Figure 5: why not show the experimental distribution from Ou et al?

- Figure 6 & 7: experimental results. Can the authors show images from their own experiments? Can they show that cohesion/RAD21 is really depleted after auxin treatment?

It is currently under review in a different journal.

- In the Discussion, a fair discussion on the limitations of the methods (dynamics, etc) is missing.

Minor

- Line 34-36: the logical relationship between this sentence and the ones before and after is very unclear.

- Along the text, authors use the term 'connectivity' to describe 3D (Hi-C) contacts between different regions of the same chromosome/polymer. This is misleading as connectivity in polymer physics describes the connection along the polymer and not in the 3D space.

No. I don’t think we used connectivity in that sense. We agree with your statement on the use of connectivity in polymer physics, and is what we always had in mind for this model.

- Line 92: typo.

- On the SR-EV method: does the relaxation process create local knots in the structure?

We have not checked for knots.

- Table 1: the good correspondence with linker length is remarkable but likely 'fortunate', other chosen resolutions would have led to other results. Moreover, the model cannot account for the fine structure of chromatin fiber. Can the authors comment on that?

Fortunate to the extent that we sample the model parameter to overall catch the structure of chromatin.

- Line 211: 'without the need of imposing any parameter': alpha is a parameter, no?

Correct. Phrase deleted.

- L267-269 & 450-451: actually in Liu & Dekker, they do observe an effect on Hi-C map (C_p(n)), weak but significant and not negligible.

Our statements read ‘minimal’ and ‘relatively insensitive’. It is observed, but very small.

- L283-286: This is a perspective statement that should be in the discussion.

Moved to the Discussion, as suggested.

- L239-241: The authors seem to emphasize some contradictions with recent results on phase separation. This is unclear and should be relocated to discussion.

We just pointed out recent experiments, as stated. No intention to generate a discussion with any of them.

- L311-313: Unclear statement.

- L316-325: This is not results but discussion/speculation.

Moved to Discussion

- Along the text: 'promotor'-> 'promoter'. 

- Corrected.

- L364: explain more in detail PWS microscopy.

Reviewer #2 (Recommendations For The Authors):

Even though there are claims about nucleosome-resolution chromatin polymer, it is not clear that this work can generate structures with known nucleosome-resolution features. Nucleosome-level structure is much beyond a random walk with excluded volume and is driven by specific interactions. The authors should clarify this.

Author response:

We thank the editor and reviewers for their supportive comments about our modeling approach and conclusions, and for raising several valid concerns; we address them briefly below.

Concerns about model’s biological realism and impact on interpretations

The goal of this paper was to use an interpretable and modular model to investigate the impact of varying sensorimotor delays. Aspects of the model (e.g. layered architecture, modularity) are inspired by biology; at the same time, necessary abstractions and simplifications (e.g. using an optimal controller) are made for interpretability and generalizability, and they reflect common approaches from past work. The hypothesized effects of certain simplifying assumptions are discussed in detail in Section 3.5. Furthermore, the modularity of our model allows us to readily incorporate additional biological realism (e.g. biomechanics, connectomics, and neural dynamics) in future work. In the revision, we will add citations and edits to the text to clarify these points.

Concerns that the model is overly complex

To investigate the impact of sensorimotor delays on locomotion, we built a closed-loop model that recapitulates the complex joint trajectories of fly walking. We agree that locomotion models face a tradeoff between simplicity/interpretability and realism — therefore, we developed a model that was as simple and interpretable as possible, while still reasonably recapitulating joint trajectories and generalizing to novel simulation scenarios. Along these lines, we also did not select a model that primarily recreates empirical data, as this would hinder generalizability and add unnecessary complexity to the model. We do not think these design choices are significant weaknesses of this model; in fact, few comparable models account for all joints involved in locomotion, and fewer explicitly compare model kinematics with kinematics from data. We will add citations and edits to the text to clarify these points in the revision.

Concerns about the validity of the Kinematic Similarity (KS) metric to evaluate walking

We chose to incorporate only the first two PCA modes dimensions in the KS metric because the kernel density estimator performs poorly for high dimensional data. Our primary use of this metric was to indicate whether the simulated fly continues walking in the presence of perturbations. For technical reasons, it is not feasible to perform equivalent experiments on real walking flies, which is one of the reasons we explore this phenomenon with the model. We note the dramatic shift from walking to non-walking as delay increases (Figure 5). To be thorough, in the revision, we will investigate the effect of incorporating additional PCA modes, and whether this affects the interpretation of our results. We will additionally edit the discussion and presentation of the KS metric to clarify its purpose in this study. We agree with the reviewers that the KS metric is too coarse to reflect fine details of joint kinematics; indeed, in the unperturbed case, we evaluate our model’s performance using other metrics based on comparisons with empirical data (Figures 2, 7, 8).

Author response:

We thank the reviewers for their engagement and constructive comments. This provisional response aims to clarify key misconceptions, address major criticisms, and outline our revision plans.

A primary concern of the reviewers appears to be our model's limitations in addressing a broad range of empirical findings. This, however, misinterprets our core contribution. Our work centers on a cautionary tale that before advocating for newly discovered cell types and their purported special roles in spatial cognition—an approach prevalent in the field—such claims must be tested against alternative (null) hypotheses that may contradict intuitive expectations. We present such an alternative hypothesis regarding spatial cells and their assumed privileged roles. We show that key findings in the field - spatial “cell types”,  arise in a set of null models without spatial grounding (including untrained variants) despite the models not being a model for spatial processing, and we also found that they had no privileged role for representing spatial information.

Our proposal is not a new model attempting to explain the brain, and therefore we do not aim to capture every empirical finding. Indeed, we would not expect an object recognition model (and its untrained variant) with no explicit spatial grounding to account for all phenomena in spatial cognition. This underscores our key point: if there exists a basic, spatially agnostic model that can explain certain degrees of empirical findings using criteria from the literature (i.e. place, head-direction and border cells), what implications does this have for the more complex theories and models proposed as underlying mechanisms of special cell types?

Regarding concerns about the limited scope and generalizability of our setting, we will clarify that we considered multiple DNN architectures, both trained and untrained, on multiple decoding tasks (position, head direction, and nearest-wall distance). We plan to extend our experiments further as detailed in the revision plan below.

Further, there was a methodological concern about using a linear decoder on a fixed DNN for spatial decoding tasks being a form of "hacking". However, linear readout is standard practice in neuroscience to characterize information available in a neural population. Moreover, our tests on untrained networks also showed spatial decoding capabilities, suggesting it's not solely due to the linear readout.

For our full revision plan:

(1) We will revise the manuscript to better reflect these above points, clarifying our paper's stance and improving the writing to reduce misconceptions.

(2) We will address individual public reviews in more detail.

(3) We intend to address key reviewer recommendations, focusing on better situating our work within the broader context of the existing literature whilst emphasizing the null hypothesis perspective.

(4) In general, we will consider additional aspects of the literature and conduct new experiments to strengthen the relevance of our work to existing work. We highlight a number of potential experiments which we believe can address reviewer concerns:

a. Blurring the visual inputs to DNNs to match rodent perception.

b. Vary environmental settings to verify whether our findings are more

generalizable (which we predict to be the case).

c. Vary the environment to assess remapping effects, which will strengthen the

connection of our work to the literature.

Author response:

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

Public Reviews

Reviewer #1 (Public Review):

Summary:

Federer et al. tested AAVs designed to target GABAergic cells and parvalbumin-expressing cells in marmoset V1. Several new results were obtained. First, AAV-h56D targeted GABAergic cells with >90% specificity, and this varied with serotype and layer. Second, AAV-PHP.eB.S5E2 targeted parvalbumin-expressing neurons with up to 98% specificity. Third, the immunohistochemical detection of GABA and PV was attenuated near viral injection sites.

Strengths:

Vormstein-Schneider et al. (2020) tested their AAV-S5E2 vector in marmosets by intravenous injection. The data presented in this manuscript are valuable in part because they show the transduction pattern produced by intraparenchymal injections, which are more conventional and efficient.

Our manuscript additionally provides detailed information on the laminar specificity and coverage of these viral vectors, which was not investigated in the original studies.

Weaknesses:

The conclusions regarding the effects of serotype are based on data from single injection tracks in a single animal. I understand that ethical and financial constraints preclude high throughput testing, but these limitations do not change what can be inferred from the measurements. The text asserts that "...serotype 9 is a better choice when high specificity and coverage across all layers are required". The data presented are consistent with this idea but do not make a strong case for it.

We are aware of the limitations of our results on the AAV-h56D. We agree with the Reviewer that a single injection per serotype does not allow us to make strong statements about differences between the 3 serotypes. Therefore, in the revised version of the manuscript we have tempered our claims about such differences and use more caution in the interpretation of these data (Results p. 6 and Discussion p.10). Despite this weakness, we feel that these data still demonstrate high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested. We feel that in itself this is sufficiently useful information for the primate community, worthy of being reported. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.

A related criticism extends to the analysis of Injection volume on viral specificity. Some replication was performed here, but reliability across injections was not reported. My understanding is that individual ROIs were treated as independent observations. These are not biological replicates (arguably, neither are multiple injection tracks in a single animal, but they are certainly closer). Idiosyncrasies between animals or injections (e.g., if one injection happened to hit one layer more than another) could have substantial impacts on the measurements. It remains unclear which results regarding injection volume or serotype would hold up had a large number of injections been made into a large number of marmosets.

For the AAV-S5E2, we made a total of 7 injections (at least 2 at each volume), all of which, irrespective of volume, resulted in high specificity and efficiency for PV interneurons. Our conclusion is that larger volumes are slightly less specific, but the differences are minimal and do not warrant additional injections. Additionally, we kept all the other parameters across animals constant (see new Supplementary Table 1), all of our injections involved all cortical layers, and the ROIs we selected for counts encompassed reporter protein expression across all layers. To provide a better sense of the reliability of the results across injections, in the revised version of the manuscript we now provide results for each of the AAV-S5E2 injection case separately in a new Supplementary Table 2. The results in this table indicate the results are indeed rather consistent across cases with slightly greater specificity for injection volumes in the range of 105-180 nl.

Reviewer #2 (Public Review):

This is a straightforward manuscript assessing the specificity and efficiency of transgene expression in marmoset primary visual cortex (V1), for 4 different AAV vectors known to target transgene expression to either inhibitory cortical neurons (3 serotypes of AAV-h56D-tdTomato) or parvalbumin (PV)+ inhibitory cortical neurons in mice. Vectors are injected into the marmoset cortex and then postmortem tissue is analyzed following antibody labeling against GABA and PV. It is reported that: "in marmoset V1 AAV-h56D induces transgene expression in GABAergic cells with up to 91-94% specificity and 80% efficiency, depending on viral serotype and cortical layer. AAV-PHP.eB-S5E2 induces transgene expression in PV cells across all cortical layers with up to 98% specificity and 86-90% efficiency."

These claims are largely supported but slightly exaggerated relative to the actual values in the results presented. In particular, the overall efficiency for the best h56D vectors described in the results is: "Overall, across all layers, AAV9 and AAV1 showed significantly higher coverage (66.1{plus minus}3.9 and 64.9%{plus minus}3.7)". The highest coverage observed is just in middle layers and is also less than 80%: "(AAV9: 78.5%{plus minus}9.1; AAV1: 76.9%{plus minus}7.4)".

In the abstract, we indeed summarize the overall data and round up the decimals, and state that these percentages are upper bound but that they vary by serotype and layer while in the Results we report the detailed counts with decimals. To clarify this, in the revised version of the Abstract we have changed 80% to 79% and emphasize even more clearly the dependence on serotype and layer. We have amended this sentence of the Abstract as follows: “We show that in marmoset V1 AAV-h56D induces transgene expression in GABAergic cells with up to 91-94% specificity and 79% efficiency, but this depends on viral serotype and cortical layer.”

For the AAV-PHP.eB-S5E2 the efficiency reported in the abstract (“86-90%) is also slightly exaggerated relative to the results: “Overall, across all layers coverage ranged from 78%{plus minus}1.9 for injection volumes >300nl to 81.6%{plus minus}1.8 for injection volumes of 100nl.”

Indeed, the numbers in the Abstract are upper bounds, for example efficiency in L4A/B with S5E2 reaches 90%. To further clarify this important point, in the revised abstract we now state ”AAV-PHP.eB-S5E2 induces transgene expression in PV cells across all cortical layers with up to 98% specificity and 86-90% efficiency, depending on layer”.

These data will be useful to others who might be interested in targeting transgene expression in these cell types in monkeys. Suggestions for improvement are to include more details about the vectors injected and to delete some comments about results that are not documented based on vectors that are not described (see below).

Major comments:

Details provided about the AAV vectors used with the h56D enhancer are not sufficient to allow assessment of their potential utility relative to the results presented. All that is provided is: "The fourth animal received 3 injections, each of a different AAV serotype (1, 7, and 9) of the AAV-h56D-tdTomato (Mehta et al., 2019), obtained from the Zemelman laboratory (UT Austin)." At a minimum, it is necessary to provide the titers of each of the vectors. It would also be helpful to provide more information about viral preparation for both these vectors and the AAVPHP.eB-S5E2.tdTomato. Notably, what purification methods were used, and what specific methods were used to measure the titers?

We thank the Reviewer for this comment. In the revised version of the manuscript, we now provide a new Supplementary Table 1 with titers and other information for each viral vector injection. We also provide information regarding viral preparation in a new sections in the Methods entitled “ Viral Preparation”  (p12).

The first paragraph of the results includes brief anecdotal claims without any data to support them and without any details about the relevant vectors that would allow any data that might have been collected to be critically assessed. These statements should be deleted. Specifically, delete: “as well as 3 different kinds of PV-specific AAVs, specifically a mixture of AAV1-PaqR4-Flp and AAV1-h56D-mCherry-FRT (Mehta et al., 2019), an AAV1-PV1-ChR2-eYFP (donated by G. Horwitz, University of Washington),” and delete “Here we report results only from those vectors that were deemed to be most promising for use in primate cortex, based on infectivity and specificity. These were the 3 serotypes of the GABA-specific pAAV-h56D-tdTomato, and the PV-specific AAVPHP.eB-S5E2.tdTomato.” These tools might in fact be just as useful or even better than what is actually tested and reported here, but maybe the viral titer was too low to expect any expression.

These data are indeed anecdotal, but we felt this could be useful information, potentially preventing other primate labs from wasting resources, animals and time, particularly, as some of these vectors have been reported to be selective and efficient in primate cortex, which we have not been able to confirm. We made several injections in several animals of those vectors that failed either to infect a sufficient number of cells or turned out to be poorly specific. Therefore, the negative results have been consistent in our hands. But we agree with the Reviewer that our negative results could have depended on factors such as titer. In the revised version of the manuscript, following the reviewer’s suggestion, we have deleted this information.

Based on the description in the Methods it seems that no antibody labeling against TdTomato was used to amplify the detection of the transgenes expressed from the AAV vectors. It should be verified that this is the case - a statement could be added to the Methods.

That is indeed the case. We used no immunohistochemistry to enhance the reporter proteins as this was unnecessary. The native/ non-amplified tdT signal was strong. This is now stated in the methods (p.12).

Reviewer #3 (Public Review):

Summary:

Federer et al. describe the laminar profiles of GABA+ and of PV+ neurons in marmoset V1. They also report on the selectivity and efficiency of expression of a PV-selective enhancer (S5E2). Three further viruses were tested, with a view to characterizing the expression profiles of a GABA-selective enhancer (h56d), but these results are preliminary.

Strengths:

The derivation of cell-type specific enhancers is key for translating the types of circuit analyses that can be performed in mice - which rely on germline modifications for access to cell-type specific manipulation - in higher-order mammals. Federer et al. further validate the utility of S5E2 as a PV-selective enhancer in NHPs.

Additionally, the authors characterize the laminar distribution pattern of GABA+ and PV+ cells in V1. This survey may prove valuable to researchers seeking to understand and manipulate the microcircuitry mediating the excitation-inhibition balance in this region of the marmoset brain.

Weaknesses:

Enhancer/promoter specificity and efficiency cannot be directly compared, because they were packaged in different serotypes of AAV.

The three different serotypes of AAV expressing reporter under the h56D promoter were only tested once each, and all in the same animal. There are many variables that can contribute to the success (or failure) of a viral injection, so observations with an n=1 cannot be considered reliable.

This is an important point that was also brough up by Reviewer 1, which we have addressed in our reply-to-Reviewer 1. For clarity and convenience, below we copy our response to Reviewer 1.

“We are aware of the limitations of our results on the AAV-h56D. We agree with the Reviewer that a single injection per serotype does not allow us to make strong statements about differences between the 3 serotypes. Therefore, in the revised version of the manuscript we will temper our claims about such differences and use more caution in the interpretation of these data. Despite this weakness, we feel that these data still demonstrate high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested. We feel that in itself this is sufficiently useful information for the primate community, worthy of being reported. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 would have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.”

The language used throughout conflates the cell-type specificity conferred by the regulatory elements with that conferred by the serotype of the virus.

Authors’ reply. In the revised version of the manuscript, we have corrected ambiguous language throughout.

Recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

My Public Review comments can be addressed by dialing down the interpretation of the data or providing appropriate caveats in the presentation of the relevant results and their discussion.

We have done so. See text additions on p. 6 of the Results and p.10 of the Discussion.

Minor comments:

92% of PV+ neurons in the marmoset cortex were GABAergic. Can the authors speculate on the identity of the 8% PV+/GABA- neurons (e.g., on the basis of morphology)? Are they likely excitatory? Are they more likely to represent failures of GABA staining?

We do not know what the other 8% of PV+/GABA- neurons are because we did not perform any other kind of IHC staining. Our best guess is that at least to some extent these represent failures of GABA staining, which is always challenging to perform in primate cortex. However, in mouse PV expression has been demonstrated in a minority of excitatory neurons.

"Coverage of the PV-AAV was high, did not depend on injection volume.." The fact that the coverage did not depend on injection volume presumably depends, at least in part, on how ROIs were selected. Surely different volumes of injection transduce different numbers of neurons at different distances from the injection track. This should be clarified.

The ROIs were selected at the center of the injected site/expression core from sections in which the expression region encompassed all cortical layers. Of course, larger volumes of injection resulted in larger transduced regions and therefore overall larger number of transduced neurons, but we counted cells only withing 100 µm wide ROIs at the center of the injection and the percent of transduced PV cells in this core region did not vary significantly across volumes. We have clarified the methods of ROI selection (see Methods pp. 13).

Figure 2. What is meant by “absolute” in the legend for Figure 2? (How does “mean absolute density” differ from “mean density?”)

We meant not relative, but this is obvious from the units, so we have removed the word “absolute” in the legend.

Some non-significant p-values are indicated by "p>0.05" whereas others are given precisely (e.g., p = 1). Please provide precise p-values throughout. Also, the p-value from a surprisingly large number of comparisons in the first section of the results is "1". Is this due to rounding? Is it possible to get significance in a Bonferroni-corrected Kruskal-Wallis test with only 6 observations per condition?

We now report exact p values throughout the manuscript (with a couple of exceptions where, in order to avoid reporting a large number of p values which interrupts the flow of the manuscript) we provide the upper bound value and state all those comparisons were below that value). The minimum sample size for Kruskall Wallis is 5, for each group being compared, and we our sample is 6 per group.

Figure 3: The density of tdTomato-expressing cells appears to be greater at the AAV9 injection site than at the AAV1 injection site in the example sections shown. Might some of the differences between serotypes be due to this difference? I would imagine that resolving individual cells with certainty becomes more difficult as the amount of tdTomato expression increases.

There was an error in the scale bar of Fig. 3C, so that the AAV1 injection site was shown at higher magnification than indicated by the wrong scale bar. Hence the density of tdTomato appeared lower than it is. Moreover, the tdT expression region shown in Fig. 3A is a merge of two sections, while it is only from a single section in panels B and C, leading to the impression of higher density of infected cells in panel A. The pipette used for the injection in panel A was not inserted perfectly vertical to the cortical surface, resulting in an injection site that did not span all layers in a single section; thus, to demonstrate that the injection indeed encompassed all layers (and that the virus infected cells in all layers), we collapsed label from two sections. We have now corrected the magnification of panel C so that it matches the scale bar in panel A, and specify in the figure legend that panel A label is from two sections.

Text regarding Figure 3: The term “injection sizes” is confusing. I think it is intended to mean “the area over which tdTomato-expressing cells were found” but this should be clarified.

Throughout the manuscript, we have changed the term injection site to “viral-expression region”.

Figure 3: What were the titers of the three AAV-h56D vectors?

Titers are now reported in the new Supplementary Table 1.

Figure 3: The yellow box in Figure 3C is slightly larger than the yellow boxes in 3A and 3B. Is this an error or should the inset of Figure 3 have a scale bar that differs from the 50 µm scale bar in 3A?

There were indeed errors in scale bars in this figure, which we have now corrected. Now all boxes have the same scale bar.

Was MM423 one of the animals that received the AAV-h56D injections or one of the three that received AAV-S5E2 injection?

This is an animal that received a 315nl injection of AAV-PHP.eB-S5E2.tdTomato. This is now specified in the Methods (see p. 12) and in the new Supplementary Table 1.

Please provide raw cell counts and post-injection survival times for each animal.

We now provide this information in Supplementary Tables 1 and 2.

How were the different injection volumes of the AAV-S5E2 virus arranged by animal? Which volume of the AAV-S5E2 virus was injected into the two animals who received single injections?

We now provide this information in Supplementary Table 1.

Figure 6A: the point is made in the text that "[the distribution of tdT+ and PV+ neurons] did not differ significantly... peaking in L2/3 and 4C " Is the fact that the number of tdT+ and PV+ peak in layers 2/3 and 4C a consequence of these layers being thicker than the others? If so, this statement seems trivial.

No, and this is the reason why we measured density in addition to percent of cells across layers in Figure 2. Figure 2B shows that even when measuring density, therefore normalizing by area, GABA+ and PV+ cell density still peaks in L2/3 and 4. Thus, these peaks do not simply reflect the greater thickness of these layers.

Do the authors have permission to use data from Xu et al. 2010?

Yes, we do.

Reviewer #2 (Recommendations For The Authors):

Minor comments:

"Viral strategies to restrict gene expression to PV neurons have also been recently developed (Mehta et al., 2019; Vormstein-Schneider et al., 2020)." Mich et al. should also be cited here. Cell Rep. 2021;34(13):108754.

We thank the reviewer for pointing out this missing references. This is now cited.

“GABA density in L4C did not differ from any other layers, but the percent of GABA+ cells in L4C was significantly higher than in L1 (p=0.009) and 4A/B (p=<0.0001).” This and other similar observations depend on calculating the percentage of cells relative to the total number of DAPI-labeled cells in each layer. Since it is apparent that there must be considerable variability between layers, it would be helpful to add a histogram showing the densities of all DAPI-labeled cells for each layer.

This is not how we calculated density. Density, as now clarified in the Results on p. 4, was defined as the number of cells per unit area. Counts in each layer were divided by each layers’ counting area. This corrects for differences in number of total labeled cells per layer. Therefore, reporting DAPI density is not necessary (we did not count DAPI cell density per layer).

"Identical injection volumes of each serotype, delivered at 3 different cortical depths (see Methods), resulted in different injection sizes, suggesting the different serotypes have different capacity of infecting cortical neurons. AAV7 produced the smallest injection site, which additionally was biased to the superficial and deep layers, with only few cells expressing tdT in the middle layers (Fig. 3B). AAV9 (Fig. 3A) and AAV1 (Fig. 3C) resulted in larger injection sites and infected all cortical layers." Differences noted here might reflect either differences related to the AAV serotype or to differences in titers. Please add details about titers for each vector and add comments as appropriate. Another interpretation would be that there are differences in viral spread within the tissue.

We have now added Supplementary Table 1 which reports titers in addition to other information about injections. The titers and volumes used for AAV9 and AAV7 were identical, while the titer for AAV1 was higher. Therefore, the differences in infectivity, particularly the much smaller expression region obtained with AAV7 cannot be attributed to titer. Likely this is due to differences in tropism and/or viral spread among serotypes. This is now discussed (see Results p. 5bottom and 6 top).

“Recently, several viral vectors have been identified that selectively and efficiently restrict gene expression to GABAergic neurons and their subtypes across several species, but a thorough validation and characterization of these vectors in primate cortex has lacked.” Is this really a fair statement, or is the characterization presented here also lacking? Methods used by others for quantifying specificity and efficiency are essentially the same as used here. See for example Mich et al. (which is not cited).

The original validation in primates of the vectors examined in our study was based on small tissue samples and did not examine the laminar expression profile of transgene expression induced by these enhancer-AAVs. For example, the validation of the h56D-AAV in marmoset cortex in the original paper by Mehta et al (2019) was performed on a tissue biopsy with no knowledge of which cortical layers were included in the tissue sample. The only study that shows laminar expression in primate cortex (Mich et al., which is now cited), only shows qualitative images of viral expression across layers, reporting total specificity and coverage pooled across samples; moreover, the study by Mich et al.  deals with different PV-specific enhancers than the ones characterized in our study. Unlike any of the previous studies, here we have quantified specificity and coverage across layers.

"Specifically, we have shown that the GABA-specific AAV9-h56D (Mehta et al., 2019) induces transgene expression in GABAergic cells with up to 91-94% specificity and 80% coverage, and the PV-specific AAV-PHP.eB-S5E2 (Vormstein-Schneider et al., 2020) induces transgene expression in PV cells with up to 98% specificity and 86-90% coverage." These statements in the discussion repeat the somewhat exaggerated coverage numbers noted above for the Abstract.

The averages across all layers are reported in the Results. The Discussion, abstract and discussion report upper limits, and this is made clear by stating “up to”, and now we have also added “depending on layer”.

Reviewer #3 (Recommendations For The Authors):

Abstract:

• Ln 2: Can you be more specific about what you mean by the 'various functions of inhibition'? e.g. do you mean 'the various inhibitory influences on the local microcircuit' or similar?

These are listed in the introduction to the paper but there is no space in the abstract to do so. Now the sentence reads: “various computational functions of…”.

• Ln 5: 'has' to 'is'/'has been'.

The grammar here is correct “has derived”.

• Ln 6: humans are primates! Maybe change this to 'nonhuman primates'?

We have added “non-human”

• Ln n-1: 'viral vectors represent' -> 'viral vectors are'.

We have changed it to “are”

Intro:

• Many readers may expect 'VIP' to be listed as the third major sub-class of interneurons. Could you note that the 5HT3a receptor-expressing group includes VIP cells?

Done (p.3).

• "Understanding cortical inhibitory neuron function in the primate is critical for understanding cortical function and dysfunction in the model system closest to humans" - this seems close to being circular logic (not quite, but close). Could you modify this sentence to reflect why understanding cortical function and dysfunction in NHP may be of interest?

This sentence now reads (p.3):” Understanding cortical inhibitory neuron function in the primate is critical for understanding cortical function and dysfunction in the model system closest to humans, where cortical inhibitory neuron dysfunction has been implicated in many neurological and psychiatric disorders, such as epilepsy, schizophrenia and Alzheimer’s disease (Cheah et al., 2012; Verret et al., 2012; Mukherjee et al., 2019)”. We also note that this was already stated in the previous version of the paper but in the Discussion section which read (and still reads on p. 9 2nd paragraph): “It is important to study inhibitory neuron function in the primate, because it is unclear whether findings in mice apply to higher species, and inhibitory neuron dysfunction in humans has been implicated in several neurological and psychiatric disorders (Marin, 2012; Goldberg and Coulter, 2013; Lewis, 2014).”.

• "In particular, two recent studies have developed recombinant adeno-associated viral vectors (AAV) that restrict gene expression to GABAergic neurons". This sentence places the emphasis on the wrong component of the technology. The fact that AAV was used is irrelevant; these constructs could equally have been packaged in a lenti, CAV, HSV, rabies, etc. The emphasis should be on the recently developed regulatory elements (the enhancers/promoters).

Same problem with the following excerpts; this text implies that the serotype/vector confers cell-type selectivity, but the results presented do not support this assertion (the promoter/enhancer is what confers the selectivity).

• "specifically, three serotypes of an AAV that restricts gene expression to GABAergic neurons".

• "one serotype of an AAV that restricts gene expression to PV cells".

• "GABA- and PV-specific AAVs".

• "GABA-specific AAV" (in results).

• "PV-specific AAVs".

• "In this study, we have characterized several AAV vectors designed to restrict expression to GABAergic cells" (in discussion).

• "GABA-virus". GABA is a NT, not a virus.

We have modified the language in all these sections and throughout the manuscript.

Results:

• Enhancer specificity and efficiency cannot be directly compared, because they were packaged in different serotypes of AAV.

We agree, and in fact we are not making comparisons between different enhancers (i.e., S5E2 and h56D).

The three different serotypes of AAV expressing reporter under the h56D promoter were only tested once each, and all in the same animal. There are many variables that can contribute to the success (or failure) of a viral injection, so observations with an n=1 cannot be considered reliable.

The authors need to either: (1) replicate the h56D virus injections in (at least) a second animal, or (2) rewrite the paper to focus on the AAV.PhP mDlx virus alone - for which they have adequate data - and mention the h56D data as an anecdotal result, with clear warnings about the preliminary nature of the observations due to lack of replication.

We agree about the lack of sufficient data to make strong statements about the differences between serotypes for the h56D-AAV. In the revised version of the manuscript, following the Reviewers’ suggestion, we have chosen to temper our claims about differences between serotypes for the h56D enhancer and use more caution in the interpretation of these data. We feel that these data still demonstrate sufficiently high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested, to warrant their use in primates. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species. Our edits in regard to this point can be found in the Results on p. 6 and Discussion on p. 10.

• Did the authors compare h56D vs mDlx? This would be a useful and interesting comparison.

We did not.

• 3 tissue sections were used for analysis. How were these selected? Did the authors use a stereological approach?

For the analysis in Fig. 2, the 3 sections were randomly selected and for the positioning of the ROIs we selected a region in dorsal V1 anterior to the posterior pole  (to avoid laminar distortions due to the curvature of the brain). This is now specified (see p. 4).

• "both GABA+ and PV+ cells peak in layers" revise for clarity (e.g., the counts peak).

In now reads “GABA+ and PV+ cell percent and density” (see p.4).

• "we refer to this virus as GABA-AAV" these are 3 different viruses!

The idea here was to use an abbreviation instead of using the full viral name every single time. Clearly the reviewer does not like this, so we have removed this convention throughout the paper and now specify the entire viral name each time.

• "Identical injection volumes of each serotype, delivered at 3 different cortical depths (see Methods), resulted in different injection sizes". Do you mean 'resulted in different volumes of expression'?

Yes. We have now rephrased this as follows: “…resulted in viral expression regions that differed in both size as well as laminar distribution” (p.5).

• “suggesting the different serotypes have different capacity of infecting cortical neurons”. You can’t draw any firm conclusions from a single injection. The rest of this section of the results, along with the whole of Figure 4, and Figure 7a-d, is in danger of being misleading. Please remove. The best you can do here is to say ‘we injected 3 different viruses that express reporter under the h56D promoter. The results are shown in Figure 3, but these are anecdotal, as only a single injection of each virus was performed’. You could then note in the discussion to what extent these results are consistent with the existing literature (e.g., AAV9 often produces good coverage in NHP – anterograde and retrograde, AAV1 also works well in the CNS, although generally doesn’t infect as aggressively as AAV9. I’m not familiar with any attempts to use AAV7).

With respect to Fig. 4, our approach in the revised version is detailed above. For convenience we copy it below here. With respect to Fig 7A-D, we feel the results are more robust as the data from the 3 serotypes here were pooled together, as the 3 serotype similarly downregulated GABA and PV expression at the injection site, and we do not make any statement about differences among serotypes for the data shown in Fig. 7A-D.

“In the revised version of the manuscript, following the Reviewer ’s suggestion, we have chosen to temper our claims about differences between serotypes for the h56D enhancer and use more caution in the interpretation of these data (see revised text in the Results on p. 6 and in the Discussion on p. 10). We feel that these data still demonstrate sufficiently high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested, to warrant their use in primates. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.”

• Figure 3: why the large variation in tissue quality? Are the 3 upper images taken at the same magnification? If not, they need different scale bars. The cells in A (upper row) look much smaller than those in B and C, and the size of the 'inset' box varies.

We thank the reviewer for noticing this. We discovered an error in the scale bar of Fig. 3C, so that the AAV1 injection site was shown at higher magnification than indicated by the wrong scale bar. We have now corrected the error in scale bars. We have also fixed the different box sizes.

• "Overall, across all layers coverage ranged from 78%{plus minus}1.9 for injection volumes >300nl to 81.6%{plus minus}1.8 for injection volumes of 100nl." Coverage didn't differ between layers, so revise this to: "Overall, across all layers coverage ranged from 78% to 81.6%." or give an overall mean (~80%).

We have corrected the sentence as suggested by the Reviewer (see p. 8 first paragraph).

• "extending farther from the borders" -> "extending beyond the borders".

We have corrected the sentence as suggested by the Reviewer (see p. 8).

• "The reduced GABA and PV immunoreactivity caused by the viruses implies that the specificity of the viruses we have validated in this study is likely higher than estimated". Yes, but for balance you should also note that they may harm the physiology of the cell.

We have added a sentence acknowledging this to the Discussion. Specifically, on p. 10, we now state: “However, this reduced immunoreactivity raises concerns about the virus or high levels of reporter protein possibly harming the cell physiology.”

Discussion:

• "but a thorough validation and characterization of these vectors in primate cortex has lacked" better to say "has been limited", because Dimidschstein 2016 (marmoset V1) and Vormstein-schneider 2020 (macaque S1 and PFC) both reported expression in NHP.

We have added the following sentence to this paragraph of the Discussion. “In particular, previous studies have not characterized the specificity and coverage of these vectors across cortical layers.”(see p. 8).

• "whether finding in mice" -> 'whether findings in mice'.

Corrected, thanks.

• The discussion re: species differences is missing reference to Kreinen 2020 (10.1038/s41586-020-2781-z).

This reference has been added. Thanks.

• “Injections of about 200nl volume resulted in higher specificity (95% across layers) and coverage” – this is misleading. The coverage was not statistically different among injection volumes.

We have added the following sentence: ”although coverage did not differ significantly across volumes.” (see p. 10).

• "it is possible that subtle alteration of the cortical circuit upon parenchymal injection of viruses (including AAVs) leads to alteration of activity-dependent expression of PV and GABA." Or (and I would argue, more likely) the expression of large quantities of your big reporter protein compromised the function of the cell, leading to reduced expression of native proteins. You don't mention any IHC to amplify the RFP signal, so I'm assuming that your images are of direct expression. If so, you are expressing A LOT of reporter protein.

We have added a sentence acknowledging this to the Discussion. Specifically, on p. 10, we now state: “However, this reduced immunoreactivity raises concerns about the virus or high levels of reporter protein possibly harming the cell physiology.”

Methods:

• It's difficult to piece together which viruses were injected in which monkeys, at what volumes, and at what titer. Please compile this info into a table for ease of reference (including any other relevant parameters).

We now provide a Supplementary Table 1.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors of this manuscript characterize new anion conducting that is more red-shifted in its spectrum than prior variants called MsACR1. An additional mutant variant of MsACR1 that is renamed raACR has a 20 nm red-shifted spectral response with faster kinetics. Due to the spectral shift of these variants, the authors proposed that it is possible to inhibit the expression of MsACR1 and raACR with lights at 635 nm in vivo and in vitro. The authors were able to demonstrate some inhibition in vitro and in vivo with 635 nm light. Overall the new variants with unique properties should be able to suppress neuronal activities with red-shifted light stimulation.

Strengths:

The authors were able to identify a new class of anion conducting channelrhodopsin and have variants that respond strongly to lights with wavelength >550 nm. The authors were able to demonstrate this variant, MsACR1, can alter behavior in vivo with 635 nm light. The second major strength of the study is the development of a red-shifted mutant of MsACR1 that has faster kinetics and 20 nm red-shifted from a single mutation.

Weaknesses:

The red-shifted raACR appears to work much less efficiently than MsACR1 even with 635 nm light illumination both in vivo (Figure 4) and in vitro (Figure 3E) despite the 20 nm red-shift. This is inconsistent with the benefits and effects of red-shifting the spectrum in raACR. This usually would suggest raACR either has a lower conductance than MsACR1 or that the membrane/overall expression of raACR is much weaker than MsACR1. Neither of these is measured in the current manuscript.

Thank you for addressing this crucial issue. We posit that the diminished efficiency of raACR in comparison to MsACR1 WT can be attributed to the tenfold acceleration of its photocycle. As noted by Reviewer 1, the anticipated advantages associated with a red-shifted opsin, particularly in in vivo preparations, are offset by its accelerated off-kinetics. Consequently, the shorter dwell time of the open state leads to a reduced number of conducted ions per photon. Nevertheless, the operational light sensitivity is not drastically altered compared to MsACR WT (Fig. 3C). We believe that the rapid kinetics offer interesting applications, such as the precise inhibition of single action potentials through holography.

There are limited comparisons to existing variants of ACRs under the same conditions in the manuscript overall. There should be more parallel comparison with gtACR1, ZipACR, and RubyACR in identical conditions in cultured cell lines, cultured neurons, and in vivo. This should be in terms of overall performance, efficiency, and expression in identical conditions. Without this information, it is unclear whether the effects at 635 nm are due to the expression level which can compensate for the spectral shift.

We compared MsACR1 and raACR with GtACR1 in ND cells in supplemental figure 4. We concur that further comparisons could be useful to emphasise both the strengths of MsACRs and applications where they may not be as suitable. We are currently in the process of outlining a separate article. We firmly believe that each ACR variant occupies a distinct application niche, which necessitates a more comprehensive electrophysiological comparison to provide valuable insights to the scientific community.

There should be more raw traces from the recordings of the different variants in response to short pulse stimulation and long pulse stimulation to different wavelengths. It is difficult to judge what the response would be like when these types of information are missing.

We appreciate Reviewer 1's feedback and have compiled a collection of raw photoresponses, encompassing various pulse widths and wavelengths, which can be found in the Supplementary materials (Supplementary Figures 4 and 5).

Despite being able to activate the channelrhodopsin with 635 nm light, the main utility of the variant should be transcranial stimulation which was not demonstrated here.

We concur with Reviewer 1's assessment that MsACR prime application is indeed transcranial stimulation. However, it's worth emphasising that the full advantages of transcranial optical stimulation become most apparent when animals are truly freely moving without any tethered patch cords. Our ongoing research in the laboratory is dedicated to the development of a wireless LED system that can be securely affixed to the animal's skull. We aim to demonstrate the potential of these novell optogenetic approaches in the field of behavioural neuroscience in the coming year.

Figure 3B is not clearly annotated and is difficult to match the explanation in the figure legend to the figure. The action potential spikings of neurons expressing raACR in this panel are inhibited as strongly as MsACR1.

We have enhanced the figure caption and annotations for clarity. The traces presented in Figure 3B are intended to demonstrate the overall effectiveness of each variant. However, it is in the population data analysis, as depicted in Figure 3E, where the meaningful insights are revealed.

For many characterizations, the number of 'n's are quite low (3-7).

We acknowledge Reviewer 1's suggestion regarding the in vivo data and agree with the importance of including more animals, as well as control animals. However, we are committed to adhering to the principles of the 3Rs (Replacement, Reduction, Refinement) in animal research, and given the robustness of our observed effects, we will add animals to reach the minimal number of animals per condition (n = 2) to minimise unnecessary animal usage while ensuring statistical power.

We will continue to adhere to the established standards in the field, aiming for a range of 3 to 7 cells per condition, sourced from at least two independent preparations, to ensure the robustness and reliability of our in vitro data.

Reviewer #2 (Public Review):

Summary:

The authors identified a new chloride-conducting Channelrhodopsin (MsACR1) that can be activated at low light intensities and within the red part of the visible spectrum. Additional engineering of MsACR1 yielded a variant (raACR1) with increased current amplitudes, accelerated kinetics, and a 20nm red-shifted peak excitation wavelength. Stimulation of MsACR1 and raACR1 expressing neurons with 635nm in mice's primary motor cortices inhibited the animals' locomotion.

Strengths:

The in vitro characterization of the newly identified ACRs is very detailed and confirms the biophysical properties as described by the authors. Notably, the ACRs are very light sensitive and allow for efficient in vitro inhibition of neurons in the nano Watt/mm^2 range. These new ACRs give neuroscientists and cell biologists a new tool to control chloride flux over biological membranes with high temporal and spatial precision. The red-shifted excitation peaks of these ACRs could allow for multiplexed application with blue-light excited optogenetic tools such as cation-conducting channelrhodopsins or green-fluorescent calcium indicators such as GCaMP.

Weaknesses:

The in-vivo characterization of MsACR1 and raACR1 lacks critical control experiments and is, therefore, too preliminary. The experimental conditions differ fundamentally between in vitro and in vivo characterizations. For example, chloride gradients differ within neurons which can weaken inhibition or even cause excitation at synapses, as pointed out by the authors. Notably, the patch pipettes for the in vitro characterization contained low chloride concentrations that might not reflect possible conditions found in the in vivo preparations, i.e., increasing chloride gradients from dendrites to synapses.

We appreciate Reviewer 2’s feedback regarding missing control experiments. We will respond to these concerns in another section of our manuscript, as suggested.

Regarding the chloride gradient, we understand the concerns of Reviewer 2, yet we chose these ionic conditions, particularly as they were used in the initial electrical characterization of GtACR1 in a neuronal context (Mahn et al., 2016). We will make sure to provide this context in our manuscript to justify our choice of ionic conditions.

Interestingly, the authors used soma-targeted (st) MsACR1 and raACR1 for some of their in vitro characterization yielding more efficient inhibition and reduction of co-incidental "on-set" spiking. Still, the authors do not seem to have utilized st-variants in vivo.

At the time of submission, due to the long-term absence of our lab technician, we were not able to produce purified viruses. Therefore, we decided to move on with the submission. We now produced the virus externally, and will provide the experiments.

Most importantly, critical in vivo control experiments, such as negative controls like GFP or positive controls like NpHR, are missing. These controls would exclude potential behavioral effects due to experimental artifacts. Moreover, in vivo electrophysiology could have confirmed whether targeted neurons were inhibited under optogenetic stimulations.

We have several non-injected control animals that we used to calibrate this particular paradigm and never saw similar responses. However, we acknowledge the suggestion of Reviewer 2 and will include the GFP-injected control as recommended.

Some of these concerns stem from the fact that the pulsed raACR stimulation at 635 nm at 10Hz (Fig. 3E) was far less efficient compared to MsACR1, yet the in vivo comparison yielded very similar results (Fig. 4D).

As outlined previously, the accelerated photocycle of raACR results in a reduction in photocurrent amplitude, consequently diminishing the potency of inhibition per photon. In the context of in vitro stimulation, where single action potentials are recorded, this reduction in inhibition efficiency is resolved. However, in the realm of in vivo behavioural analysis, the observed effect is not contingent on single action potentials but rather stems from the disruption of the entire M1 motor network. In this context, despite the reduced efficiency of the fast-cycling raACR, it still manages to interrupt the M1 network, leading to similar behavioural outcomes.

Also, the cortex is highly heterogeneous and comprises excitatory and inhibitory neurons. Using the synapsin promoter, the viral expression paradigm could target both types and cause differential effects, which has not been investigated further, for example, by immunohistochemistry. An alternative expression system, for example, under VGLUT1 control, could have mitigated some of these concerns.

Indeed, we acknowledge the limitations of our current experimental approach. We are in the process of planning and conducting additional experiments involving cre-dependent expression of st-MSACR and st-raACR in PV-Cre mice.

Furthermore, the authors applied different light intensities, wavelengths, and stimulation frequencies during the in vitro characterization, causing varying spike inhibition efficiencies. The in vivo characterization is notably lacking this type of control. Thus, it is unclear why the 635nm, 2s at 20Hz every 5s stimulation protocol, which has no equivalent in the in vitro characterization, was chosen.

We appreciate the valuable comment from the reviewer. The objective of our in vitro characterization is to elucidate the general effects of specific stimulation parameters on the efficiency of neuronal inhibition. For instance, we aim to demonstrate that lower light intensities result in less efficient inhibition, or that pulse stimulation may lead to a less complete inhibition, albeit significantly reducing the energy input into the system.

In the in vivo characterization, we face constraints such as animal welfare considerations and limitations in available laser lines, which prevent us from exploring the entire parameter space as comprehensively as in the in vitro preparation. Additionally, it is important to note that membrane capacitance tends to be higher in vivo compared to dissociated hippocampal neurons. Consequently, we have opted for a doubled stimulation frequency from 10 Hz to 20 Hz and the stimulation pattern of 2 seconds ”on” and 5 seconds “off”. This approach allows the animals to spend less time in an arrested state while still demonstrating the effect of MsACR and variants.

In summary, the in vivo experiments did not confirm whether the observed inhibition of mouse locomotion occurred due to the inhibition of neurons or experimental artifacts.

In addition, the author's main claim of more efficient neuronal inhibition would require them to threshold MsACR1 and raACR1 against alternative methods such as the red-shifted NpHR variant Jaws or other ACRs to give readers meaningful guidance when choosing an inhibitory tool.

The light sensitivity of MsACR1 and raACR1 are impressive and well characterized in vitro. However, the authors only reported the overall light output at the fiber tip for the in vivo experiments: 0.5 mW. Without context, it is difficult to evaluate this value. Calculating the light power density at certain distances from the light fiber or thresholding against alternative tools such as NpHR, Jaws, or other ACRs would allow for a more meaningful evaluation.

We thank the reviewers for their comments.

Reviewer #1 (Recommendations For The Authors):

The study would be much strengthened if the authors can perform more experiments and characterization to support their claims, in addition to showing more raw electrophysiological traces/results and not just summary charts and graphs.

As outlined above, further experiments are planned. We appreciate the suggestion to include more raw electrophysiological traces. Photocurrent traces of all included mutants of MsACR1 measured in ND cells and traces of hippocampal neuronal measurements of non- and soma-targeted MsACR1 and raACR will be included as supplemental figures.

Reviewer #2 (Recommendations For The Authors):

Major concern:

It is unclear if the optogenetic light stimulation in Fig. 4 caused direct inhibition of neuronal activity in M1, which cell types were targeted, and how MsACR1 and raACR1 compare to other optogenetic inhibitors.

Also, the rationale for the light stimulation (635 nm, 2s, 20Hz, every 5s) is not clear.

I would suggest the following to address these concerns:

(1) M1 expression and stimulation of a negative control such as GFP to exclude that experimental artifacts cause the observed behavioral outcomes.

We are now preparing the required GFP control, and will add it to the new version of the manuscript.

(2) Expression and stimulation of NpHR as a positive control.

We will use st-GtACR1 as a positive control.

(3) Electrophysiological measurements of neuronal activity under optogenetic stimulation to confirm the effectiveness of neuronal inhibition, i.e. suppression of spontaneous firing under light etc.

We concur with Reviewer 2 regarding the potential value of incorporating such in vivo optrode recordings into our manuscript to enable readers to assess the effectiveness of MsACR. As part of our plan for the next version of the manuscript, we intend to conduct these experiments.

(4) ChR2 or other cation-conducting channelrhodopsins with the same expression paradigm could be used to observe diametrically opposite effects.

As Reviewer 2 has already pointed out, the complex interactions that can occur in our viral strategy when an inhibitory opsin is expressed in both excitatory and inhibitory neurons make us sceptical about the possibility of an excitatory opsin leading to opposing effects.

Considering the non-linear input-output function of cortical circuits, optogenetic activation of neurons, even when expressed in either inhibitory or excitatory neurons, is likely to result in the perturbation of the cortical network, which will likely also lead to locomotor arrest.

(5) The authors should confirm whether the expression under synapsin preferentially targeted excitatory and inhibitory cells because inhibiting inhibitory cells could lead to the disinhibition of the principal cells. Synapsin promoters can drive expression in glutamatergic and GABAergic neurons. An alternative expression system under VGLUT1 promoter could yield better targeting.

We concur with Reviewer 2 and will conduct the next set of experiments using the PV-Cre mouse line. Additionally, we will employ in vivo electrophysiology to further confirm the inhibition of the motor cortex network.

(6) Titrating of optogenetic stimulation: The author should test whether increasing or decreasing light intensities and stimulation frequencies as well as different wavelengths (550 nm vs 635 nm) cause differences in inhibiting locomotion in vivo as it did for inhibiting the neuronal firing in vitro (Fig. 3B-E).

The non-linear input-output function within cortical networks, coupled with our sole reliance on behaviour as a readout, will pose challenges in resolving subtle effects on locomotion arrest across various stimulation parameters.

For our planned in vivo electrophysiology recordings, we will measure cortical firing rates as a proxy rather than relying solely on behavioural observations. This approach will allow us to map the fundamental axes of our parameter space in vivo, considering factors such as wavelength, light intensity, and frequency

(7) Explanation of why the 20Hz/2s light stimulation protocol was chosen.

As outlined above, considering animal welfare and increased membrane capacitance in vivo, we opted for the outlined stimulation protocol. This approach allows the animals to spend less time in an arrested state while still demonstrating the effect of MsACR and variants.

(8) In vivo thresholding against other inhibitory tools, such as RubyACRs, Jaws, etc would provide critical guidance for the audience and potential users. It would be particularly important to compare the necessary light intensities for reaching similar behavioral outcomes.

We concur with Reviewer 2 and will prepare data using GtACR1 as a reference.

(9) The author should calculate or reasonably estimate the in vivo light intensity during optogenetic stimulation to provide a meaningful comparison to their in vitro characterization. Ideally, they can provide an estimated volume for efficient stimulation of MsACR1 and raACR1 and compare it to other optogenetic tools.

We will conduct a Monte Carlo simulation and offer a comparison of the effective activation volume across various classes of optogenetic tools.

Minor concerns:

(1) Why were st- MsACR1 and raACR1 used in vitro but not in vivo? The viral constructs were described as AAV/DJ-hSyn1-MsACR-mCerulean and AAV/DJ-hSyn1-raACR-mCerulean.

As mentioned earlier, we were unable to produce purified soma-targeted MsACR variants before the manuscript submission. We will now provide these measurements.

(2) Light intensities for the spectral measurements are missing.

During action spectra measurements, a motorised neutral density filter wheel is used to have equal photon flux for all tested wavelengths. Additionally, the light intensity is further reduced by using additional neutral density filters to ensure sufficiently low photocurrents to determine the spectral maximum. Therefore, the light intensity varied between constructs and sometimes measurements. We added the following line to the respective methods section to further clarify this: “(typically in the low µW-range at 𝜆max)”.

(3) MsACR1 is slower and probably more light-sensitive than raACR1, which is faster but has larger photocurrents. These are complementary tradeoffs, and the audience might wonder how MsACR1 and raACR1 photocurrents compare under similar conditions. Therefore, I suggest an alternative representation in Fig. 2C. That is, the presentation of the excitation spectra under similar light intensities and with absolute photocurrent values.

Unfortunately, due to the reasons stated above, MsACR1 and raACR action spectra were not recorded with the same light intensity. However, MsACR1 and raACR are compared under the same conditions for Fig. 2B, E, and F (560 nm light at ~3.2 mW/mm2) as well as in Supp. Fig. 4C.

(4) Figure legends for figures 3F and G are missing details for describing the stimulation paradigm.

We added more details about the stimulation paradigm.

Author response:

Reviewer #1 (Public Review):

Summary:

This work sets out to elucidate mechanistic intricacies in inflammatory responses in pneumonia in the context of the aging process (Terc deficiency - telomerase functionality).

Strengths:

Very interesting, conceptually speaking, approach that is by all means worth pursuing. An overall proper approach to the posited aim.

We want to thank the reviewer for taking the time to review our manuscript and for providing positive feedback regarding our research question.

Weaknesses:

The work is heavily underpowered and may have statistical deficits. This precludes it in its current state from drawing unequivocal conclusions.

Thank you for this essential and valuable comment. We fully accept that the small sample size of the Tercko/ko mice is a major limitation of our study and transparently discuss this in our manuscript.

However, due to Animal Welfare regulations, only a reduced number of mice were approved because of the strong burden of disease. Consequently, only three non-infected and five infected mice were available to us. This reduced number of mice presents a clear limitation to our study. However, due to ethical considerations related to animal welfare and sustainability, as well as compliance with German animal welfare regulations, it is not possible to obtain additional Tercko/ko mice to increase the dataset. The animal studies are an important aspect of our study; however, our hypothesis was also investigated at multiple levels, including in an in vitro co-culture model (Figure 5), to ensure comprehensive analysis.

Thus, we clearly demonstrated that S. aureus pneumonia in Tercko/ko mice leads to a more severe phenotype, orchestrated by the dysregulation of both innate and adaptive immune response.

Reviewer #2 (Public Review):

Summary:

The authors demonstrate heightened susceptibility of Terc-KO mice to S. aureus-induced pneumonia, perform gene expression analysis from the infected lungs, find an elevated inflammatory (NLRP3) signature in some Terc-KO but not control mice, and some reduction in T cell signatures. Based on that, They conclude that disregulated inflammation and T-cell dysfunction play a major role in these phenomena.

Strengths:

The strengths of the work include a problem not previously addressed (the role of the Terc component of the telomerase complex) in certain aspects of resistance to bacterial infection and innate (and maybe adaptive) immune function.

We would like to thank the reviewer for the positive feedback regarding our aim to investigate the impact of Terc deletion on the pulmonary immune response to S. aureus.

Weaknesses:

The weaknesses outweigh the strengths, dominantly because conclusions are plagued by flaws in experimental design, by lack of rigorous controls, and by incomplete and inadequate approaches to testing immune function. These weaknesses are as follows

(1)  Terc-KO mice are a genomic knockout model, and therefore the authors need to carefully consider the impact of this KO on a wide range of tissues. This, however, is not the case. There are no attempts to perform cell transfers or use irradiation chimera or crosses that would be informative.

We thank the reviewer for bringing up this important point. The aim of our study, however; was to investigate the impact of Terc deletion in the lung and on the response to bacterial pneumonia, rather than to provide a comprehensive characterization of the Tercko/ko model itself. This characterization of different tissues and cell types has already been conducted by previous studies. For instance, studies that characterize the general phenotype of the model (Herrera et al., 1999; Lee et al., 1998; Rudolph et al., 1999) but also investigations that shed light on the impact of Terc deletion on specific cell types such as microglia (Khan et al., 2015) or T cells (Matthe et al., 2022). The impact of Terc deletion on T cells is also discussed in our manuscript in lines 89 to 105. Furthermore, a section about the general phenotype of the Terc deletion model is included in the introduction in lines 126 to 138. Thus we discussed the relevant literature regarding Tercko/ko mice in our manuscript and attempted to provide a more in-depth characterization of the lung by investigating the inflammatory response to infection as well as changes in the gene expression (Figure 2-4).

(2)  Throughout the manuscript the authors invoke the role of telomere shortening in aging, and according to them, their Terc-KO mice should be one potential model for aging. Yet the authors consistently describe major differences between young Terc-KO and naturally aging old mice, with no discussion of the implications. This further confuses the biological significance of this work as presented.

Thank you for mentioning this relevant point. We want to apologize for the confusion regarding this matter. While Tercko/ko mice are a well-established model for premature aging, these effects become more apparent with increasing generations (G) and thus, G5 and 6 mice are the most affected by Terc deletion (Lee et al., 1998; Wong et al., 2008).

Thus, while Tercko/ko mice are a common model for premature aging, this accelerated aging phenotype is predominantly apparent in later-generation Tercko/ko (G5 and 6) or aged Tercko/ko mice (Lee et al., 1998; Wong et al., 2008). Since the aim of this study was to analyze the impact of Terc deletion on the lung and its immune response to bacterial infections instead of the impact of telomere shortening and telomerase dysfunction, young G3 Tercko/ko mice (8 weeks) were used in this study. This is also mentioned in the lines 131-134. In this study, Tercko/ko mice were used not as a model of aging, but rather as a model specifically for Terc deletion. The old WT mice function as a control cohort to observe possible common but also deviating effects between aging and Terc deletion. In our sequencing data, we observe that uninfected young WT mice are very similar to uninfected Tercko/ko mice. Other studies have also reported this lack of major differences between uninfected WT and Tercko/ko mice in the G3 knockout mice (Kang et al., 2018). Conversely, uninfected young WT and Tercko/ko mice exhibited great differences, for instance, regarding the numbers of differentially expressed genes (Supplemental Figure 1H). Thus, differences between naturally aged mice and young G3 Tercko/ko mice are not surprising. To clarify this aspect we reconstructed the paragraph discussing the Tercko/ko mice (lines 126-134). Additionally we added a paragraph explaining the purpose of the naturally aged mice to the lines 134 to 138:

“As control cohort age-matched young WT mice were utilized. To investigate whether Terc deletion, beyond critical telomere shortening, impacts the pulmonary immune response, we used young Tercko/ko mice. Additionally, naturally aged mice (2 years old) were infected to explore the potential link to a fully developed aging phenotype.”

(3)  Related to #2, group design for comparisons lacks a clear rationale. The authors stipulate that Terc- KO will mimic natural aging, but in fact, the only significant differences seen between groups in susceptibility to S. aureus are, contrary to the authors' expectation, between young Terc-KO and naturally old mice (Figures 1A and B, no difference between young Terc-KO and young wt); or there are no significant differences at all between groups (Figures 1, C, D,).

We thank the reviewer for this essential comment. As mentioned above the Tercko/ko mice in this study are not selected to model natural aging. To model telomerase dysfunction and accelerated aging selection of later generation or aged Tercko/ko mice would have been more suitable.

The lack of statistical significance in some figures is likely due to the heterogeneity of disease phenotype of S. aureus infection in mice, which is a limitation of our study that we discuss in our discussion section in lines 577-583. The phenotype of S. aureus infection can vary greatly within a mouse population, highlighting the limitations of mice as a model for S. aureus infections. To account for this heterogeneity we divided the infected Tercko/ko mice cohort into different degrees of severity based on the clinical score and the presence of bacteria in organs other than the lung (mice with systemic infection).

Despite the heterogeneity especially within the Tercko/ko mice cohort the differences between the knockout and young as well as old WT mice were striking. Including the fatal infections, 80% of the Tercko/ko mice had a severe course of disease, while none of the WT mice displayed a severe course (Figure 1A, B and Supplemental Figure 1A, B). This hints towards a clear role of Terc in the response to S. aureus infection in mice. Thus while in some figures the differences are not significant, strong trends towards a more severe phenotype of S. aureus infection in the Tercko/ko mice regarding bacterial load, score and inflammatory response could be observed in our study.

Another example of inadequate group design is when the authors begin dividing their Terc-KO groups by clinical score into animals with or without "systemic infection" (the condition where a bacterium spreads uncontrollably across the many organs and via blood, which should be properly called sepsis), and then compare this sepsis group to other groups (Supplementary Figures 1G; Figure 2; lines 374-376 and 389- 391). This gives them significant differences in several figures, but because they did not clearly indicate where they applied this stratification in the figure legends, the data are somewhat confusing. Most importantly, methodologically it is highly inappropriate to compare one mouse with sepsis to another one without. If Terc-KO mice with sepsis are a comparator group, then their controls have to be wild-type mice with sepsis, who are dealing with the same high bacterial load across the body and are presumably forced to deploy the same set of immune defenses.

We sincerely appreciate the significant time and effort you have invested in reviewing our manuscript. However, with all due respect, we must point out that the definition of sepsis you have referenced is considered outdated. According to the Third International Consensus Definitions for Sepsis and Septic Shock (Sepsis-3), sepsis is defined as "a life-threatening organ dysfunction caused by a dysregulated host response to infection" (Marvin Singer, 2016, JAMA). Given this fundamental misunderstanding of our findings, we find the comment regarding the inadequacy of our groups to be both dismissive and lacking in scientific merit. We would like to emphasize that the group size used in our study is consistent with accepted standards in infection research. We strongly reject any insinuations of inadequacy that have been repeatedly mentioned throughout the review.

In order to provide a nuanced investigation of disease severity in Tercko/ko mice, we added the term “systemic infection” to the figures whenever the mice were divided into groups of mice with and without systemic infection. This is the case for Figure 2A and Supplemental Figure 1C-E. The division into mice with and without systemic infection is also mentioned in the figure legend of Figure 2A in lines 933 to 936 and for Supplemental Figure 1 in lines 1053-1054. We agree that Supplemental Figure 1G is somewhat confusing as the mice with systemic infection are highlighted in this graph but not included as a separate group within our sequencing analysis. We added a sentence to the figure legend clarifying this (lines 1042-1045):

“Nevertheless, the infected Tercko/ko mice were considered one group for the expression analysis and not split into separate groups for the subsequent analysis.”

Additionally, we revised the section regarding this grouping in different degrees of severity in our Material and Methods section to clarify that this division was only performed for specific analysis (line 191):

“…for the indicated analysis.”

Furthermore, the mice which were classified as systemically infected mice were not septic mice, as mentioned above. Those mice were classified by us as systemically infected based on their clinical score and the presence of bacteria in other organs than the lung as stated in the lines 188-191 and 377-382.

Bacteremia is a symptom of very severe cases of hospital-acquired pneumonia with a very high mortality (De la Calle et al., 2016).

Therefore, the systemically infected mice or rather mice with bacteremia display an especially severe pneumonia phenotype, which is distinct from sepsis. The presence of this symptom in our Tercko/ko mice further highlights the clinical relevance of our study. This aspect was added to the manuscript in the lines 569-571.

“The detection of bacteria in extra pulmonary organs is of particular interest, as bacteremia is a symptom of severe pneumonia and is associated with high mortality (De la Calle et al., 2016).”

(4)  The authors conclude that disregulated inflammation and T-cell dysfunction play a major role in S. aureus susceptibility. This may or may not be an important observation, because many KO mice are abnormal for a variety of reasons, and until such reasons are mechanistically dissected, the physiological importance of the observation will remain unclear.

Two points are important here. First, there is no natural counterpart to a Terc-KO, which is a complete loss of a key non-enzymatic component of the telomerase complex starting in utero.

Second, the authors truly did not examine the key basic features of their model, including the features of basic and induced inflammatory and immune responses. This analysis could be done either using model antigens in adjuvants, defined innate immune stimuli (e.g. TLR, RLR, or NLR agonists), or microbial challenge. The only data provided along these lines are the baseline frequencies of total T cells in the spleen of the three groups of mice examined (not statistically significant, Figure 4B). We do not know if the composition of naïve to memory T cell subsets may have been different, and more importantly, we have no data to evaluate whether recruitment of the immune response (including T cells) to the lung upon microbial challenge is similar or different. So, what are the numbers and percentages of T cells and alveolar macrophages in the lung following S. aureus challenge and are they even comparable or are there issues in mobilizing the T cell response to the site of infection? If, for example, Terc-KO mice do not mobilize enough T cells to the lung during infection, that would explain the paucity in many T-cell- associated genes in their transcriptomic set that the authors report. That in turn may not mean dysfunction of T cells but potentially a whole different set of defects in coordinating the response in Terc-KO mice.

We thank the reviewer for highlighting these important aspects. Regarding the first point, indeed there is no naturally occurring deletion of Terc in humans. However, studies reported reduced expression of Terc and Tert in the tissues of aged mice and rats (Tarry-Adkins et al., 2021; Zhang et al., 2018). Terc itself has been found to have several important immunomodulatory functions such as the activation of the NF- κB or PI3-kinase pathway (Liu et al., 2019; Wu et al., 2022). As those aforementioned pathways are relevant for the immune response to S. aureus infections, the authors were interested in exploring the impact of Terc deletion on the pulmonary immune response. The potential immunomodulatory functions of Terc are discussed in lines 106-121. To further clarify our rationale we added a sentence to the introduction in lines 121-125.

“Interestingly, downregulation of Terc and Tert expression in tissues of aged mice and rats has been found (Tarry-Adkins, Aiken, Dearden, Fernandez-Twinn, & Ozanne, 2021; Zhang et al., 2018).

Therefore, as a potential immunomodulatory factor reduced Terc expression could be connected to age- related pathologies.”

Regarding the second point, as we focused on the effect of Terc deletion in the lung and its role in S. aureus infection, we investigated inflammatory and immune response parameters relevant to this setting. For instance, inflammation parameters in the lungs of all three mice cohorts were measured to investigate differences in the inflammatory response in the non-infected and infected mice (Figure 2A). Those measurements showed no baseline difference in key inflammatory parameters between young WT and Tercko/ko mice, which is consistent with previous findings (Kang et al., 2018). The inflammatory response to infection with S. aureus in the Tercko/ko mice cohort differed significantly from the other cohorts (Figure 2A), hinting towards a dysregulated inflammatory response due to Terc deletion. Furthermore, we investigated general immune cell frequencies such as dendritic cells, macrophages, and B cells in the spleen of all three mice cohorts to gather a baseline understanding of the general immune cell populations. In our manuscript only total T cell frequencies were included due to its relevance for our data regarding T cells (Figure 4B). This data could show that there was no difference of total amount of T cells in the spleen of all three mice cohorts. For a more detailed insight into our analysis we added the frequencies of the other immune cell populations analyzed in the spleen as a Supplemental Figure 3B-F. Additionally, a figure legend for the graphs was added.

Therefore, while we did not analyze baseline frequencies of specific populations of T cells, we analyzed and characterized the inflammatory and immune response of our model in a way relevant to our research question.

The differences observed in T cell marker and TCR gene expression was also partly present between the uninfected and infected Tercko/ko mice such as the complete absence of CD247 expression in infected Tercko/ko, which is however expressed in uninfected mice of this cohort (Figure 4A, C and D). Thus, this effect cannot be solely attributed to an inadequate mobilization of T cells to the lung after infectious challenge. However, we agree that a more detailed insight into recruited immune cells to the lung or frequencies of different T cell populations could contribute to a better understanding of the proposed mechanism and would be an interesting experiment to conduct in further studies. We accept this as a limitation of our study and included it in our discussion section in lines 720-724:

“As total CD4+ T cells were analyzed in this study, it would be useful to investigate specific T cell populations such as memory and effector T cells to elucidate the potential mechanism leading to T cell dysfunctionality in further detail. Additionally, analysis of differences in immune cell recruitment to the lungs between young WT and Tercko/ko mice would be relevant.”

(5)  Related to that, immunological analysis is also inadequate. First, the authors pull signatures from the total lung tissue, which is both imprecise and potentially skewed by differences, not in gene expression but in types of cells present and/or their abundance, a feature known to be affected by aging and perhaps by Terc deficiency during infection. Second, to draw any conclusions about immune responses, the authors would have to track antigen-specific T cells, which is possible for a wide range of microbial pathogens using peptide-MHC multimers. This would allow highly precise analysis of phenomena the authors are trying to conclude about. Moreover, it would allow them to confirm their gene expression data in populations of physiological interest

We thank the reviewer for highlighting this important and relevant point. In our study, we aimed to investigate the role of Terc expression in modulating inflammation and the immune response to S. aureus infection in the lung. To address this, we examined the overall impact of age, genotype, and infection on lung inflammation and gene expression. Therefore, sequencing of total lung tissue was essential for addressing the research question posed. Our findings demonstrate that Tercko/ko mice exhibit a more severe phenotype following S. aureus infection, characterized by an increased bacterial load and heightened lung inflammation (Figures 1 and 2). Furthermore, our data suggest that Terc plays a role in regulating inflammation through activation of the NLRP3 inflammasome, along with the dysregulation of several T cell marker genes (Figures 2, 4, and 5). However, this study lacks a detailed analysis of distinct T cell populations, including antigen-specific T cells, as noted earlier. Investigating these aspects in future studies would be valuable to validate and expand upon our findings. We have incorporated these suggestions into the discussion section (lines 720-724)

“As total CD4+ T cells were analyzed in this study, it would be useful to investigate specific T cell populations such as memory and effector T cells to elucidate the potential mechanism leading to T cell dysfunctionality in further detail. Additionally, analysis of differences in immune cell recruitment to the lungs between young WT and Tercko/ko mice would be relevant.”

Nevertheless, our study provides first evidence of a potential connection between T cell functionality and Terc expression.

Third, the authors co-incubate AM and T cells with S. aureus. There is no information here about the phenotype of T cells used. Were they naïve, and how many S. aureus-specific T cells did they contain? Or were they a mix of different cell types, which we know will change with aging (fewer naïve and many more memory cells of different flavors), and maybe even with a Terc-KO? Naïve T cells do not interact with AM; only effector and memory cells would be able to do so, once they have been primed by contact with dendritic cells bringing antigen into the lymphoid tissues, so it is unclear what the authors are modeling here. Mature primed effector T cells would go to the lung and would interact with AM, but it is almost certain that the authors did not generate these cells for their experiment (or at least nothing like that was described in the methods or the text).

Thank you for bringing up this important question. For the co-cultivation experiment of T cells and alveolar macrophages, total CD4+ T cells of both young WT and Tercko/ko were used. We did not select for a specific population of T cells. Our sequencing data indicated the complete downregulation of CD247 expression, which is an important part of the T cell receptor, in the lungs of infected Tercko/ko mice (Figure 4A, C and D). Given that this factor is downregulated under chronic inflammatory conditions, we investigated the impact of the inflammatory response in alveolar macrophages on the expression of various T cell-derived cytokines, as well as CD247 expression (Figure 5D, E) (Dexiu et al., 2022). This aspect is also highlighted in the discussion in lines 623-637. Therefore, a co-cultivation model of T cells and alveolar macrophages was established and confronted with heat-killed S. aureus to elicit an inflammatory response of the macrophages. To emphasize this purpose, we have revised our statement about the model setup in lines 517-519 of the manuscript:

“An overactive inflammatory response could be a potential explanation for the dysregulated TCR signaling.”

The authors hope this will clarify the intent behind the model setup.

(6)  Overall, the authors began to address the role of Terc in bacterial susceptibility, but to what extent that specifically involves inflammation and macrophages, T cell immunity, or aging remains unclear at present.

We thank the reviewer for the helpful and relevant comments. The authors accept the limitations of the presented study such as the reduced number of Tercko/ko mice and the limitations of murine models for S. aureus infection itself and discuss those in the discussion section in the lines 559-561; 577-583; 690-692 and 720-726. However, we hope that our responses have provided sufficient evidence to convince the reviewer that our data supports a clear role for Terc expression in regulating the immune response to bacterial infections, particularly with respect to inflammation and its potential connection to T cell functionality.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:<br /> I really enjoyed this manuscript from Torsekar et al on "Contrasting responses to aridity by

different-sized decomposers cause similar decomposition rates across a precipitation gradient". The authors aimed to examine how climate interacts with decomposers of different size categories to influence litter decomposition. They proposed a new hypothesis: "The opposing climatic dependencies of macrofauna and that of microorganisms and mesofauna should lead to similar overall decomposition rates across precipitation gradients".

This study emphasizes the importance as well as the contribution of different groups of organisms (micro, meso, macro, and whole community) across different seasons (summer with the following characteristics: hot with no precipitation, and winter with the following characteristics: cooler and wetter winter) along a precipitation gradient. The authors made use of 1050 litter baskets with different mesh sizes to capture decomposers contribution. They proposed a new hypothesis that was aiming to understand the "dryland decomposition conundrum". They combined their decomposition experiment with the sampling of decomposers by using pittfall traps across both experiment seasons. This study was carried out in Israel and based on a single litter species that is native to all seven sites. The authors found that microorganism contribution dominated in winter while macrofauna decomposition dominated the overall decomposition in summer. These seasonality differences combined with the differences in different decomposers groups fluctuation along precipitation resulted in similar overall decomposition rates across sites.<br /> I believe this manuscript has a potential to advance our knowledge on litter decomposition.

Strengths:

Well design study with combination of different approaches (methods) and consideration of seasonality to generalize pattern.

The study expands to current understanding of litter decomposition and interaction between factors affecting the process (here climate and decomposers).

Weaknesses:

The study was only based on a single litter species.

We now discuss the advantages and limitations of this approach in the methods and devote a completely new paragraph to this important point in the discussion (lines 394-401).

Reviewer #2 (Public Review):

Summary: Torsekar et al. use a leaf litter decomposition experiment across seasons, and in an aridity gradient, to provide a careful test of the role of different-sized soil invertebrates in shaping the rates of leaf litter decomposition. The authors found that large-sized invertebrates are more active in the summer and small-sized invertebrates in the winter. The summed effects of all invets then translated into similar levels of decomposition across seasons. The system breaks down in hyper-arid sites.

Strengths: This is a well-written manuscript that provides a complete statistical analysis of a nice dataset. The authors provide a complete discussion of their results in the current literature.

Weaknesses:

I have only three minor comments. Please standardize the color across ALL figures (use the same color always for the same thing, and be friendly to color-blind people).

Thank you for this important suggestion. We have now changed all figures to standardize all colors and chose a more color-blind friendly pallete.

Fig 1 may benefit from separating the orange line (micro and meso) into two lines that reflect your experimental setup and results. I would mention the dryland decomposition conundrum earlier in the Introduction.

We based our novel hypotheses on a thorough literature search. Accordingly, decomposition is expected to be positively associated with moisture, regardless of the decomposer body size. Our contribution to theory was to suggest that macro-detritivores may respond very differently to climatic conditions and dominate litter decomposition in warm arid-lands (we listed the reasons in the text). Consequently, we did not distinguish between microorganisms and mesofauna. We assumed that both groups inhabit the litter substrate and have limited adaptation to dry conditions. Our results provide strong evidence that this presumption is likely wrong and that mesofauna respond to climate very differently from micro-decomposers. Yet, we cannot use hindsight understanding to improve our original hypothesis. We now emphasize this important point at the discussion as important future direction. 

Although we are very appreciative and pleased with the reviewer enthusiasm to highlight the importance of our work as a possible solution to the longstanding dryland decomposition conundrum, we decided not to move it to the introduction. This is because we think that our work is not centred on resolving the DDC but provides more general principles that may lead to a paradigm shift in the way ecologists study nutrient cycling across ecosystems.

And the manuscript is full of minor grammatical errors. Some careful reading and fixing of all these minor mistakes here and there would be needed.

We apologize and did our best to find and fix those mistakes

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I really enjoyed this manuscript from Torsekar et al on "Contrasting responses to aridity by different-sized decomposers cause similar decomposition rates across a precipitation gradient". The authors aimed to examine how climate interacts with decomposers of different size categories to influence litter decomposition. They proposed a new hypothesis: "The opposing climatic dependencies of macrofauna and that of microorganisms and mesofauna should lead to similar overall decomposition rates across precipitation gradients".

This study emphasizes the importance as well as the contribution of different groups of organisms (micro, meso, macro, and whole community) across different seasons (summer with the following characteristics: hot with no precipitation, and winter with the following characteristics: cooler and wetter winter) along a precipitation gradient. The authors made use of 1050 litter baskets with different mesh sizes to capture decomposers contribution. They proposed a new hypothesis that was aiming to understand the "dryland decomposition conundrum". They combined their decomposition experiment with the sampling of decomposers by using pitfall traps across both experiment seasons. This study was carried out in Israel and based on a single litter species that is native to all seven sites. The authors found that microorganism contribution dominated in winter while macrofauna decomposition dominated the overall decomposition in summer. These seasonality differences combined with the differences in different decomposers groups fluctuation along precipitation resulted in similar overall decomposition rates across sites.

I believe this manuscript has the potential to advance our knowledge on litter decomposition. Below i provide my general and specific comments.

General comments:

(1) Study in general is well designed and well thought beforehand,

(2) Study aims to expand the current understanding of the dryland decomposition conundrum

(3) The should put a caveat to the fact they only use one litter species and call for examining litter mixture in the same gradient.

(4) Please check the way you reduce the random effects from your initial model, I have provided a better way to do so in my specific comments

(5) For Figure 1, authors can check my comment on this and see if they could revise the figure.

Thank you for the positive feedback and your valuable comments. We have tried to best address all comments and suggestions for improvement and clarification

Specific comments

Line # 57 Please write "Theory suggests" instead of "Theory suggest"

We changed the text as suggested

Line # 70, please write "Indeed, handful evidence shows" instead of "Indeed, handful evidence show"

We changed the text as suggested

Figure 1: I like this conceptual framework. I have a silly question, why is it that the slopes of the whole community at the beginning (between Hyperarid and Arid) is the same as the Macro fauna, I would think the slope should be higher as this is adding up right? and also the same goes for the decomposition of whole community later on. For me this should reflect the adding or summing up (if i am right) then the authors should think about how this could be reflected in the figure.

We agree with your interpretation that the whole community decomposition reflects the addition by constituent decomposers. The slope of the whole community decomposition between hyper-arid and arid is slightly higher than the one of macro decomposition to reflect the additive effect of macro with meso+micro decomposition. We have now changed the figure slightly to make this point more visible (Line 106).

Line # 111 Please make "Methods" bold as well to be consistent with others headings.

We changed the formatting as suggested

Line #125 and in other lines as well please replace "X" by "x" to denote multiplication.

We changed the formatting as suggested

Table 1 Please add "*" to climate like this "Climate*" so that the end note of the table could make sense

Thank you for this suggestion. We have now added the asterisk referring to the note below the Table.

Figure 2, please consider putting at line #133, mean annual precipitation (MAP), as such for line # 135 You can directly says The precipitation map ....

We made both changes as suggested.

Line # 138 I would not use the different units for the same values. I do understand that you want to emphasize the accuracy but i would write instead 3 +- 0.001 g

We changed the units as suggested.

Line # 145, how is the litter basket customized to rest at 1 cm above ground level?

We have now clarified –that we cut-open windows one centimeter above the cage floor. The cages were positioned on the soil (line 144).

Lines # 181-183, I like the approach of checking the necessity of having the random effects. However, it has been reported that likelihood ratio test (LRT) are not really reliable to test for random effects. I will suggest you rather use permutations instead. I think the function is confint(MODEL) you need to specify the number of permutation the higher the better but you should start with 99 first and see how the results look like if promising then you can even go to 9999. But it will need computation power and and time.

Thank you for the suggestion. We now used a simulation-based exact test, instead of a LRT, to examine the random effect, as recommended by the authors from the “lme4” package. As recommended, we used 9999 simulations. The simulation test yielded a similar result to those originally reported (see lines 181-183).

Line # 187, 188, 188, please do not use capital letter to start mesofauna, macrofauna and whole-community

We changed the formatting as suggested

Line # 205 Please add the version number of R in the text.

We now included the version number as suggested.

Line # 209-211, could you please check whether "then" is the word you want to use or "than"

Our bad- we indeed meant “than” and have made the appropriate changes.

Line # 227 and in other places as well please provide the second degree of freedom of the F test.

Thank you for this important comment. We have now added the second degree of freedom to the relevant results (lines 229, 232).

Figure 3 and Figure 4 show some results that are negative, can you please explain what might be the reasons behind this?

We now explain this important point in the figures’ captions.

Figure 5 Please add label to the x-axis.

Thank you-we have now included a label.

Line # 357, the sentence "... meso-decomposition, like microbial decomposition,...", I don't understand which criteria authors used to classify microbial decomposition as "meso-decomposition"?

We now remove this potential cause of confusion by using the term ‘meso-decomposition’ to distinguish from microbial decomposition (Line 366).

Line # 380 Kindly put "per se" in italic.

We changed the formatting as suggested

References

The references format are not consistent. For example for the same journal (say Trends in Ecology and Evolution) the authors sometimes wrote the full name like at line # 36 (and also realize that "vol" should not be written as such) but wrote the abbreviations at line #42

Our bad- we apologize and carefully checked all references to make sure the style is consistent.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Strengths: 

Overall the work is novel and moves the field of Alzheimer's disease forward in a significant way. The manuscript reports a novel concept of aberrant activity in VIP interneurons during the early stages of AD thus contributing to dysfunctions of the CA1 microcircuit. This results in the enhancement of the inhibitory tone on the primary cells of CA1. Thus, the disinhibition by VIP interneurons of Principal Cells is dampened. The manuscript was skillfully composed, and the study was of strong scientific rigor featuring well-designed experiments. Necessary controls were present. Both sexes were included.

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

Limitations:

(1) The authors attributed aberrant circuit activity to the accumulation of "Abeta intracellularly" inside IS-3 cells. That is problematic. 6E10 antibody recognizes amyloid plaques in addition to Amyloid Precursor Protein (APP) as well as the C99 fragment. There are no plaques at the ages 3xTg mice were examined. Thus, the staining shown in Figure 1a is of APP/C99 inside neurons, not abeta accumulations in neurons. At the ages of 3-6 months, 3xTg starts producing abeta oligomers and potentially tau oligomers as well (Takeda et al., 2013 PMID: 23640054; Takeda et al., 2015 PMID: 26458742 and others). Emerging literature suggests that abeta and tau oligomers disrupt circuit function. Thus, a more likely explanation of abeta and tau oligomers disrupting the activity of VIP neurons is plausible.

The Reviewer correctly points out that 3xTg-AD mice typically do not exhibit plaques before 6 months of age, with limited amounts even up to 12 months, particularly in the hippocampus. To the best of our knowledge, the 6E10 antibody binds to an epitope in APP (682-687) that is also present in the Abeta (3-8) peptide. Consequently, 6E10 detects full-length APP, α-APP (soluble alpha-secretase-cleaved APP), and Abeta (LaFerla et al., 2007). Nonetheless, we concur with the Reviewer's observation that the detected signal includes Abeta oligomers and the C99 fragment, which is currently considered an early marker of AD pathology (Takasugi et al., 2023; Tanuma et al., 2023). Studies have demonstrated intracellular accumulation of C99 in 3-month-old 3xTg mice (Lauritzen et al., 2012), and its binding to the Kv7 potassium channel family, which results in inhibiting their activity (Manville and Abbott, 2021). If a similar mechanism operates in IS-3 cells, it could explain the changes in their firing properties observed in our study. Consequently, we have revised the manuscript to include this crucial information in both the Results and Discussion sections.

(2) Authors suggest that their animals do not exhibit loss of synaptic connections and show Figure 3d in support of that suggestion. However, imaging with confocal microscopy of 70micron thick sections would not allow the resolution of pre- and post-synaptic terminals. More sensitive measures such as electron microscopy or array tomography are the appropriate techniques to pursue. It is important for the authors to either remove that data from the manuscript or address the limitations of their technique in the discussion section. There is a possibility of loss of synaptic connections in their mouse model at the ages examined.

We appreciate the Reviewer’s perspective on the techniques used for imaging synaptic connections. While we acknowledge the limitations of confocal microscopy for resolving pre- and post-synaptic structures in thick sections, we respectfully disagree regarding the exclusive suitability of electron microscopy (EM). Our approach involved confocal 3D image acquisition using a 63x objective at 0.2 um lateral resolution and 0.25 Z-step, providing valuable quantitative insights into synaptic bouton density. Despite the challenges posed by thick sections, this method together with automatic analysis allows for careful quantification. Although EM offers unparalleled resolution, it presents challenges in quantification. We have included the important details regarding image acquisition and analysis in the revised manuscript.

Reviewer #2 (Public Review):

Summary:

The submitted manuscript by Michaud and Francavilla et al., is a very interesting study describing early disruptions in the disinhibitory modulation exerted by VIP+ interneurons in CA1, in a triple transgenic model of Alzheimer's disease. They provide a comprehensive analysis at the cellular, synaptic, network, and behavioral level on how these changes correlate and might be related to behavioral impairments during these early stages of the disease.

Main findings:

- 3xTg mice show early Aß accumulation in VIP-positive interneurons.

- 3xTg mice show deficits in a spatially modified version of the novel object recognition test. - 3xTg mice VIP cells present slower action potentials and diminished firing frequency upon current injection.

- 3xTg mice show diminished spontaneous IPSC frequency with slower kinetics in Oriens / Alveus interneurons.

- 3xTg mice show increased O/A interneuron activity during specific behavioral conditions. - 3xTg mice show decreased pyramidal cell activity during specific behavioral conditions.

Strengths:

This study is very important for understanding the pathophysiology of Alzheimer´s disease and the crucial role of interneurons in the hippocampus in healthy and pathological conditions.

We are thankful to the reviewer for their insightful recognition of our efforts and their enthusiasm for the results of this research.

Weaknesses:

Although results nicely suggest that deficits in VIP physiological properties are related to the differences in network activity, there is no demonstration of causality.

We completely agree with the reviewer's observation regarding the lack of demonstration of causality in our results. Investigating causality in the relationship between deficits in VIP physiological properties and differences in network activity is indeed a crucial aspect of this project. However, achieving this goal will require a significant amount of time and dedicated manipulations in a new mouse model (VIP-Cre-3xTg). We appreciate the importance of this line of investigation and consider it as a priority for our future research endeavors.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Limitations:

(1) The authors should describe their model and state the age at which these mice start depositing amyloid plaques and neurofibrillary tangles. Readers might not be familiar with this model. It is also important to mention that circuit disruptions are assessed prior to plaque and tangle formation.

We have included a detailed description of the 3xTg-AD mouse model in the Introduction section, including information on the age at which amyloid plaques and neurofibrillary tangles begin to appear. Additionally, we have clarified that circuit disruptions were assessed before the formation of plaques and tangles. These details have been added to both the Introduction and the Results sections to ensure clarity for readers unfamiliar with the model.

(2) Ns are presented in Supplemental Table 1. Units are presented in a note to Supplementary Table 1. It would be advisable to specify Ns and units as the data is being presented in the results section or figure legends for easy access.

We have now included the Ns (sample sizes), specifying the number of cells or sections and the number of experimental animals, directly within the Results section and in the figure legends. This ensures that readers have immediate access to this information without needing to refer to the supplementary materials.

(3) Several typos require correction:

a. "mamory" - Line 22, page 5.

b. The term "Interneurons" is abbreviated as both "INs" and "IN" throughout the manuscript. The author should consistently choose one abbreviation.

We have corrected the typo "mamory" to "memory" on line 22, page 5. Additionally, we have standardized the abbreviation for "Interneurons" to "INs" throughout the manuscript for consistency.

(4) Note 2 in Supplementary Table 1 states that animals of both sexes with equal distribution were used throughout the study. It would be best for the reader to assess the data distribution based on sex. Thus, it is advisable for the authors to depict male and female data points as distinct symbols throughout the figures.

Unfortunately, we do not have detailed sex-disaggregated data for all datasets, which limits our ability to depict male and female data points separately across all figures. Therefore, we have opted to pool data from both sexes for a more comprehensive analysis. We believe this approach maintains the robustness of our findings.

Reviewer #2 (Recommendations for the authors):

Major Points:

- To keep the logical line of reasoning and to be able to interpret the results, it would be important to use the same metrics when comparing the population activity of O/A interneurons and principal cells in the different behavioral conditions.

We have revised Figures 4 and 5 to enhance the coherence in data presentation. This includes using consistent metrics for comparing the population activity of both O/A interneurons and principal cells across different behavioral conditions. These changes ensure a clearer and more logical interpretation of the results.

- Although results nicely suggest that deficits in VIP physiological properties are related to the differences in network activity, there is no demonstration of causality. Would it be possible to test if manipulating VIP neurons one could obtain such specific results? Alternatively, it could be discussed more in detail how the decrease in disinhibition could lead to the changes in network activity demonstrated here.

We agree with the reviewer that establishing causality between VIP neuron deficits and changes in network activity would be very important. However, demonstrating causality would require a new line of investigation, involving the use of specific mouse models to selectively manipulate VIP neurons. This is an exciting direction that we plan to prioritize in our future research. For this study, we have included a discussion on the potential mechanisms by which decreased disinhibition might lead to the observed changes in network activity. Specifically, we propose that in young adult 3xTg-AD mice, the altered firing of I-S3 cells may lead to enhanced inhibition of principal cells. This could shift the excitation/inhibition balance, input integration and firing output of principal cells thereby impacting overall network activity. These points are discussed in detail in the revised Discussion section.

- On the same lines the correlations showed in the manuscript, would be more robust if there was an in vivo demonstration that 3xTg mice indeed show decreased activity in vivo. The same experiments could also clarify if VIP cells in control animals are more active at the time of decision-making and during object exploration as suggested in the manuscript.

Thank you for your comment. In response to the point raised, we would like to highlight that we have recently documented the increased activity of VIP-INs in the D-zone of the T-maze and during object exploration in a study published in Cell Reports (Tamboli et al., 2024). This publication is now referenced in our manuscript to support our findings. Regarding the in vivo activity of 3xTg mice, our observations indicated no significant differences in major behavioral patterns such as locomotion, rearing, and exploration of the T-maze when comparing Tg and non-Tg mice. These findings are presented in detail in Figure 4c and Supplementary Fig. 5. We believe these data support the robustness of our correlations by demonstrating that the overall behavioral activity of 3xTg mice is comparable to that of non-transgenic controls, thus focusing attention on the specific roles of VIP-INs in early prodromal state of AD pathology.

Minor Points:

- Figure 1c: Heading of VIP-Tg should have capital letters.

Thank you for pointing that out. We have corrected the heading to "VIP-Tg" with capital letters in Figure 1c.

- Figure 1d: The finding that no change was observed in the percentage of VIP+/CR+ is based on three animals and 3-4 slices per mouse. However, the result of VIP+CR+ in tg-mice has an outlier that might bias the results. I would suggest increasing the number of animals to confirm these results.

Thank you for your insightful suggestion. We addressed the potential impact of the outlier in the VIP+/CR+ cell density analysis by recalculating the results after removing the outlier using the interquartile range method. This reanalysis revealed a statistically significant difference in the VIP+/CR+ cell density between non-Tg and Tg mice, which we have now detailed in the Results section. Despite this, we have chosen to retain the outlier in our final presentation to accurately represent the biological variability observed in our sample. We agree that increasing the number of animals would further validate these findings and will consider this in future studies.

- Figure 3d: Would it be possible to identify the recorded interneurons? Is it expected that most of those are OLM cells?

Thank you for your question. We were unable to fully recover all recorded cells using biocytin staining. However, for those cells with preserved axonal structures, we identified both OLM and bistratified cells, which are the primary targets of I-S3 cells. We have now included this information in the Results section to clarify the types of interneurons identified.

- Figure 3: Why quantify VGat terminals instead of quantification of VIP-GFP terminals? Combined with the Calretinine labeling it would be more useful to indicate that no changes were observed at the morphological bouton level specifically in disinhibitory interneurons. Please also describe which imageJ plugin was used for the quantification.

Thank you for your question. Our primary objective was to quantify the synaptic terminals of CR+ INs in the CA1 O/A region, which are predominantly formed by I-S3 cells. Therefore, VGaT and CR co-localization was used to guide this analysis. GFP expression in axonal boutons can sometimes be inconsistent and less reliable for precise quantification. For this analysis, we utilized the “Analyze Particles” function in ImageJ, combined with watershed segmentation, which is now specified in the Methods section.

-  Figure 4g: How was the statistical test performed? If data was averaged across mice, please add error bars and data points in the figure.

Thank you for your question. To compare the alternation percentage between non-Tg and Tg mice, we used Fisher’s Exact test as detailed in Supplementary Table 1. In this analysis, we considered each animal's choice individually, comparing the preference for correct versus incorrect choices between the two groups. Since Fisher’s Exact test is designed for analyzing qualitative data rather than quantitative data, averaging across mice was not applicable, and therefore, we did not include error bars or data points in the figure.

- Figure 4h: To conclude that the increase in activity is larger in the 3xTg mice, there should be a statistical comparison for the magnitude of change between the decision and the stem zone for control and 3xTg mice. To show that there is no significant difference in this measurement in the control mice is insufficient.

Thank you for your suggestion. We performed a statistical comparison of the magnitude of change in activity between the stem zone and the D-zone for non-Tg and 3xTg mice, as recommended. Our analysis showed no significant difference in this magnitude of change between the two genotypes. These results have now been included in the Results section. However, we would like to highlight an important finding regarding the nature of these changes. In the 3xTg mice, there was a consistent increase in the activity of O/A INs when entering the Dzone. In contrast, non-Tg mice displayed a range of responses, including both increases and decreases in activity. This indicates a higher reliability in the firing of O/A INs in the D-zone of 3xTg mice. Our recent study suggests that VIP-INs are particularly active in the D-zone (Tamboli et al., 2024). Therefore, the absence or reduced input from VIP-INs in 3xTg mice may lead to the observed higher engagement of O/A INs in this zone. We believe this observation is crucial for understanding the differential yet nuanced changes in neural dynamics in these mice.

- In the methods, it is stated that there was a pre-selection of animals depending on learning performance. Would it be possible to also show the data from animals that did not properly learn? Alternatively, it would be useful to plot the correlation between performance in this test and the difference between activity in the stem and the decision-making zone. The reason to ask for this is that there is a trend for control animals to show reduced alternations (50 vs 80%, although not significant, it is a big difference). Considering that there is also a trend in control animals to show increased activity in the decision-making zone, it would be important to confirm that this is not only due to differences in performance. The current statistical procedure does not allow discarding this.

In this study, we excluded from the analysis the animals that refused to explore the T-maze and spent all their time in the stem corner, or refused to explore the objects and stayed in the open field maze (OFM) corner. These exclusions applied to both non-Tg (n = 6) and Tg (n = 5) groups, indicating that low exploratory activity is not necessarily linked to AD-related mutations. During the T-maze test, we also observed several animals that made incorrect choices (4 out of 9 non-Tg and 1 out of 6 Tg mice). However, due to the low number of animals making incorrect choices, we were unable to form a separate group for analysis based on incorrect choices. These details are now provided in the Methods section.

- Figure 4i. It is not clear when exactly cell activity was measured. If it was during the entire recording time, I think it would be interesting to see if the activity of O/A interneurons is different specifically during interaction with the object in 3xTg mice.

Cell activity was indeed measured throughout the entire recording session and analyzed in relation to animal behavior (immobility to walking; Fig. 4d,e), and periods specifically related to interaction with objects were extracted for analysis (Figure 4i).

- Why was the object modulation measured during a different task in which both objects were the same? The figure is misleading in that sense, as it suggests the experiment was the same as for the other panels with two different objects. It would be important to correct this if the authors want to correlate the deficits in NOR in 3xTg mice and changes in IN activity.

The study specifically investigated object-modulated neural activity during the Sampling phase. Therefore, two identical objects were placed in the arena for animal exploration. As mentioned above, due to several animals failing to explore the OFM and objects on the second day, they were excluded from the analysis, preventing the conduct of the novel-object exploration Test Trial. Both non-Tg and Tg mice showed a lack of exploration in the OFM and Tmaze, for reasons that remain unclear. Consequently, we opted to present robust data on neural activity during the initial sampling of two identical objects. However, further investigation is needed to understand how this activity relates to deficits observed in the classical NOR test.

- Figure. 5c-f. I would strongly suggest performing the same quantification and displaying similar figures for the fiber photometry experiments in interneurons and principal cells. It would help to interpret the data.

We have taken the reviewer's suggestion into account and standardized the data analysis and presentation. Figures 4d, e and 5c, d now depict the walk-induced activity in INs and PCs, respectively. Figures 4h and 5f compare activity between the stem and D-zone in the T-maze. Additionally, Figures 4j and 5h illustrate the object modulation of INs and PCs, respectively.

- Although velocity and mobility were quantified, it would be important to show also that they are not different during those times when activity was dissimilar, as in the decision zone.

We have analyzed these data and found no significant differences between the two genotypes in terms of velocity and mobility during these periods. This analysis is now presented in Supplementary Figure 5e, f and detailed in the Results section.

- Figure 5g-h. Similarly, I would suggest using the same metrics in order to correlate the results from interneuron and principal cell activity photometry.

We have updated this figure to align with the presentation of interneurons (Figure 4j) and included RMS analysis to emphasize lower variance in object modulation of PCs as an indicator of increased network inhibition.

- Was object modulation variance also different for INs depending on the mouse phenotype?

We conducted this additional analysis but did not find any significant difference.

- Figure S4: would it be possible to identify the postsynaptic partners?

As mentioned above, for those cells with preserved axonal structures, we identified both OLM and bistratified cells. We have now included this information in the Results section to clarify the types of interneurons identified.