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Referee #3

Evidence, reproducibility and clarity

Recommendation: Publish after revisions

Duart and colleagues have put forth a manuscript detailing the under-appreciated effect of intrahelical salt bridge formation to the insertion transmembrane helices. Utilizing an in vitro and in vivo applicable construct of vehicle protein leader peptidase (Lep) from Escherichia coli, the authors were able to use glycosylation patterns as a way to quantify the apparent free energy of membrane insertion for multiple transmembrane helices. These results have demonstrated the importance of taking salt bridge formation into account when developing membrane protein prediction tools; however, prior to publication, further analyses would be beneficial for supporting their quantitative conclusions.

Major Comments:

• It would be helpful if the authors detailed their process in deciding which of the 136 potential salt bridge-containing helices were chosen for further investigations.
• Considering the data presented in Fig. 3c, it may be useful to also include charged pair mutations in the i, i+3 positions in the analyses of helix G and helix A, as these positions are the most likely to form salt bridges. This would act as a useful positive control, to see if the mutations would improve the insertion of the sequence.
• Page 14, Line 255: Authors state "The salt bridge contributes approximately ~0.5 kcal/mol to the apparent experimental free energy of membrane insertion." Can this change in apparent free energy be attributed completely to the mutation? Are there any potential interactions between the inserted helix and the natural H2 transmembrane sequence of Lep that could be changing with the various mutations?
• It is promising to see these results in the context of the Lep protein, but the authors should consider the effect these salt bridges may have in the context of the full protein. Creating mutants of Halorhodopsin or calcium ATPase would determine the impact of potential salt bridge disruption on protein folding, which would provide some context on the functional consequences of these mutations.
• Authors have presented a strong argument for the inclusion of potential salt bridge formation in the prediction of transmembrane helices; however, they have not detailed the necessary steps for developing a new system. It would be encouraging to see recommendations on the next steps towards better prediction software.

Minor comments:

• Page 8, Line 118: Authors state "Our results showed a tendency to better insertion when charge pairs were placed in positions (i, i+1; i, i+3; i, i+4) that are permissive with salt bridge formation (Fig. 1c), actually an effect not observed in the predictions (Fig. 1b)." It is important to clarify that this "better" insertion in Fig. 1c is compared to each respective predicted value in Fig. 1b. Currently, it reads as if the authors are suggesting the introduction of the charged pair residues is helping the insertion of the unaltered L4/A15 sequence.
• Figure 1a: Add cytoplasmic and lumen identifiers for clarity.
• Figure 3b: Slashes for "Opp charge" and "Same charge" in the legend appear to be reversed according to the values presented in Table 2.

Significance

This paper increases our understanding of salt bridges in membrane protein structure and function, as performed systematically by a lab with major expertise in this research area.

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Referee #2

Evidence, reproducibility and clarity

As the title states, Duart et al. have examined the energetic cost of the translocon-assisted insertion of TM helices containing salt bridges into membranes. The paper has three parts: (1) model studies using the methods of Hessa et al. (12,13), (2) statistical analysis of salt bridges in membrane proteins of known 3D structure, and (3) Hessa et al. measurements of selected i,i+4 salt-bridge containing TM helices from halorhodopsin (PDB ID = 3QBG) and calcium ATPase (1SU4). The major overall conclusion is that for i,i+4 salt bridges yield a more favorable insertion free energy of about 0.5 to 0.7 kcal/mol.

The subject of the paper is broadly interesting, but it suffers from several problems that must be addressed before it can be considered seriously for publication. The comments below are described in terms of the three parts.

(1) Figure 1b reports tabular values of predicted Hessa et al. DG values for sequences that contain K, D, or K & D substitutions in a parent L4A15 parent sequence, which has a favorable DG of about -0.5 kcal/mol. For all of the other sequences, DG is predicted to be unfavorable 1.4 kcal/mol to 3.5 kcal/mol. Figure 1c presents triplicate experimental measurements of DG for the sequences in Figure 1b shown as bar graphs. All of the sequences yield unfavorable DG values of about +0.2 kcal/mol except for the parent sequence that has a favorable value close to the predicted value.

There are several problems with these data and their presentation. Fig. 1b should also include the measured DGs with standard deviations in addition to the predicted values. In Fig. 1c, the positive values are plotted on different scale than the sole negative value. This causes the authors to insert a break in the bar representing the sole negative value. The bars are color coded in a mysterious way that is not clearly described in the figure legend. In any case, the measured DG values are all about the same.

A fundamental problem with the measurements is that the method of Hessa et al (12) should have been adhered to rigidly. As those authors noted "The quantification [of DG values]is maximally sensitive for H-segments with DGapp values close to zero (p < 0.5 in Fig. 1d); therefore, for each kind of residue we balanced the contribution from the central residue by varying the number of Leu residues until an H-segment with DG in the range -1.2 to 1.2 kcal/mol was found." The measurements reported Fig. 1b and 1c are far outside the maximum sensitivity range. The Western blots upon which the numbers are based should have been included (perhaps as an appendix).

(2) The statical analysis seems fine and is useful.

(3) Fig.4, halorhodopsin helix G measurements. The table of Fig. 4a should be expanded to include both in vitro (panel e) and in vivo data (panel f). It is not entirely clear where the values given in the table are from, but presumably from the in vitro data (panel e). Fig. 5, calcium ATPase helix A. Comments similar to those regarding Fig. 4 apply. The division of the long helix into a short greasy one and longer one carrying more charges is interesting, but it seems to add little to the main intent of the paper to assess the thermodynamic properties of helices containing salt-bridges.

Overall, the paper would be stronger if it focused mostly on the part (1) experiments to arrive at definitive answer to the energetics of salt-bridge insertion. As it stands, it is a smash up of ideas and experiments.

Significance

Surprisingly,there have been no reported measurements that I am aware that examine the energetic cost of inserting TM helices containing salt bridge into membranes. This paper is a start in that direction.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the manuscript „Intra-helical salt bridge contribution to membrane protein insertion" the authors investigate the effect of salt bridge formation between positively and negatively charged amino acids on the insertion behavior of α-helical protein segments into the membrane. Generally it is believed that polar or even charged residues prevent stable membrane insertion of α-helical protein segments, but some of these authors had already shown in a previous paper that such residues are more frequent than expected in transmembrane helices. In the current study, the authors investigate in detail the role of intra-helical salt bridge formation on stable membrane insertion. Using an in vitro membrane insertion assay based on the E. coli leader peptidase (Lep) protein, they found better membrane insertion for helical segments with opposite charge pairs placed at positions compatible with intra-helical salt bridge formation (positions i→i+1; i→i+3 and i→i+4). Furthermore, the authors performed a database screen which revealed that oppositely charged residues are overrepresented at these positions. Finally they picked two candidate membrane proteins from the database (Halorhodopsin and calcium ATPase 1) and proved the presence of an intra-helical salt bridge and determined the contribution of the salt bridge to the apparent free energy of membrane insertion (ΔGapp), which was in the range of 0,5-0,7 kcal/mol.

Major comments

1. It seems that the data in Fig. 3b has been mixed up, making it difficult to judge the conclusions. The bars with forward slash seem to represent the "same charge" data and the bars with backward slash seem to represent the "opposite charge" data (exactly contrary to the figure legend). In general the forward and backward slash representation is not easily distinguishable, and for the position i+4 both bars contain a forward slash (making it impossible to discriminate same and opposite charge). Please use filled and unfilled bars instead. Furthermore the bar diagram in Fig. 3a is stacked for opposite and same charge, whereas in Fig. 3b the respective bars are placed next to each other. Additionally the label of the y-axis in Fig. 3c is misleading, as it is not the "Frac. of opp. charged pairs" but the fraction of oppositely charged pairs that form salt bridges.
2. The authors don´t give details no how the log odds ratios and the respective p-values have been determined. Please include this in the Materials and Methods section. What does a p-value of 0.00e+00 mean (see Table 2, Spacing: +3, "All Log odds")?
3. What is the proof that for the isolated helix A from the calcium ATPase 1 the membrane embedded part is identical to the full-length protein? The authors investigated two different helix A peptides, the full-length helix ranging from L49-F78, and one short fragment ranging from L49-A69 containing the more hydrophilic N-terminal region, which is the membrane-embedded region in the full-length protein. The authors state: "In contrast, when only the membrane-embedded sequence was included, the Lep chimera was mainly doubly-glycosylated (Fig. 5c, lane 3), suggesting that helix A is properly inserted when the full helical sequence is present." In my opinion this conclusion cannot be drawn from the data presented. The authors used an isolated helical segment, so in my opinion it is much more likely that the isolated full-length helix inserted via its hydrophobic C-terminal part (L60-F78) into the membrane. The authors themselves state in their manuscript: "It has been previously shown that the position in the membrane of TM helices in protein folded structures does not always correspond to the thermodynamically favored positions in the membrane of the isolated helices." Also the i→i+5 mutant points into that direction, because the effect of disturbing the intra-helical salt bridge for the helix A is much less pronounced compared to the similar data in Fig. 4f for the Halorhodopsin protein. In my opinion this shows that most probably only one charged residue (R63) is embedded inside the membrane (with a membrane embedded part of L60-F78).

Minor comments:

1. line 151: ",see Figure 2)" Typo: Bracket missing.
2. line 172: "Other known structural features can also be hinted at, including aromatic ring stacking by His-Trp pair [20] at i→i+6." Please give some more examples of important structural features of membrane proteins, which can be seen in your analysis (e.g. I think that also the glycine zipper can be seen in the i→i+4 data set).
3. line 255: "The salt bridge contributes approximately ~0,5 kcal/mol to the apparent experimental free energy of membrane insertion." Please explain that this value was derived from the comparison of the ΔGexp between the wt and the i→i+5 mutant. Please comment also on the large difference between the predicted (ΔGpred) and the experimental values (ΔGexp), even if no salt-bridge is involved (e.g. for the DD mutant).
4. line 348: "Asp-Lys pairs at position i, i+4 and Glu-Lys pairs at position i→ i+3 are the most prevalent as seen previously in Figure 2. They are both among the most prevalent oppositely charged pairs and the charged pairs that form the highest number of salt bridges in membrane protein structures. This is in stark contrast to Glu-Arg pair at position i→ i+1 that although as frequent in pairs as Asp-Lys and Glu-Lys at positions i→i+4 and i→i+3 respectively, only form salt bridges in one-fourth of the cases." Fig. 2 shows that each charge pair has a different prevalence depending on the order (e.g. Asp-Lys and Lys-Asp pairs). I think for this statement the sum of both prevalences should be taken into account, and as the sum is not easy discernible from Fig. 2, it would help to include a table containing the sums. Furthermore, it would be good to refer also to Fig. 3, which also contains a part of the discussed data.
5. line 402: "c-myc tag (Glu-Gln-Lys-Leu-Ile-Ser-Glu-Glu-Asp-Leu, EQKLISEEDL) was added in Ct in hanging with de PCR primer before cloning." Please revise the sentence and I think the one letter code for the c-myc tag is sufficient (please correct this also in line 428).
6. line 420: "A region's total ΔG is the sum of these individual scores weighted on where in the region the residue, a residue in the middle of the helix has a higher weight than residues at the ends." Please revise the sentence, the meaning is unclear.
7. line 436: "Total protein was quantified and equal amounts of protein submitted to Endo H treatment or mock-treated, followed by SDS-PAGE analysis and transferred into a PVDF transfer membrane (ThermoFisher Scientific)." Please revise the sentence.
8. line 498: "Topological files with sequence and membrane topology are created with the help of the RCSB secondary structure file and only membranes annotated as pure α-helices were retained." I assume that the description contains a typo (membranes annotated as pure α-helices?)
9. line 507: typo "..., but we did not clustered the proteins" 14: line 560: "The individual value of each experiment in represented by a solid dot being represented as a green square the experimental ΔG value for the L4/A15 sequence from [2]." Please revise the sentence. 15: line 562: "The wt and simple mutants are shown in white bars." Typo: single mutants 16: line 563: "Charges at compatible distances with salt bridge formation (i→i+1; i→i+3; and i→i+4) are shown in yellow. Not compatible distances with salt bridge formation (i→i+2; and i→i+5) are shown in dark gray. Compatible distances but not compatible amino acid pair (i, i+4 DD pair) is shown in clear gray." The given colors don´t match with the figure (i→i+1 = brown; i→i+3 = orange; i→i+4 = yellow and i→i+4 DD pair = white) 17: line 597: "The different monomers are shown in transparent blue, purple and indigo." The different colors are hardly distinguishable in the figure. 18: Figure 4a: The table could be simplified. I think the column "charges" can be removed, as it contains not really charges and the names of the peptides already contain the same information. The column "Å" contains only a value for the wt (and not for the DK i,i+5 mutant) and as the distance for the wt is also given in Fig. 4g, this column can be also removed.
10. Fig. 4f: The marker lane is hardly visible (completely dark lane)
11. Fig. 5b: The column "Å" contains only values for the wt sequences (long and short). See also comment 18.
12. Fig 5d: Why is in the SDS gel a mass shift between the wt and the i→i+5 mutant visible, even though the peptide mass is equal.
13. There are several changes of font type or format changes (e.g. line 210-214). Please correct this.

Significance

As a structural biologist with a focus on membrane-proteins, I understand that the study is concerned on intra-helical salt bridges, but the implications of inter-helical salt bridges should also be discussed, at least in the introduction or outlook. The authors propose that their results are important for the improvement of membrane protein topology prediction methods, so for this aim it is also necessary to take any potential inter-helical salt bridges into account. In this context, it would be relevant to point point out that there even exist extended rows of salt bridges between transmembrane segments (charge-zippers), which serve an important structural element in several membrane proteins.

The article is well written and most of the conclusions drawn from the experimental results are convincing. I agree with the authors that their results are relevant for future improvement of membrane protein topology prediction software, which so far does not take the possibility of salt bridge formation into account. Therefore, I recommend publication after clarification/revision of the abovementioned points.

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Reply to the reviewers

We thank the three reviewers for their helpful and valuable comments. We plan to address their criticisms in a revised manuscript and hope that our manuscript will then be significantly improved.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The authors have presented a very interesting and compelling set of data regarding the impact of conditional deletion of the only known pathway allowing the uptake of pyruvate into mitochondria. The paper comprises two interwoven stories that are both important. The first is the remarkable finding that the majority of excitatory neurons in the cortex (i.e. those under the influence of the CaMKII promoter) show remarkable metabolic flexibility as they tolerate elimination of pyruvate oxidation, considered the major supplier of ATP in neurons. The data on this seem clear although the authors did not delve into the potential mechanisms of metabolic compensation that likely occurs. Instead they examined whether there was some mal-adaptive compensation and they found clear evidence of this: in the absence of MPC activity the mice are much more prone to epileptic seizures, unveiled experimentally by relatively standard protocols (kindling). The authors present largely very convincing evidence that this mal-adaptive compensation in turn ends up decreasing the activity of KV7.2/7.3 channels whose job is normally to limit runaway repetitive firing by mediating an hyperpolarizing K+ efflux following an action potential. This channel, put on the map as it was one of the downstream targets modulated by cholinergic metabotropic activation, is also know known to be controlled by Calmodulin and therefore cytosolic Ca levels. Overall, I think at its core this manuscript is interesting and important. There however several weaknesses, I fear, will diminish the impact on the eventual readership. If these points can be addressed, it will strengthen the longevity of these findings:

1) It is puzzling why the authors resorted to using shRNA-mediated KD of MPC1 for some of the in vitro studies when they have gone to the trouble of making a floxed CRE-dependent mouse. Primary cells (e.g. Fig 1) or organotypic cultures (Fig. 6) from these mice would have made a more consistent set of starting conditions to compare data across the manuscript. As there viruses expressing the CRE recombinase are widely available this could have been used on mice simply harboring the floxed gene it they are worried about waiting for the expression of the CaMKII promoter for in-vitro conditions.

This is indeed a good point. Indeed initially, when we started these experiments, we tried to use viruses expressing the CRE recombinase in cultured neurons from mice harboring the floxed gene as proposed by the reviewer. However, for reasons that we do not fully understand, the use of AAVs or lentiviruses expressing the CRE was found to be deleterious for the cultured neurons. In view of this toxicity we tried using TAT-CRE recombinase, a recombinant cell-permeant fusion recombinase, which we added directly to the medium. However, this strategy proved to be poorly efficient. We finally used cultures of Cre-floxed neurons in which we tried to knockout MPC1 gene using 4-hydroxytamoxifen in the culture medium. However, we did not obtain satisfying results because, as previously reported, cortical neurons grow poorly in the presence of 4-hydroxytamoxifen (Nichols et al., Cell Death and Disease, 2018. https://doi.org/10.1038/s41419-018-0607-9). For these reasons we turned to the shRNA strategy and to the use of 3 small molecule inhibitors of the MPC each with different chemical structures. Both the RNA interference and the pharmacological approaches gave similar results, reinforcing our confidence in the specificity of the results, and the unlikelihood of off-target effects.

2) The data in Figure 5 gets a little less convincing as using extracellular glutamate to drive Ca elevations is so non-physiological that the results might really be distorted by the participation of something irrelevant to the story, even though it supports the overall interpretation for a role of Ca/CaM in the control of the channel. Similarly, the use of RU360 should be done with caution. The drug, although a useful antagonist of MCU in purified mitochondria, is famously finicky with respect to its ability to cross membranes and could well have off target impact. A much cleaner experiment would be to suppress the expression of MCU via KD. Presumably in the MPC-deficient neurons, this would have minimal impact on Ca signals. Given the frequent ambiguity associated with interpreting pharmacological results, coupled to the central importance of this finding in interpreting the entire paper, I think carrying out experiments with molecular genetic manipulation of MCU is warranted.

The main point of this figure is to study the capacity of MPC1 KO neurons to handle intracellular calcium increase and to regulate calcium homeostasis. To this end, we used strategies described to acutely increase cytosolic calcium, either through membrane depolarization with KCl (Rienecker et al., ASN Neuro. 2020. https://doi.org/10.1177/1759091420974807) or through activation of glutamate receptors using glutamate (For example see Wong, Vis Neurosci, 1995 : DOI: 10.1017/s0952523800009469). It is important to mention that the concentration of glutamate used in our experiments (10 microM for 2 min) is well below the concentration normally used to induce excitotoxicity (100-500 microM for 30min). The fact that both stimulations provided similar results and clearly indicated a defect in the clearance of cytosolic calcium in MPC-deficent neurons.

Regarding the concern with RU360, we are aware of the problems with plasma membrane permeability associated with this compound, and for this reason we included a membrane permeabilizer (0.02% pluronic acid) to facilitate its entry into the cell. This was indicated in the Material and Methods section (line 585) as well as in the figure legend (line 948). In order to clarify this methodology, we will add this information in the main text. It should be noted that this concern would not apply to the electrophysiogical experiments, since in this case the compound was injected directly into the cell. We would like to add that we chose to inhibit the MCU using a chemical inhibitor rather than a shRNA because of the well known difficulty in obtaining a complete loss of function of the MCU using RNA interference (Nichols et al., Cell Death and Disease, 2018. https://doi.org/10.1038/s41419-018-0607-9). Nevertheless, as recommended by the reviewer, we will attempt to downregulate the expression of MCU using shRNA.

3) The authors have not really made clear in this paper whether the ability to suppress the phenotype of the MPC deficiency with ketones is really related to a providing TCA cycle support or instead a pharmacological impact on non-TCA related targets (such as the Kv7.2/7.3 channels). Presumably the use of other ketones might circumvent this. The action of ketone bodies has been a topic of considerable interest in neuroscience, given the clinical relevance for childhood epilepsies. Previous studies for example have argued for direct inhibition of the vesicular glutamate transporter (Juge et al. Neuron 2010). The use of other ketones (acetoacetate) would narrow down the interpretations of the data.

Our results point to 2 two possible mechanisms of ketone bodies: i) providing acetyl-CoA to the Krebs cycle, thereby stimulating OXPHOS and ii) direct action of 3-beta hydroxybutyrate on the activity of Kv7/7.3 channels. The reviewer is asking whether, in addition to 3-beta hydroxybutyrate, other ketone bodies, acetone or acetoacetate, may display antiepileptic activity, which would probably indicate that providing substrates to the TCA cycle is sufficient to prevent neuron-intrinsic hyperactivity and seizures. We agree that this in an interesting question and we will now test the effect of acetoacetate on PTZ-induced seizures in MPC KO mice.

**other**

1) In vitro - scramble controls only serve to demonstrate there is no general effect of treating cells with shRNAs, but do not address if there is an off-target effect. The most convincing thing here would be to have an shRNA-insensitive variant that rescues.

We have used 2 different shRNAs and 3 chemically unrelated inhibitors of the MPC and in all cases we obtained similar results. Therefore, we think that it is unlikely that the effects we observe are due to an off-target activity. The experiment proposed by the reviewer is interesting but extremely difficult. The idea would be to reintroduce a shRNA-insensitive MPC1 into MPC1-deficient neurons treated with shRNA. This is difficult as it is known that the expression level of MPC1 needs to be matched to that of MPC2, otherwise it leads to depolarization of the mitochondria. Obtaining the right level of MPC1 would be extremely difficult to achieve in practice.

2) Does rescuing CaMK binding to KCNQ channels rescue the phenotypes?

The question raised by the Reviewer implies that CaM is not constitutively bound to KCNQ channels, which is a matter of debate. As we pointed out in the discussion, ‘Intracellular calcium decreases CaM-mediated KCNQ channel activity (32, 36) by detaching CaM from the channel or by inducing changes in configuration of the calmodulin-KCNQ channel complex (36).’ The CaM-KCNQ tethering is also described in a review by Alaimo and Villaroel, 2018 (doi:10.3390/biom80300579): ‘[…] CaM was first defined as an integral subunit constitutively tethered to the C-terminal region of Kv7.2/3 channels since Kv7.2 mutants that were deficient in CaM binding were unable to generate measurable currents [5,21]. However, this model has been questioned since Kv7.2 channels, carrying a hB mutation [40] or Kv7.4 hA mutated channels [41] that do not bind CaM, can still reach the plasma membrane and are functional.’

When considering to manipulate CaM binding to KCNQ, it should also be considered that previous studies on this matter have mainly worked with heterologous systems and through genetic manipulations of CaM (by expression of a dominant negative or by overexpression of CaM) or of the KCNQ binding motif.

Based on both theoretical and practical issues, we, thus, believe that it is not feasible to implement a straightforward approach that would be compatible with our mouse model.

An alternative, indirect approach, as indicated by Reviewer #3, would be to test the effect of Ca2+ chelators. Although this is likely to introduce confounding effects through the inhibition of other Ca2+-dependent channels, we propose to focus on trying this option and assess whether a XE991-sensitive component will be unmasked in MPC1 deficient cells.

3) As the authors imply that BHB activates KCNQ channels, showing this directly in their prep would provide some convincing data. If this is true, why doesn't BHB increase firing rate of WT neurons?

Activation of KCNQ channels is expected to reduce (not increase) neuronal firing. When exposed to BHB, we indeed found that WT cells also show a trend towards decreased excitability (p=0.08). We will report this trend in the revised figure 5F. Given that KCNQ channels are already available to be recruited upon repetitive firing in WT cells (to a larger extent as compared to KO, as indicated by our data with XE991) it is conceivable that a further potentiating effect of BHB at the concentration used for ex vivo recordings (2 mM) will be limited.

4) How does the anti-epileptic effects of ketones in this study relate to previous reports of regulation of KATP channels? One of main concerns is that ketones might have a parallel anti-epileptic effect in the MPC1 KO mice that is unrelated to the mechanism proposed here.

The ketogenic diet is likely to exert several effects including disruption of glutamatergic synaptic transmission, inhibition of glycolysis, and activation of ATP-sensitive potassium channels as pointed out by the reviewer. We do not exclude that inhibition of the MPC could also have an impact on the KATP channels and we are currently exploring this possibility. However, such work to dissect the potential implication of the KATP channels would go well beyond the scope of the present paper. Nevertheless, we will plan to certainly raise this important possibility in the discussion.

**Minor comments:**

1- What is the MPC1 KO efficiency in CaMK neurons? The western blot in 2c is from the whole cortex and therefore does not show that.

This is indeed a good comment, however, please note that the estimation of MPC1 KO efficiency has also been evaluated in synaptosomes isolated from MPC1 KO cortices. These structures are mainly isolated from neurons (Carlin et al., JCB, 1980. 10.1083/jcb.86.3.831). As shown in figure 2C, these synaptosomes are massively enriched for CamKII and contain less astrocytic marker GFAP in comparison to the whole cortex. The amount of MPC1 in the synaptosomes prepared from the KO animals is strongly decreased. Nevertheless, as recommended by the reviewer, we plan to quantify the efficiency of the KO by performing a double immunostaining for MPC1 and a specific marker for neurons.

2- Mitochondrial Ca2+ levels are not measured directly, for which there are many tools. This is needed to demonstrate definitively that there is a defect in Ca2+ handling."

The reviewer raised an important point and we plan to monitor the levels of mitochondrial calcium in MPC-deficient neurons using the mito-Aequorin, a luminescent quantitative probe targeted to mitochondria (Granatiero et al., Cold Spring Harb. Protoc. 2014. 10.1101/pdb.top066118)

Reviewer #1 (Significance (Required)):

see above.

**Referee Cross-commenting**

It seems we are in reasonable agreement about the pros & cons of the manuscript. I agree that alternative approaches to RU360 are warranted.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

De la Rossa and colleagues examined the consequences of conditionally knocking out MPC1,a subunit of the mitochondrial pyruvate carrier. They found that despite decreased levels of oxidative phosphorylation in excitatory neurons, phenotypically these conditional knockout mice were normal at rest. However, when challenged by inhibition of GABA neurotransmission, these animals developed severe seizure activity and expired. These authors then showed that neurons with an absence of MPC1 were hyperexcitable in part through abnormal calcium homeostasis, which was associated with a reduction in M-type inhibitory potassium channel activity. Intriguingly, the ketogenic diet and the major ketone body beta-hydroxybutyrate were able to reverse these changes.

This is a carefully conducted research study that reveals cell type-specific alterations of MPC1 deletion and functional consequences. The study design was logical and involved an exhaustive array of methodologies. The manuscript was generally well written and organized, and there are no major concerns. This study shows a direct causal relationship between impaired bioenergetics at the level of mitochondrial, and subsequent behavioral seizures, and is perhaps the most direct demonstration to date that an intrinsic disturbance of metabolic function can result in seizure activity (through changes in calcium regulation and impairment of ion channel activity). This will be an important contribution to the scientific literature.

**MINOR:**

1. Page 4, line 86: Would recommend changing "paroxystic" to "paroxysmal" (the latter which is a more recognized term). We will make the change.

Page 5, line 124: recommend including the concentration of beta-hydroxybutyrate used when first mentioned. In general, concentration and dose information were difficult to find, as well as route of administration (for kainate, page 7, line 175). This type of information was not conveniently presented.

We will follow the reviewer’s recommendation.

Page 5, line 128: "both overcomed" is awkward. Would recommend using "both reversed".

We fully agree and will make the change in the revised manuscript.

Page 8, line 193: the authors probably meant "astro-MPC1-WT mice", not "neuro-MPC1-WT mice".

Thank you for the acurate look. This will be changed.

Page 12, lines 280-282: the authors might want to mention that chronic exposure of BHB might reduce the hyperexcitability of neuro-MPC1-KO mice.

This point could indeed be discussed.

Please review entire manuscript and use consistent tense. For example, on page 13, line 309, to maintain the past tense, it should read "We first assessed whether..."

Thanks for the recommendation.

Page 13, line 318: the authors used 10 mM BHB when examining calcium levels, but they earlier used 2 mM. They need to explain why they used a different concentration; and 2 vs 10 mM are quite different.

The reviewer makes a valid point. When we performed the in vitro experiments, we used 10 mM BHB, which is slightly higher than the amount of ketone bodies measured in the blood of mice fed on a ketogenic diet for 2 days (Supplementary figure 4). This concentration of BHB has also been used by others (see for example: Izumi et al., JCI 1998, 101:1121-1132). Later on, when electrophysiology experiments were performed, the person in charge of these experiments followed a previously published protocol by Yellen and colleagues, in which the authors had used 2 mM BHB (Ma et al., J. Neurosci 2007,27: 3618-3625). This explains the differences between the concentrations used in vitro and in vivo.

Page 13, line 323: it is not necessary to say "...interesting study published during the preparation of this manuscript." This phrase should be deleted, and the relevant reference simply cited.

We will follow the reviewer’s recommendation.

The authors need to explain more clearly in the beginning what exactly is meant by "paradoxical" hyperactivity. They provide greater meaning later in the manuscript, but this should be clarified at the outset.

We will explain why we used this adjective in the beginning as recommended by the reviewer.

Reviewer #2 (Significance (Required)):

This is a very important study to show how primary defects in metabolism (i.e., disruption of the mitochondrial pyruvate carrier) can lead to epilepsy. Moreover, it details a primary mechanism that connects cellular bioenergetics to membrane excitability (through changes in calcium homeostasis and M-current function).

This is a well-conducted study that utilizes a multiplicity of experimental tools to link biochemistry with seizure activity. This type of study is not so readily done, and strengthens the notion that primary defects in metabolism can result in epileptic seizures.

This study is unique and attempts successfully to be more than just correlational. Hence it is a valuable contribution to the field.

The audience will likely consist of metabolic geneticists, neurologists/epileptologists, and neuroscientists. This is a beautiful study that runs the translational spectrum from biochemistry to behavior.

My expertise is in the field of translational epilepsy research, with a focus on mitochondria, metabolism, the ketogenic diet and ketone bodies. Thus, I am qualified to critically evaluate the entire manuscript.

**Referee Cross-commenting**

After reading comments and reviewing the manuscript again, would agree with Reviewer #1, and would change recommendation to MAJOR REVISION.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This manuscript tests the genetic requirement of the mitochondrial pyruvate carrier (MPC) in regulation of neuronal excitability. The authors find that MPC deficiency in glutamatergic neurons is associated with aerobic glycolysis, inhibition of the M-type K channels, and neuronal hyperexcitability that manifests in increased sensitivity to chemical pro-convulsants without changes in resting conditions. Alterations in Ca homeostasis in MPC-deficient neurons is consistent with reduced mitochondrial membrane potential and attendant diminution of mitochondrial calcium buffering capacity. The authors further show that the effect of MPC deficiency can be phenocopied by treatment of wild type neurons with a chemical inhibitor of the mitochondrial Ca uniporter (MCU). Based on these data, it is proposed that reduced mitochondrial Ca uptake causes neuronal hyperexcitability in the absence of MPC. Overall, the manuscript presents detailed electrophysiology and in vivo seizure studies. However, there is significant disconnect between the actual data in Fig. 6 and the authors' conclusions/proposed mechanism. In particular, the evidence for the role of Ca in the hyperexcitability due to MPC deficiency is the weak link in the authors' argument.

1. The studies linking reduced mitochondrial Ca uptake to hyperexcitability in MPC-deficient neurons (Fig. 6) have several limitations that significantly weaken the paper: 1a. The Ca measurements in cortical neurons (Fig. 6A-F) are performed under conditions (glutamate/KCl) that are fundamentally different from those used in electrophysiology of CA1 pyramidal neurons (Fig. 6G-N). The electrophysiological excitation is much briefer and less extreme than the chemical stimulation, and it is not clear that the Ca dysregulation occurs at the earliest times (see Fig. 6A).

This point was also raised by reviewer 1. Please see our response to point 2.

1b. The conclusion that MCU is functionally responsible for MPC's effect on neuronal excitability is singularly based on the use of RU360 as a chemical inhibitor of MCU but the specificity of this reagent is questionable. Evidence for a cause and effect relationship that directly implicates altered MCU/mitochondrial Ca buffering has not been provided.

This accurate point was also raised by the reviewer 1. Please see our response to point 2 for a complete response. We will downregulate expression of MCU using shRNAs. We will also measure the mitochondrial calcium level in the hope of better understanding whether the phenotype of the MPC-deficient mice is due to impaired mitochondrial calcium uptake.

1c. There is a large variation in the effect of 10 uM RU360 on firing frequency, comparing Fig. 6H and N (blue traces), including the shape of the traces and values at ramp number 6. This calls into question the reliability of the comparisons in each separate figure.

Data presented in each single graph in the main Figures were obtained from groups of littermates through recordings conducted in consecutive days. Some caution is warranted when comparing data between different figures (i.e. between different experimental series), as several factors may contribute to inter-experiment variability, including variability between different batches of animals. However, the difference pointed out by the reviewer regarding the values of cell firing reported in Fig. 6H and N is only apparent. When applying depolarizations with ramps of 5s, a fair amount of WT cells infused with RU-360 show high instantaneous firing frequency, especially for the last ramps that steeply reach high current levels. This leads to accommodation/inactivation of the action potential towards the end of the ramps, as shown in the example trace in Fig 6G. As a result, the current-frequency plot deviates from linearity, as it is the case in Fig 6H (blue trace) and, even more evidently, in Fig 6N. We have now reanalyzed the same recordings from WT cells infused with 10 µM RU-360 and measured the firing frequency in response to a square depolarizing step (250 pA) of 0.5 or 1 second. No difference was found between the firing frequencies of the cells from Fig 6H and Fig. 6N (group 1 and group 2, respectively, in the figure below). Although the ramps may lead to some distortion for higher stimulation levels, we have decided to show results from ramps consistently throughout the main figures because this protocol with continuously increasing currents allows us to measure more precisely the rheobase and the firing threshold (as opposed to the stepwise increments of a square stimulation).

1d. The calcium > PIP2 > M-type K+ channel axis is well established but has not been fully explored in the context of MPC deficiency. The use of a calcium chelator will likely be informative in this context, and would be better evidence for a role of Ca in the MPC effects.

Although the use of a Ca2+ chelator such as BAPTA is likely to introduce confounding effects through the inhibition of other Ca2+-dependent channels, we will try this option and assess whether a XE991-sensitive component will be unmasked in MPC deficient cells.

1e. The ability of BHB to rescue various parameters in this and other figures in the paper is interesting but does not directly speak to the specific mechanism as to how MPC deficiency affects neuronal excitability. BHB's effect is consistent with the metabolic flexibility of neurons when the TCA cycle cannot be fueled by glucose/pyruvate (as in GLUT1 or MPC deficiency).

The mechanism we propose to explain the hyperexcitability of MPC-deficient neurons relies on the low mitochondrial membrane potential and their decreased capacity to buffer calcium. Based on our data, we propose that calcium accumulation in the cytosol disrupts the CaM-KCNQ interaction leading to hyperexcitability. Indeed, BHB could act in two possible (and parallel) ways. 1: directly on the M-type channels, 2. on mitochondria by providing acetylCoA to the TCA cycle. The use of an alternative ketone body will be informative in disentangling these two possibilities.

The manuscript (and the field) will benefit from a more scholarly discussion and integration of published literature:

2a. The published studies on the outcome of pharmacologic MPC inhibition in neurons (Ref 18, Divakaruni et al.) are not only consistent with the bioenergetic effect in Fig. 1, but more importantly, show that interference with MPC does not lead to broad deficiencies in energy metabolism but rather remodel fuel utilization patterns to alternative substrates that feed the TCA cycle (BHB, leucine, etc). For this reason, terms such as "mitochondrial dysfunction" and "OXPHOS deficiency" used throughout the manuscript to describe MPC deficiency are vague and imprecise. In addition, this metabolic flexibility may explain lack of defects under resting conditions. In light of these considerations, the argument as to whether aerobic glycolysis in MPC-deficient neurons explains the lack of phenotype in resting conditions (p 17) seems one-sided. Overall, the studies in ref 18 are relevant to the current manuscript and should be better integrated in the discussion.

We fully agree with the possibility that the rewiring of cell metabolism in MPC-deficient neurons in the presence of leucine, BHB and other metabolites could explain the lack of phenotype in resting conditions. We thank the reviewer for this highly relevant comment which we will include in the revised discussion.

2b. Several references are cited to describe the role of OXPHOS vis-à-vis aerobic glycolysis in neuronal function. At times, however, the authors' statements are not consistent with what these papers actually show (or do not show). For example, see the use of refs 6 and 44 on p17 of the discussion, where the authors state that aerobic glycolysis uncoupled from OXPHOS is sufficient to provide ATP for normal neurotransmission, but this does not mean OXPHOS is not needed.

We agree that these references are not appropriate here and they will be removed.

2c. Although the XE991 experiments support an important role for the M-type channels in the altered excitability with deficiency, it is not clear that the proposed mechanism can explain all of the electrophysiological differences, particularly those resting properties that are measured without a Ca challenge to the neurons. It would be good to discuss other possible mechanisms that could affect neuronal excitability.

Our results point to M-type channels as important players in the phenotype of the MPC-deficient mice. Previous reports indicate that inhibition of this channel by XE991 can modulate input resistance, membrane potential and firing threshold of pyramidal cells (e.g. Shah et al, 2018, doi/10.1073/pnas.0802805105; Hu et al. 2007, DOI:10.1523/JNEUROSCI.4463-06.2007; Petrovic et al., 2012, doi:10.1371/journal.pone.0030402). We also found that XE991 induced a shift towards more negative potentials in the firing threshold of WT cells, but not in MPC1 deficient cells (-3.3±0.6 vs. -0.4±1.0, n=9, 8, p=0.027). However, we agree with the reviewer that the phenotype is probably highly complex and that additional mechanisms may contribute to modulate the intrinsic excitability of MPC-deficient neurons. One such mechanism could be closure of KATP channels, which we are currently investigating. This will be discussed.

Reviewer #3 (Significance (Required)):

The significance of the advance: The studies provide genetic evidence for the role of MPC in neuronal excitability.

The work in the context of existing literature: Please see specific comments above under point 2 regarding the need for a scholarly discussion and integration of existing literature.

Audience that might be interested: mitochondrial bioenergetics and metabolism and metabolic control of neuronal excitation.

Keywords describing expertise: metabolism, mitochondria and electrophysiology.

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Referee #3

Evidence, reproducibility and clarity

This manuscript tests the genetic requirement of the mitochondrial pyruvate carrier (MPC) in regulation of neuronal excitability. The authors find that MPC deficiency in glutamatergic neurons is associated with aerobic glycolysis, inhibition of the M-type K channels, and neuronal hyperexcitability that manifests in increased sensitivity to chemical pro-convulsants without changes in resting conditions. Alterations in Ca homeostasis in MPC-deficient neurons is consistent with reduced mitochondrial membrane potential and attendant diminution of mitochondrial calcium buffering capacity. The authors further show that the effect of MPC deficiency can be phenocopied by treatment of wild type neurons with a chemical inhibitor of the mitochondrial Ca uniporter (MCU). Based on these data, it is proposed that reduced mitochondrial Ca uptake causes neuronal hyperexcitability in the absence of MPC. Overall, the manuscript presents detailed electrophysiology and in vivo seizure studies. However, there is significant disconnect between the actual data in Fig. 6 and the authors' conclusions/proposed mechanism. In particular, the evidence for the role of Ca in the hyperexcitability due to MPC deficiency is the weak link in the authors' argument.

1. The studies linking reduced mitochondrial Ca uptake to hyperexcitability in MPC-deficient neurons (Fig. 6) have several limitations that significantly weaken the paper:

1a. The Ca measurements in cortical neurons (Fig. 6A-F) are performed under conditions (glutamate/KCl) that are fundamentally different from those used in electrophysiology of CA1 pyramidal neurons (Fig. 6G-N). The electrophysiological excitation is much briefer and less extreme than the chemical stimulation, and it is not clear that the Ca dysregulation occurs at the earliest times (see Fig. 6A).

1b. The conclusion that MCU is functionally responsible for MPC's effect on neuronal excitability is singularly based on the use of RU360 as a chemical inhibitor of MCU but the specificity of this reagent is questionable. Evidence for a cause and effect relationship that directly implicates altered MCU/mitochondrial Ca buffering has not been provided.

1c. There is a large variation in the effect of 10 uM RU360 on firing frequency, comparing Fig. 6H and N (blue traces), including the shape of the traces and values at ramp number 6. This calls into question the reliability of the comparisons in each separate figure.

1d. The calcium > PIP2 > M-type K+ channel axis is well established but has not been fully explored in the context of MPC deficiency. The use of a calcium chelator will likely be informative in this context, and would be better evidence for a role of Ca in the MPC effects.

1e. The ability of BHB to rescue various parameters in this and other figures in the paper is interesting but does not directly speak to the specific mechanism as to how MPC deficiency affects neuronal excitability. BHB's effect is consistent with the metabolic flexibility of neurons when the TCA cycle cannot be fueled by glucose/pyruvate (as in GLUT1 or MPC deficiency).

1. The manuscript (and the field) will benefit from a more scholarly discussion and integration of published literature:

2a. The published studies on the outcome of pharmacologic MPC inhibition in neurons (Ref 18, Divakaruni et al.) are not only consistent with the bioenergetic effect in Fig. 1, but more importantly, show that interference with MPC does not lead to broad deficiencies in energy metabolism but rather remodel fuel utilization patterns to alternative substrates that feed the TCA cycle (BHB, leucine, etc). For this reason, terms such as "mitochondrial dysfunction" and "OXPHOS deficiency" used throughout the manuscript to describe MPC deficiency are vague and imprecise. In addition, this metabolic flexibility may explain lack of defects under resting conditions. In light of these considerations, the argument as to whether aerobic glycolysis in MPC-deficient neurons explains the lack of phenotype in resting conditions (p 17) seems one-sided. Overall, the studies in ref 18 are relevant to the current manuscript and should be better integrated in the discussion.

2b. Several references are cited to describe the role of OXPHOS vis-à-vis aerobic glycolysis in neuronal function. At times, however, the authors' statements are not consistent with what these papers actually show (or do not show). For example, see the use of refs 6 and 44 on p17 of the discussion, where the authors state that aerobic glycolysis uncoupled from OXPHOS is sufficient to provide ATP for normal neurotransmission, but this does not mean OXPHOS is not needed.

2c. Although the XE991 experiments support an important role for the M-type channels in the altered excitability with deficiency, it is not clear that the proposed mechanism can explain all of the electrophysiological differences, particularly those resting properties that are measured without a Ca challenge to the neurons. It would be good to discuss other possible mechanisms that could affect neuronal excitability.

Significance

The significance of the advance: The studies provide genetic evidence for the role of MPC in neuronal excitability.

The work in the context of existing literature: Please see specific comments above under point 2 regarding the need for a scholarly discussion and integration of existing literature. Audience that might be interested: mitochondrial bioenergetics and metabolism and metabolic control of neuronal excitation.

Keywords describing expertise: metabolism, mitochondria and electrophysiology.

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Referee #2

Evidence, reproducibility and clarity

De la Rossa and colleagues examined the consequences of conditionally knocking out MPC1,a subunit of the mitochondrial pyruvate carrier. They found that despite decreased levels of oxidative phosphorylation in excitatory neurons, phenotypically these conditional knockout mice were normal at rest. However, when challenged by inhibition of GABA neurotransmission, these animals developed severe seizure activity and expired. These authors then showed that neurons with an absence of MPC1 were hyperexcitable in part through abnormal calcium homeostasis, which was associated with a reduction in M-type inhibitory potassium channel activity. Intriguingly, the ketogenic diet and the major ketone body beta-hydroxybutyrate were able to reverse these changes.

This is a carefully conducted research study that reveals cell type-specific alterations of MPC1 deletion and functional consequences. The study design was logical and involved an exhaustive array of methodologies. The manuscript was generally well written and organized, and there are no major concerns. This study shows a direct causal relationship between impaired bioenergetics at the level of mitochondrial, and subsequent behavioral seizures, and is perhaps the most direct demonstration to date that an intrinsic disturbance of metabolic function can result in seizure activity (through changes in calcium regulation and impairment of ion channel activity). This will be an important contribution to the scientific literature.

MINOR:

1. Page 4, line 86: Would recommend changing "paroxystic" to "paroxysmal" (the latter which is a more recognized term).
2. Page 5, line 124: recommend including the concentration of beta-hydroxybutyrate used when first mentioned. In general, concentration and dose information were difficult to find, as well as route of administration (for kainate, page 7, line 175). This type of information was not conveniently presented.
3. Page 5, line 128: "both overcomed" is awkward. Would recommend using "both reversed".
4. Page 8, line 193: the authors probably meant "astro-MPC1-WT mice", not "neuro-MPC1-WT mice".
5. Page 12, lines 280-282: the authors might want to mention that chronic exposure of BHB might reduce the hyperexcitability of neuro-MPC1-KO mice.
6. Please review entire manuscript and use consistent tense. For example, on page 13, line 309, to maintain the past tense, it should read "We first assessed whether..."
7. Page 13, line 318: the authors used 10 mM BHB when examining calcium levels, but they earlier used 2 mM. They need to explain why they used a different concentration; and 2 vs 10 mM are quite different.
8. Page 13, line 323: it is not necessary to say "...interesting study published during the preparation of this manuscript." This phrase should be deleted, and the relevant reference simply cited.
9. The authors need to explain more clearly in the beginning what exactly is meant by "paradoxical" hyperactivity. They provide greater meaning later in the manuscript, but this should be clarified at the outset.

Significance

This is a very important study to show how primary defects in metabolism (i.e., disruption of the mitochondrial pyruvate carrier) can lead to epilepsy. Moreover, it details a primary mechanism that connects cellular bioenergetics to membrane excitability (through changes in calcium homeostasis and M-current function).

This is a well-conducted study that utilizes a multiplicity of experimental tools to link biochemistry with seizure activity. This type of study is not so readily done, and strengthens the notion that primary defects in metabolism can result in epileptic seizures.

This study is unique and attempts successfully to be more than just correlational. Hence it is a valuable contribution to the field.

The audience will likely consist of metabolic geneticists, neurologists/epileptologists, and neuroscientists. This is a beautiful study that runs the translational spectrum from biochemistry to behavior.

My expertise is in the field of translational epilepsy research, with a focus on mitochondria, metabolism, the ketogenic diet and ketone bodies. Thus, I am qualified to critically evaluate the entire manuscript.

Referee Cross-commenting

After reading comments and reviewing the manuscript again, would agree with Reviewer #1, and would change recommendation to MAJOR REVISION.

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Referee #1

Evidence, reproducibility and clarity

The authors have presented a very interesting and compelling set of data regarding the impact of conditional deletion of the only known pathway allowing the uptake of pyruvate into mitochondria. The paper comprises two interwoven stories that are both important. The first is the remarkable finding that the majority of excitatory neurons in the cortex (i.e. those under the influence of the CaMKII promoter)show remarkable metabolic flexibility as they tolerate elimination of pyruvate oxidation, considered the major supplier of ATP in neurons. The data on this seem clear although the authors did not delve into the potential mechanisms of metabolic compensation that likely occurs. Instead they examined whether there was some mal-adaptive compensation and they found clear evidence of this: in the absence of MPC activity the mice are much more prone to epileptic seizures, unveiled experimentally by relatively standard protocols (kindling). The authors present largely very convincing evidence that this mal-adaptive compensation in turn ends up decreasing the activity of KV7.2/7.3 channels whose job is normally to limit runaway repetitive firing by mediating an hyperpolarizing K+ efflux following an action potential. This channel, put on the map as it was one of the downstream targets modulated by cholinergic metabotropic activation, is also know known to be controlled by Calmodulin and therefore cytosolic Ca levels. Overall, I think at its core this manuscript is interesting and important. There however several weaknesses, I fear, will diminish the impact on the eventual readership. If these points can be addressed, it will strengthen the longevity of these findings:

1) It is puzzling why the authors resorted to using shRNA-mediated KD of MPC1 for some of the in vitro studies when they have gone to the trouble of making a floxed CRE-dependent mouse. Primary cells (e.g. Fig 1) or organotypic cultures (Fig. 6) from these mice would have made a more consistent set of starting conditions to compare data across the manuscript. As there viruses expressing the CRE recombinase are widely available this could have been used on mice simply harboring the floxed gene it they are worried about waiting for the expression of the CaMKII promoter for in-vitro conditions.

2) The data in Figure 5 gets a little less convincing as using extracellular glutamate to drive Ca elevations is so non-physiological that the results might really be distorted by the participation of something irrelevant to the story, even though it supports the overall interpretation for a role of Ca/CaM in the control of the channel. Similarly, the use of RU360 should be done with caution. The drug, although a useful antagonist of MCU in purified mitochondria, is famously finicky with respect to its ability to cross membranes and could well have off target impact. A much cleaner experiment would be to suppress the expression of MCU via KD. Presumably in the MPC-deficient neurons, this would have minimal impact on Ca signals. Given the frequent ambiguity associated with interpreting pharmacological results, coupled to the central importance of this finding in interpreting the entire paper, I think carrying out experiments with molecular genetic manipulation of MCU is warranted.

3) The authors have not really made clear in this paper whether the ability to suppress the phenotype of the MPC deficiency with ketones is really related to a providing TCA cycle support or instead a pharmacological impact on non-TCA related targets (such as the Kv7.2/7.3 channels). Presumably the use of other ketones might circumvent this. The action of ketone bodies has been a topic of considerable interest in neuroscience, given the clinical relevance for childhood epilepsies. Previous studies for example have argued for direct inhibition of the vesicular glutamate transporter (Juge et al. Neuron 2010). The use of other ketones (acetoacetate) would narrow down the interpretations of the data.

other

1) In vitro - scramble controls only serve to demonstrate there is no general effect of treating cells with shRNAs, but do not address if there is an off-target effect. The most convincing thing here would be to have an shRNA-insensitive variant that rescues.

2) Does rescuing CaMK binding to KCNQ channels rescue the phenotypes?

3) As the authors imply that BHB activates KCNQ channels, showing this directly in their prep would provide some convincing data. If this is true, why doesn't BHB increase firing rate of WT neurons?

4) How does the anti-epileptic effects of ketones in this study relate to previous reports of regulation of KATP channels? One of main concerns is that ketones might have a parallel anti-epileptic effect in the MPC1 KO mice that is unrelated to the mechanism proposed here.

Minor comments:

1- What is the MPC1 KO efficiency in CaMK neurons? The western blot in 2c is from the whole cortex and therefore does not show that. 2- Mitochondrial Ca2+ levels are not measured directly, for which there are many tools. This is needed to demonstrate definitively that there is a defect in Ca2+ handling."

Significance

see above.

Referee Cross-commenting

It seems we are in reasonable agreement about the pros & cons of the manuscript. I agree that alternative approaches to RU360 are warranted.

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Referee #1

Evidence, reproducibility and clarity

This study seeks to define how human lysosomes selectively downregulate membrane proteins and identify the machinery involved in this process. To this end, the authors screened a set of 30 lysosome membrane proteins (LMPs) in a cycloheximide chase assay in a human cell line which led to the identification of RNF152 (an E3 ligase) as a particularly short lived LMP. Further experiments demonstrate that RNF152 degradation is ubiquitin, ESCRT and lysosome dependent. They also show that the E3 ubiquitin ligase activity of RNF152 is critical for its turnover. The overall technical quality of the experiments is high and conclusions about the degradation of RNF152 are mostly reasonable. My most significant concern is that while compelling data is provided for RNF152 turnover, the authors over-reach in their efforts to generalize their findings to other LMPs. Given that the E3 ligase activity of RNF152 is so important for its turnover, RNF152 might be a special case. Consistent with this, the authors did not characterize other LMPs with similarly high rates of turnover. Although it would be interesting if RNF152 regulates the stability of other LMPs, until such proteins are identified, the authors should be more cautious in their interpretation. Speculation on this matter is reasonable so long as it is labeled as such. Even with respect to RNF152 turnover mechanisms, the overall conclusions would be significantly strengthened by a demonstration that the endogenously expressed, untagged protein behaves in a similar manner to what was described for the GFP-tagged transgene. With respect to the question about how long it would take for the authors to address these concerns, I cannot give a precise answer as it would depend on whether they decide to much more narrowly interpret their findings and temper their major claims (less than a month) or to expand efforts to generalize results (time frame unknown and perhaps not feasible).

1. As a specific (but not the only) example of over-reaching in generalizing the findings, the abstract ends with the following statement: "Thus, our study uncovered a conserved mechanism to down-regulate lysosome membrane proteins." My concern is that although this mechanism might be generalizable, the authors have only presented data for RNF152.
2. There is a complete reliance on over-expressed, GFP-tagged RNF152. There is no demonstration that the endogenously expressed protein undergoes such high rates of turnover. It is thus possible that the data does not reflect the normal turnover pathway for this protein.
3. In Figure 2B, why is the loss of full length RNF152-GFP not accompanied by an increase in the signal for free GFP during these pulse-chase experiments?
4. Figure 2E: Were all of the pairs of Input and IP immunoblots subject to the same exposure and image adjustments?
5. Figure 3C-E: The RNF152 mutants have slowed but not eliminated degradation. Is this dependent on their association with or ubiquitination by the endogenouslyh expressed RNF152?
6. Methods section indicates that t-tests were performed for all statistics. However, many experiments contain multiple comparisons and are thus ideally suited to t-tests. The authors should either justify the use of t-tests or provide a more suitable statistical analysis.
7. Although the model in Figure 7 shows the E3 (RNF152) ubiquitinating other proteins and promoting their ESCRT-dependent sorting into ILVs, this study did not identifying any such clients of RNF152.

Minor

Page 3: "Without treatment, almost all types of LSD patients will develop severe neurodegeneration in the central nervous system." This statement is misleading as there are multiple forms of LSDs that do not result in neurodegeneration and it is only these LSDs which can be successfully treated via enzyme replacement therapies. Unfortunately, the neuropathic LSDs remain largely untreatable due largely to issues of blood brain barrier permeability.

Page 3: "As we age, the lysosome membrane gradually accumulates damaged proteins and loses its activity, which dampens the cell's ability to remove pathogenic protein aggregates and damaged organelles, eventually leading to cell death and inflammation (Carmona-Gutierrez et al., 2016; Cheon et al., 2019; Yambire et al., 2019)." The references provided do not provide sufficient direct support for this broad statement.

Page 10: STED imaging results (currently "data not shown") should be supported by showing the relevant data.

Camera and objective information should be provided for microscopy studies.

Significance

The identification of a generalizable mechanism for the turnover of mammalian LMPs would represent a significant advance and would raise many interesting questions about mechanisms, regulations and physiological impact. While this studies contributes some interesting new clues to this topic, it falls short of unambiguously establishing how most LMPs are turned over in human cells. The data with respect to RNF152 is intriguing as it supports the idea that a novel form of ESCRT-dependent protein clearance occurs at the limiting membrane of lysosomes. However, it remains very much unclear to what extent this can be generalized to other proteins.

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Referee #2

Evidence, reproducibility and clarity

The mechanisms involved in lysosome membrane protein turnover are not well understood. Weichao et al. used a cycloheximide chase screen and overexpression 30+ lysosome membrane proteins in HEK293 cells to identify LMPs (lysosome membrane proteins) with fast turnover rates. They identified RNF152 as a suitable candidate for study given its high turnover rate and physiological relevance. They showed that RNF152's levels were regulated by ubiquitination by mutating cytosolic lysine residues and RNF152's ring domain and finding that these changes increased RNF152 stability. The researchers found that knocking down ESCRTIII and overexpressing a dominant-negative mutant of VPS4 increased RNF152 levels at steady-state and delayed RNF152 turnover. When expressed in yeast, RNF152 is localized on vacuole membrane and is also subject to regulation by the ESCRT pathway. Early ESCRT pathway members are essential for RNF152 degradation in yeast but not in mammalian cells. Taken together, these findings are important for furthering our understanding of how the levels of lysosome membrane proteins are regulated. A better understanding of ESCRT mediated LMP degradation is important not only for understanding mechanisms involved in controlling lysosomal activities but also for therapeutic development for many diseases involving dysregulation of LMP protein levels.

However, the following concerns should be addressed before the paper is published:

1. The authors have found that among 30 LMPs, three LMPs, LAPTM4A, RNF152, and OCA2, have half-lives less than 9 hours. RNF152 is a ubiquitin ligase and the authors showed that auto-ubiquitination is important for the recognition by the ESCRT machinery. Can the authors speculate how the ligase activity of RNF152 is regulated? Also, is similar mechanism involved in LAPTM4A and OCA2 turnover? Are these two proteins also ubiquitinated?
2. The authors should at least demonstrate that endogenous RNF152 levels and turnover are also regulated by ESCRT III and VPS4, using the stable cell lines the authors have already made. All of the mammalian cell experiments are performed using overexpression of RNF152, and an endogenous experiment would inspire confidence that the author's findings are not an artifact of over-expression.
3. While the authors showed that the K->R and C->S mutants of RNF152 have increased stability, it would be more compelling if they could perform an IP using HA-ubiquitin to prove this effect is due to a loss/reduction of RNF152 ubiquitination and not due to other changes in the protein. Another concern is whether mutating 8 lysine or 4 cysteine residues simultaneously would affect the folding of the protein, leading to abnormal aggregation in the cell.
4. For some of the data, statistical analysis is missing: a. All of the cycloheximide chase experiments. b. statistical significance for the puncta vs membrane GFP signal data shown in figure 6f c. The flow cytometry data
5. Fig. 4A and Fig. S2A, why MG132 treatment affects the levels of free GFP if it's inside of the lysosome?
6. Make sure that the figures are properly referenced in the text, there is one instance where the authors referenced figure 2d, when they clearly meant to reference figure 2e, and figure 2e where the authors meant to reference figure 2f etc.

Minor Comments:

1. In figure 1A, at CHX 3h, there's ~40% reduction of GFP-RNF152, however, in the rest of the figures, such as figure 2B，at CHX 2h, there's ~70-80% reduction of GFP-RNF152. How to explain the difference in the kinetics?
2. In figure 2F, it is hard to differentiate when the underline for input ends and the underline for IP begins unless the reader zooms in, please separate them a bit more.
3. Fig. 4F, it's very hard to see the red and green signals, maybe get rid of the DAPI channel increase the intensity for both green and red channels, and zoom in?
4. Scale bars are missing in the insert images in figure 1C, figure 4G and figure 6E.
5. In figure S1, the labels do not match with the blot for GFP-TMEM106B time points.

Significance

These findings are important for furthering our understanding of how the levels of lysosome membrane proteins are regulated. A better understanding of ESCRT mediated LMP degradation is important not only for understanding mechanisms involved in controlling lysosomal activities but also for therapeutic development for many diseases involving dysregulation of LMP protein levels.

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Referee #3

Evidence, reproducibility and clarity

Summary

Lysosomes play key roles in cellular homeostasis by functioning as a signaling hub for growth control and acting as a terminal catabolic station. Deregulation of lysosomes are now linked to multiple human diseases including cancer, neurodegeneration and etc. An emerging topic of interests in lysosomal biology is the regulation of lysosomal proteostasis and how it impacts the overall fitness and functionality of the lysosome per se. Zhang et al presents here a case study of quality control of lysosomal membrane proteins, with a focus on the turnover of a lysosomal anchor E3 ubiquitin ligase RNF152. They showed that RNF152 is rapidly degraded through an ESCRT-dependent fashion and that this mechanism is also conserved in yeast.

Major comments:

1. The writing of the manuscript including the abstract could be further polished. The manuscript in its present form appears to be a technical report that does not sufficiently convey the significance of this study.
2. Cyclohexamide is commonly used in studying the half-lives of proteins of interests. This is not a new method authors developed in the first place.
3. The data of protein turnover was presented by plotting the relative level of proteins as a function of time. But the use of degradation kinetics was all over the place in the manuscript, which is inappropriate scientifically. The authors should first generate fit to first order decay to acquire a degradation rate constant, k (min-1) and calculate half-life (T1/2) from there.
4. What are the functional consequences of RNF152 degradation? What are the biological impacts at both lysosomal and cellular levels in RNF152-depleted cells?
5. Given the rapid turnover of RNF152 at basal state, one can predict that this protein may become functionally important under specific circumstances, for example, certain stress. This aspect is worth exploring.
6. The authors chose RNF152 over OCA2, a melanosome-specific protein. However, OCA2 was shown to colocalize with LAMP2 much better than RNF152.

Minor comments:

1. Mislabeling and typo errors detected in the text: a. Page 7 "As expected, the full-length GFP-RNF152 and other lysosomal proteins such as LAMP2 and cathepsin D (CTSD) were enriched by Lyso-IP. In contrast, PDI (ER), Golgin160 (Golgi), EEA1 (endosomes), and GAPDH (cytosol) were not enriched (Figure 2D)." - should be Figure 2E instead. b. Page 7 "Our result confirmed that the lysosome population of GFP-RNF152 is quickly turned over, while LAMP2 is very stable on the lysosome (Figure 2E)." - should be Figure 2F instead. c. Page 14 "knocking down either TSG101 or both TSG101 and RNF152 only had a minor impact on the degradation kinetics of GFP-RNF152 (Figure S3A-B)." - should be ALIX instead of RNF152.
2. Stable cells expressing GFP-RNF152 or 3xFLAG-RNF152 were primarily used in this study. It will be useful to perform some experiments by examining the endogenous counterpart using antibodies against RNF152. For example, Figure 2D and 2E.
3. For all the flow cytometry analysis, the value of GFP intensity in respective graphs should be indicated.
4. Statistics analysis was not performed on Figure 5D.
5. In Figure 6D and J, what are the reasons for the appearance of multiple peaks, particularly, by the red line?
6. In Figure 3A, the question marks should be removed to avoid confusion. "Predicted" can be used instead if there is no direct evidence from mass spec analysis.
7. In Figure 3C, the authors identified two mutants including KR and CS that are refractory to degradation. It will be more insightful by showing the ubiquitination of these two mutants as in Figure 3B.

Significance

Multiple mechanisms including ESCRT complex have been reported to regulate the quality control of lysosomes. Understanding the roles of each mechanisms and selection of their substrates in maintenance of lysosomal integrity is of great interest in cell biology. Zhang and colleagues showed a case study of RNF152, a substrate of ESCRT-dependent degradation, but did not further pursue the biological functions of RNF152. This somewhat limits the conceptual advance of the study.

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Reply to the reviewers

We would like to thank the editor for their consideration and the reviewers for their time and thoughtful comments. Below we have written a point-by-point response to their comments and concerns. The original comments are displayed in italic fonts, whereas our responses are in regular fonts for clarity.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The submitted manuscript 'Identification of phenotype-specific networks from paired gene expression-cell shape imaging data' of Barker et al. uses a convolute of different bioinformatics tools (see Key Resource Table) to analyze reported RNA sequencing data and to correlate derived pathways with imaging features of breast cancer cell lines based on specific pathway constructions. The thin red line of the data presentation in the manuscript is not obvious.

\*Major concerns:***

1.1 The main biological 'finding' of the study RAP1 'as a potential mediator between the sensing of mechanical stimuli and regulation of NFkB activity' is reported and therefore the assumption 'how exactly extra-cellular mechanical cues are sensed by the cell and passed on to NFkB in breast cancer is not understood' is misleading. Please review: https://www.nature.com/articles/ncb2080** (human breast cancers with NF-κB hyperactivity show elevated levels of cytoplasmic Rap1. Similar to inhibiting NF-κB, knockdown of Rap1 sensitizes breast cancer cells to apoptosis) https://pubmed.ncbi.nlm.nih.gov/17510404**/ (RAP1 is a crucial element in organizing acinar structure and inducing lumen formation), and https://pubmed.ncbi.nlm.nih.gov/21429211/**.

R1.1 We thank the reviewer for pointing out these references. Teo et al. (which is cited in our manuscript) provides evidence that Rap1 regulates IKK and therefore NFkB in breast cancer, while Itoh et al. and McSherry et al. focus on Rap1’s ability to modulate migration and morphogenesis as do other similar papers cited in our manuscript. None of the papers show the significance of the Rap1-NFkB interaction in the explicit context of cell shape with Teo et al. only speculatively mentioning a potential relevance of Rap1/NFkB in migration (“Given that NF-κB is critical for [. . . ] stimulating invasion, our results document a clinical setting wherein Rap1-mediated regulation of NF-κB could be critical.”). We appreciate that the specific sentence the reviewer has drawn attention to is slightly misleading given Teo et al. and we will amend it in the revised manuscript. However, here, we use a novel methodology on a past dataset to link the concepts introduced by these 3 papers within the specific context of cellular morphology in breast cancer cells.

Specifically, in this manuscript, we identify a Rap1 expression module correlated with cell shape and find that it is at the network confluence of transcription factors activated by cell shape. This, along with our findings of modulation of NFkB co-activators, as well as previous work showing that it is a key mechano-transductive transcription factor leads us to hypothesize that Rap1 mediates the regulation and mechano-sensing of cell shape via its interaction with NFkB.

It is also important to note that, while we build on the findings of Teo et al., McSherry et al. and Itoh et al. relating NFkB, Rap1 and cell shape, we also use our method to focus on other proteins of interest. These are drawn attention to in the discussion, with the ARNT KO/TNFalpha module being the most highly correlated gene expression module with the morphological features. Also, the importance of transcriptional co-regulators of NFkB are illustrated in the network propagation, with both NR0B2 and PPARGC1A mentioned in the discussion. However, our analysis naturally concentrates on the node with the most apparent literature support, which as your reading suggests is Rap1. The significance of this manuscript is that it is an unbiased systems-based methodology used to link cell-shape with signaling, via transcription in a context-specific manner (i.e. in the context of breast cancer). This produces a phenotype-specific network that has allowed us to connect diverse mechanisms and hypotheses put forward by other authors and further our understanding of how signaling manages the sensing and regulation of cell shape in breast cancer. The methodology is also applicable to any paired transcriptomics/phenotype dataset.

1.2 Besides, Fig. 2 and 3 are unrelated to this main statements.

R1.2 Figure 2 shows the results of our morphological cluster identification and subsequent differential expression analysis. Since these were included as parts of the network, we included them to give the reader an idea of the components included by this step. Figure 3A shows the network that was generated by our pipeline which forms the basis of all subsequent biological exploration, and the discovery of Rap1 and nodes important for the regulation of cell shape. Figure 3B shows that no bias was introduced by using the specific algorithm for our network generation. As such Figures 2 and 3 are related to the generation of the cell shape-specific network that forms the basis of our study. We will amend the text and figure legends to clarify this point more carefully, and we will consider moving some of the panels to the supplementary materials to simplify the message.

1.3. The spotted RAP1 (by TFs JARD2 and RUNX2) finding is not obvious without Fig. 4 results, a network propagation of functional TFs in differentially activated processes (basal vs. luminal) in the cell shape regulatory network. Please show that RAP1 could be not identified without the network based on TF and DEG only.

R1.3 The Rap1 hypothesis is supported by both Figure S2E and Figure 4. Figure S2E shows that the Rap1 pathway-enriched gene expression module is the most differentially expressed module among those incorporated in our cell shape regulatory network. This suggests that this module is correlated to cell shape on a transcriptomic level, but does not necessarily mean anything within the context of intracellular signaling. Figure 4 shows that this gene expression module is at the confluence of activated transcription factors as specified by our constructed signaling network. This is an interesting finding as it implies (unlike Figure S2E) that the Rap1 gene expression module is relevant to intra-cellular signaling.

While the Rap1 module is indeed differentially expressed and could in theory have been found just by the DE analysis as being important, the network approach enables us to integrate these modules of co-expressed genes within known signaling networks. This allows us to go further than just making comments about expression and transcription factor activity, to discussing how signaling networks interact with our identified gene expression modules. This in turn allows us to construct more sophisticated hypotheses about cell shape regulation.

Particularly, we use this analysis to reinforce the association with Rap1 by illustrating that the Rap1 network node lies at the confluence of transcription factors activated in luminal-like and basal-like cell shapes. We also use the network to identify highly central nodes (such as PPARGC1A, CTNNB1 and ESR1) and other proteins identified in the network propagation (YAP1, IKBKB and ARNT). Furthermore, the network is used as a means of integrating gene expression modules in their signaling network environment. The method by which this embedding was done (in-going edges being transcription factors regulating the module and out-going edges being signaling proteins contained within the module) adds context specificity to a network that is otherwise generalised to many cell-types and contexts.

The lack of clarity on how we arrived at Rap1 as a key tenet of our discussion, as well as the added value to the methodology of the network analysis is something that we will certainly work on in our revision and we thank the reviewer for their valuable feedback. We will also move Figure S2E from the supplementary figures to the main Figure panels, as it is an important part of how we arrived upon Rap1 as a module of particular interest.

1.4 More complex fluorescence phenotypes are available and do not match the complexity of the RNASeq data, data input and pathway construction with only 10 simple cell shape features. Conversely, relative 'monoclonal' breast cancer cell lines may are the only application for this workflow.

R1.4 We thank the reviewer for their comment and respectfully disagree. These cell shape features were sufficient for the original authors Sero et al. to predict TF activities (PMID: 26148352) and Sailem et al. to identify clinically predictive metagenes (PMID: 27864353). Although these features seem simplistic, they concisely summarise a highly complex phenotype and are proven to encode metastatic potential (PMCID: PMC6976289) and to be prognostic markers for breast cancer progression (PMID: 28977854). Accordingly, these features are re-analysed using our workflow to better understand the signaling that drives them. Understanding other features that might match the complexity of our expression data is possible using the presented method, but is outside of the scope of the research within this manuscript as our research question focuses on the regulation of cell shape in breast cancer.

As evidence that this cell shape network is applicable beyond cell lines, we can perform an analysis on breast cancer patient data from the TCGA, demonstrating the relationship of our network’s components with metastasis, which is highly related to cell shape.

1.5 Image features Fig. 1 and 5 do not match

R1.5 It is true that the features in Fig.1 and Fig.5 do not exactly match. This is because these two datasets came from different studies. While they are slightly different features, the essential phenotypes that they quantify are the same. For example, in Fig 5., cytoplasm area, cytoplasm perimeter, nucleus area, nucleus length, nucleus width and nucleus perimeter, are clearly basic morphological features that are analogous to features in Fig.1, such as cell area, cell width to length, nucleus area, nucleus width to length. It is a solid assumption that the biological processes that drive these features are common, and our results illustrate this. Meanwhile, the existence of features measured in the dataset in Fig.5, that are not analogous to those used in the dataset used for model construction, provide convenient negative controls in order to determine that our network describes regulatory processes specific to the features used in network construction.

1.6 with Fig. 5 being a rather indirect 'proof' of usability.

R1.6 The purpose of Figure 5 is not to demonstrate usability but to prove that the network that we have identified is indeed representing cell signalling that controls cell shape. It shows that perturbations inside our network have a significantly stronger effect on phenotypes used in the creation of the network than perturbations outside our network. Moreover, it shows that this is not the case for phenotype features not used in the creation of our network, underlining that our network is both accurate and specific to the phenotypes used as input. We will add further clarifications in the text and figure legend to explain this better.

1.7 Fig. 1a has not achieved a visual descriptive state and asking a lot.

R1.7 We apologize for the lack of clarity here and will revise the figure to better present the method and reduce confusion.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The authors combine single cell morphology and gene expression data to identify signaling activities implicated in the control of cellular morphogenesis. They describe a reasonable bioinformatics pipeline from gene expression shifts between two morphological phenotypes to pathways, then to common transcription factors to signaling. As far as I can assess the situation (I am not familiar with all the tools they use) the proposed pipeline works convincingly.

We would like to thank their reviewer for their thoughtful comments and to clarify that the analysis has not been done on single cell gene expression data, but rather on bulk RNAseq data. This is further explained in the point-by-point responses below.

2.1 However, I am concerned that the logic underlying this analysis is only partially valid. The link between signaling and morphology may be more direct than via TF-based gene expression regulation. Many signals (and many of the kinases the authors test for validation) are implicated in morphology control as direct upstream regulators of cytoskeleton dynamics and adhesion. This also applies to the GTPase Rap1, which the authors fish out as the most differentially expressed signal between two types of morphologies. In addition to the indirect effect of Rap1 on morphology via NFKB regulation suggested by the authors, Rap1 will affect morphology probably very directly through activation of Rac -> F-actin and RIAM -> nascent adhesions. At minimum, the authors should discuss this complexity as a caveat of their approach. And dependent on the impact the authors hope to have with this story, I believe they should experimentally resolve the ambiguity of direct vs indirect signaling for some of their key interpretations.

R2.1 We thank the reviewer for making this fair point about the limitations of our data, i.e that we are not able to directly observe and delineate exactly how upstream signaling has modulated or is modulated by cell shape. As a first major clarification, which we will make sure to include in the text, the Rap1 node doesn’t necessarily represent the Rap1 GTPase itself. It is a co-expression module that is enriched in activators and downstream effectors of Rap1 signalling. As such when we are talking about the Rap1 module we mean the subnetwork of Rap1 signalling rather than the specific small GTPase itself. Thus, we can’t assume that Rap1 itself is the key node in this subnetwork and it is therefore complicated to design specific experiments to test the direct or indirect modulation of cell shape by Rap1. We agree however that additional information regarding the role of this module in regulating cell shape would be interesting and valuable.

For this study, we have access to transcriptomic and cell shape data from 14 cell lines with transcriptomic and cell shape data. Using the expression data, we will quantify Rap1 expression module activity and its relationship to NFkB transcriptional activity across these cell lines. By comparing in these cell lines the effect on morphology when NFkB and the Rap1 module are combinatorially activated or deactivated, we can disseminate between competing hypotheses for direct and indirect activities of these two factors on cell shape. For example, if the overwhelming source of Rap1 module’s function was via direct interaction with F-actin, then Rap1 module activity would be predictive of cell shape, regardless of NFkB activation. A caveat to this is our limited access to only 14 cell lines. Additionally, if necessary, we have access to drugs that can induce cytoskeletal defects and perturb morphology directly. This can be used to disrupt the relationship between Rap1 and F-actin that the reviewer has identified and gauge the effect on cell shape. If such an intervention disrupts the relationship between Rap1 signaling module/NFkB transcriptional activity and cell shape then we can hypothesise that the activity of Rap1 signaling is greater than just its direct activity on F-actin. Finally, we can perform a knock-down of Rap1 (or selected components of its module) and NFkB itself and gauge the effect of such a perturbation on the Rap1 gene expression module and cell shape.

That being said, these signaling modulations (whether indirect or direct) are reflected accordingly in differentially activated transcription factors, and therefore can be observed and recorded from expression data. This is an interesting finding, as it implies that signaling processes not explicitly making use of transcription factors (such as those that directly affect adhesion complexes, regulating cytoskeletal proteins etc) can still have their activity gauged through their indirect downstream expression signatures. In any case, our findings illustrate that there is a cell shape-specific modulation of the Rap1 module in breast cancer, reflected in the expression data. Rap1 almost certainly has some direct contributions to cytoskeletal dynamics in breast cancer (PMID: 10805781, PMID: 30156466 and PMID: 22644079), but here we observe clearly how it also is modulating transcription factors, that we hypothesise may contribute to the development of a morphological and transcriptomic ‘niche’ in a more robust and long-term fashion. Nonetheless, the points discussed by the reviewer are valuable and in our revision we will discuss this as a potential caveat.

In defense to the presented premise, the authors start out by looking for correlation between gene expression and morphology, and they find some signal. Correlation analysis, especially in large data sets, tends to be pretty robust and specific, even on presence of strong confounders. Thus, even though the correlation expression-morphology, which points indirectly at morphology-regulating signaling modules, is likely to be super-imposed by direct morphology-regulating signaling pathways the proposed approach will not be able to detect, the presented analysis is valuable, in principle.

We thank the reviewer for their positive comments.

That said, I have a number of substantial concerns also with the implementation and presentation of the approach.

2.2 First, on the presentation side, for a paper that talks about cell morphology it is strange to have not a single figure panel showing an image of cells, or at least cell outlines. As a reader I would like to get visual impression of how different a high vs low Rap1 gene expresser is, for example.

R2.2 - We agree that it would greatly help the clarity and message of the manuscript. As we are not able to use the public and previously published data that have been used for our paper due to copyright laws associated with journal publications, we will generate relevant images representative of the respective cell shapes and include them in the manuscript.

2.3 Along the same lines, it is not quite clear to me when the authors collate entire cell lines into a single phenotype, do they switch then to population-based analysis? That is, for example the volcano plots in 2B,C are they representing an average gene expression shift?

R2.3 - We apologise for the lack of clarity. The morphological clustering and differential expression illustrated in Figure 2 is to find expression signatures responsible for distinct breast cancer cell shapes. We link our expression data and our imaging data via the breast cancer cell lines and so are limited to studying expression in bulk per cell lines. The volcano plots in 2B,C are of the differentially expressed genes (as calculated by DESEQ2) in morphologically distinct clusters of cell lines as specified by Figure 2A. This was collated so we could observe transcriptomic differences accounting for cellular morphology, rather than differences in cell lines (these being already well characterised and not in the scope of this manuscript).

We will add additional clarifications in our revised manuscript to further explain this.

2.4 How heterogeneous are the morphological signals?

R2.4 We provide values of standard deviation for the morphological features of the derived clusters (page 4 - “Clustering based on morphology reveals distinctive cell-line shapes”). The heterogeneity of the morphological clusters is minimised as per the elbow plot shown in Figure S2A. This plot illustrates the decreasing total within-cluster variation of the cell shape groups as the number of clusters (k) is increased. The point of inflection represents the optimum number of clusters (in our case k=3). Aside from this, we note that one of those 3 clusters is significantly more heterogeneous both morphologically speaking and biologically speaking (illustrated Figure 2A) and so we used the other two which showed more informative gene expression profiles and could be annotated roughly with breast cancer subtypes (basal and luminal - although is alignment was not perfect since the grouping was based only on the morphology). We took the more heterogeneous cluster (cluster A, Figure 2A) to be the least relevant cluster in terms of morphology and biologically significance, also because it contained the non-tumorigenic cell-line MCF10A.

2.5 Are the correlations between gene expression and morphology computed with single cell data as the basis?

R2.5 Due to the availability only of bulk RNA sequencing data for the cell lines for which we also had high content imaging data, all analyses are done using bulk RNA sequencing data at the cell line level. We will clarify this in the text and methods section.

2.6 Could the volcano plots be sharpened by accounting for the single cell variation in morphology instead of lumping the cells into two morphological classes?

R2.6 As per the limitations mentioned in R2.3 and R2.5, we cannot study gene expression at the single cell level. Furthermore, the utility of using morphological clusters was so that we could observe morphological transcriptomic traits rather than those specific to cell lines.

2.7 On the back end of the paper, when the authors apply kinase inhibitors to validate some of the claimed pathways, it would be nice for the reader to see the morphological effects of these inhibitors. And to relate the kinase induced shifts to the morphological heterogeneity that is the basis for the study driving, initial correlation analysis? At the end of the day, the proof is in the pudding.

R2.7 - We thank the reviewer for his very good point, and it would certainly improve the manuscript. We will attempt to source a visual illustration of the effect of kinase inhibitors on the breast cancer cells. However, the dataset we source this data from is publicly available, but unpublished and so our use is constrained by the terms of use of LINCs. We will contact the LINCS consortium to acquire permission and if they allow, we will certainly include them in our revised manuscript.

2.8 Finally, cell morphology regulation is a pretty foundational process of life. One therefore wonders whether the pathways the authors pulled out of their analysis work also in other cell types, beyond breast cancer cells? What if they pooled data from different cell types that cover the morphological state space more broadly?

R2.8 We thank the reviewer for this interesting point. We have observed that many if not most of the general processes identified, i.e. developmental pathways, extracellular matrix regulatory pathways and adhesion pathways, are already known to be associated with cell shape regulation and mechanotransduction in many different cell types. Thus, at the ‘big picture’ level, our findings hold across multiple cell types. However, the precise wiring of our network seems to be breast cancer specific. This is evidenced by the fact that when we try to use the LINCS data from other cell types to see if our network still holds in these contexts, we do not observe significant increase in changes in morphology when perturbing central nodes within our network compared to outside of our network. This is not unexpected: depending on the individual molecular background of each tissue and tumour type, signalling networks are known to be wired differently. Indeed, our method that uses the context- and cell feature- specific gene expression modules and the transcription factors that regulate them as a basis for extracting our cell shape signalling network allow for identification of exactly its specific wiring in the context used for training, i.e. the breast cancer cells. It would be very interesting to repeat our analysis on similar data on a different tissue type to identify parts of the network that seem to be identical versus those that differ. We have not been able yet to identify public systematic high content imaging data for a different tissue across multiple cell lines, but we will continue to look for such a dataset in the literature and through our network of collaborators. We will also explore the possibility of extracting such information from images from the TCGA to perform this analysis across patients of a specific cancer type, although admittedly we are not sure how feasible it would be to extract analogous features as the ones used for the breast cancer network from the images available. We will also add this point to the discussion.

Reviewer #2 (Significance):

The premise of this manuscript is very exciting and interesting: Is it possible to identify from a correlation of cell morphology and single cell gene expression the underlying cell signaling states that control morphology? Answers to this will begin to shed some light on the black box relation of morphology as an informant of cell states, which has been exploited by pathologists, physiologists, and cell biologists for more than a century, and which has seen a sharp revival recently thanks to deep learning, which is exceedingly good at finding correlations between data patterns.

This paper would have a broad audience in quantitative cell biology, systems biology, and perhaps also life data science and cancer (although the cancer aspect is marginal).

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

\*Summary***

In this work Barker et al. used computational approaches to analyze several existing data sets (including morphology and expression) in a common context of signaling-regulatory network that correlates with cell morphological features. They identified several pathways and associated transcription factors that their expression levels correlate with specific cell morphological features. The work thus has two main contributions. First, it provides a network of signaling pathways and regulons that may affect the morphological features of breast cancer cells. Second, the computational procedure can be general to study other systems.

\*Main comments***

3.1 I assume that in all analyses using the packages listed in the manuscript, some parameters need to be selected. The authors need to provide these details, and discuss whether the results are robust against parameter choice (at least to certain degree).

R3.1 We thank the reviewer for this comment. Parameters need to be selected in WGCNA and PCSF. In WGCNA they are selected based on the guidance given by the authors of the package, little significant variation in the results was observed when these were changed (i.e. the make-up of the gene expression modules naturally changed, but the processes enriched in the modules correlated to cell shape were the same).

PCSF is a more sensitive step because the best solutions to the sub-network identification problem are observed when the network edge weights are permuted over a number of iterations. Following this, the union of the produced array of networks is taken to be the solution. Obviously, biology is an inherently noisy system and so this formulation of the PCSF algorithm can capture latent network architecture that the deterministic variation cannot. This introduces extra parameters based on the requirement to introduce random noise to the network, along with the standard PCSF parameters (seen here: https://rdrr.io/github/IOR-Bioinformatics/PCSF/man/PCSF_rand.html) that are used to take into account of user variations in network degree distribution, edge-weight distribution, etc. It is normal for some tuning of parameters to be required for users to tailor their PCSF to their supplied network. We used degree distribution to gauge whether our network appeared to be of a biological ‘scale-free’ distribution and selected parameters based on that. This provides an affirmation that our resulting network is consistent with how we understand the topology of biological networks, and as a result the parameters selected are not arbitrary.

Nonetheless, we also tested variations in these parameters and found that although levels of significance in our validation would vary, the trends apparent from our validation did not (i.e., that targeting kinases within our network produced a larger effect on cell shape than those outside). From this we were assured that our conclusions mentioned in the discussion were robust to parameter selection. All details of parameters used are currently in our gitlab page, but we will additionally include them in the methods section.

3.2 Cells show some degree of heterogeneity both in cell expression and morphological features, which can be affected by many factors. Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) identified several subgroups of MD-MBA-231 cells with persistent (over generations) distinct morphology, expression profiles, and metastasis potential. Another possible main factor to cell morphology heterogeneity is cell cycle stage. I understand that the analyses in this work are limited by the types of data available, for example, the expression data are largely bulk. One exception might be the data shown in Fig 5. Besides giving the fold changes after kinase inhibitor treatment, the authors may also analyze the variance of cells before and after treatment to estimate the relative extent of cell-cell heterogeneity relative to the effect due to treatment.

R3.2 We thank the reviewer for the comment and suggestion. We will perform such an analysis and include this point in the discussion. However, to reassure the reviewer, we are not concerned about this affecting our analysis in a major way as, in data from high content microscopy experiments such as the ones we used, hundreds of cells are sampled and the resulting quantified phenotypes are represented by the average from single cells, after removing outliers. Similarly in the bulk RNAseq experiments the dominant cell phenotype/expression profile would be mainly represented in the data. We are therefore reasonably confident that both sets of data used from each cell line indeed represented the most common phenotype for that cell line.

3.3. As related to point 2, In Fig. 1B, I am surprised that cell cycle only correlates with cell area significantly, while one knows that cells undergo dramatic change during cell cycle. For example, cells would turn to be roundish for mitosis. How would the authors explain the results? Is it possible that there is sampling bias towards interphase cells?

R3.3 We thank the reviewer for this comment and apologise for the confusion. The y axis of Fig.1B relates to gene expression modules identified in the expression data. These were named based on any informative term that could be associated with the genes within the modules as implemented by gene set enrichment. The goal was to provide more informative names than the default module names that are based on colours. ‘Cell cycle’ as a term in Reactome is a particularly generalisable gene set and was applied to the gene expression module in question because it was the only informative term identified for it. This singular gene expression module does not represent all transcriptomic activity associated with the cell cycle process. Indeed, the term ‘Cell cycle’ was also enriched in the ‘Hedgehog off-state’ gene expression module (Supplementary table 5). As the enrichment is based only on the genes: HAUS8;MCM8;NCAPH2;MIS12;BIRC5;CENPM;SPDL1;FBXO5;TYMS;TUBB4A, which are not necessarily the major cell cycle-relevant genes, we agree that the name of the specific module is not ideal and can cause confusion so we will rename this module. We will also go over the naming of all the modules to ensure that the names are indeed representative of the module functions.

\*Minor comments***

3.4 In Fig 1B, I have trouble to understand the biological relevance of some module names, like "Green", "indianred4"?

R3.4 Our pipeline uses WGCNA which constructs gene expression modules completely from gene expression data. We named modules based on terms we could find associated with the genes within a module. Some modules did not have any informative terms associated with them and so we opted to keep the default name of those modules that WGCNA supplies (based on colours). We will attempt to make this clearer in our revised manuscript, by adding a better explanation, and renaming these modules to something that makes it clear that we could not assign a clear function such as non-annotated (NA) module 1,2,3 etc.

3.5 Fig 3B: I can't find a detailed explanation on how the combined score was calculated.

R3.5 Thank you for pointing this out. This is described in Chen et al. 2013 as part of the enrichR package for gene set enrichment analysis. We will add this detail in the methods section under “Quantification and Statistical Analysis“.

3.6 Some of the cell features in Fig 5A are not in Fig 1. Are they from the same analysis? Any explanation?

R3.6 As the two datasets were acquired in two completely different studies there isn’t a 1-1 correspondence of the phenotype features, however several of them essentially represent the same phenotype. For example, in Fig 5., cytoplasm area, cytoplasm perimeter, nucleus area, nucleus length, nucleus width and nucleus perimeter, are analogous to features in Fig.1, such as cell area, cell width to length, nucleus area, nucleus width to length. The intersection between the features in these two datasets is not exact however, and we use the features in Fig.5 not used in the network construction as a negative control. This allows us to show that our network is phenotype-specific to the morphology features it was trained on. We will clarify this in the manuscript.

3.7) It is interesting that the authors have identified a number of pathways known to be related to mechanosensing. Does the Hippo-YAP/TAZ pathway appear in their analysis?

R3.7 Yes, YAP1 is also significantly highly ranked in our network propagation of activated transcription factors in Fig.4 in both luminal- and basal- shaped cell lines. Furthermore, since submitting we have been experimenting with identifying subnetworks of our regulatory network using maximum-flow. Here we assess the interaction between the Rap1 module (given its centrality to our discussion) with NFkB and what is the most efficient ‘flow’ of information between these two nodes given our network. To our interest, we identify LATS2, DVL1 (genes within the Rap1 module), YAP1 and TAZ as key mediating factors between these nodes. This implicates the Hippo-YAP/TAZ pathway as being of particular importance in the interface of our identified gene expression module and our derived signalling network. As an illustration of this we include here one of the preliminary networks derived from this analysis.

Figure - Network describing maximum flow (top 20 edges) between Rap1 signaling module as the source node and NFKB1 as the target node. The super-node representing the gene expression module is coloured red (with the interface nodes used to embed it in the signaling network coloured blue) and NFKB1 coloured azure. Edge thickness indicates weight, which was used as the maximum capacity used in the max flow calculation.

We will go over the figures and move barplots and more technical information to the supplement to make space for more figures of this nature that better illustrate the processes involved in the regulation of cell shape as derived from our analysis.

Reviewer #3 (Significance):

Extensive studies link cell morphological features and cell expression states, with some important work from one of the authors (Chris Bakal). This topic gains further interest recently. For example, Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) demonstrated that cell shape encodes metastasis potential. Wang et al. (Sci. Adv. 2020 6 (36): eaba9319) traced cell dynamics in cell feature space. Given the context, the work of Barker et al. is a timely study to establish a cell shape-signaling network from integrated analysis of several different types of data. While some previous studies have related the NFkB network and cell morphology, this work further provides unbiased analysis on the relation between cell morphological features and multiple pathways/transcription factors. It is interesting, for example, that the study identifies the correlation between the Rap1 pathway and cell morphology, which was not well studied previously. As the authors acknowledged, there are some limitations of their approach. For example, the relations identified are correlative instead of causal without further verification. The resultant network may have sampling bias. Despite these limitations, I suggest that this work will be a nice contribution to the field and can provide a basis for further studies.

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Referee #3

Evidence, reproducibility and clarity

Summary

In this work Barker et al. used computational approaches to analyze several existing data sets (including morphology and expression) in a common context of signaling-regulatory network that correlates with cell morphological features. They identified several pathways and associated transcription factors that their expression levels correlate with specific cell morphological features. The work thus has two main contributions. First, it provides a network of signaling pathways and regulons that may affect the morphological features of breast cancer cells. Second, the computational procedure can be general to study other systems.

Main comments

1) I assume that in all analyses using the packages listed in the manuscript, some parameters need to be selected. The authors need to provide these details, and discuss whether the results are robust against parameter choice (at least to certain degree).

2) Cells show some degree of heterogeneity both in cell expression and morphological features, which can be affected by many factors. Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) identified several subgroups of MD-MBA-231 cells with persistent (over generations) distinct morphology, expression profiles, and metastasis potential. Another possible main factor to cell morphology heterogeneity is cell cycle stage. I understand that the analyses in this work are limited by the types of data available, for example, the expression data are largely bulk. One exception might be the data shown in Fig 5. Besides giving the fold changes after kinase inhibitor treatment, the authors may also analyze the variance of cells before and after treatment to estimate the relative extent of cell-cell heterogeneity relative to the effect due to treatment.

3) As related to point 2, In Fig. 1B, I am surprised that cell cycle only correlates with cell area significantly, while one knows that cells undergo dramatic change during cell cycle. For example, cells would turn to be roundish for mitosis. How would the authors explain the results? Is it possible that there is sampling bias towards interphase cells?

Minor comments

4) In Fig 1B, I have trouble to understand the biological relevance of some module names, like "Green", "indianred4"?

5) Fig 3B: I can't find detailed explanation on how the combined score was calculated.

6) Some of the cell features in Fig 5A are not in Fig 1. Are they from the same analysis? Any explanation?

7) It is interesting that the authors have identified a number of pathways known to be related to mechanosensing. Does the Hippo-YAP/TAZ pathway appear in their analysis?

Significance

Extensive studies link cell morphological features and cell expression states, with some important work from one of the authors (Chris Bakal). This topic gains further interest recently. For example, Wu et al. (Sci Adv 2020, 6 (4): eaaw6938) demonstrated that cell shape encodes metastasis potential. Wang et al. (Sci. Adv. 2020 6 (36): eaba9319) traced cell dynamics in cell feature space. Given the context, the work of Barker et al. is a timely study to establish a cell shape-signaling network from integrated analysis of several different types of data. While some previous studies have related the NFkB network and cell morphology, this work further provides unbiased analysis on the relation between cell morphological features and multiple pathways/transcription factors. It is interesting, for example, that the study identifies the correlation between the Rap1 pathway and cell morphology, which was not well studied previously. As the authors acknowledged, there are some limitations of their approach. For example, the relations identified are correlative instead of causal without further verification. The resultant network may have sampling bias. Despite these limitations, I suggest that this work will be a nice contribution to the field and can provide a basis for further studies.

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Referee #2

Evidence, reproducibility and clarity

The authors combine single cell morphology and gene expression data to identify signaling activities implicated in the control of cellular morphogenesis. They describe a reasonable bioinformatics pipeline from gene expression shifts between two morphological phenotypes to pathways, then to common transcription factors to signaling. As far as I can assess the situation (I am not familiar with all the tools they use) the proposed pipeline works convincingly. However, I am concerned that the logic underlying this analysis is only partially valid. The link between signaling and morphology may be more direct than via TF-based gene expression regulation. Many signals (and many of the kinases the authors test for validation) are implicated in morphology control as direct upstream regulators of cytoskeleton dynamics and adhesion. This also applies to the GTPase Rap1, which the authors fish out as the most differentially expressed signal between two types of morphologies. In addition to the indirect effect of Rap1 on morphology via NFKB regulation suggested by the authors, Rap1 will affect morphology probably very directly through activation of Rac -> F-actin and RIAM -> nascent adhesions. At minimum, the authors should discuss this complexity as a caveat of their approach. And dependent on the impact the authors hope to have with this story, I believe they should experimentally resolve the ambiguity of direct vs indirect signaling for some of their key interpretations.

In defense to the presented premise, the authors start out by looking for correlation between gene expression and morphology, and they find some signal. Correlation analysis, especially in large data sets, tends to be pretty robust and specific, even on presence of strong confounders. Thus, even though the correlation expression-morphology, which points indirectly at morphology-regulating signaling modules, is likely to be super-imposed by direct morphology-regulating signaling pathways the proposed approach will not be able to detect, the presented analysis is valuable, in principle.

That said, I have a number of substantial concerns also with the implementation and presentation of the approach. First, on the presentation side, for a paper that talks about cell morphology it is strange to have not a single figure panel showing an image of cells, or at least cell outlines. As a reader I would like to get visual impression of how different a high vs low Rap1 gene expresser is, for example. Along the same lines, it is not quite clear to me when the authors collate entire cell lines into a single phenotype, do they switch then to population-based analysis? That is, for example the volcano plots in 2B,C are they representing an average gene expression shift? How heterogeneous are the morphological signals? Are the correlations between gene expression and morphology computed with single cell data as the basis? Could the volcano plots be sharpened by accounting for the single cell variation in morphology instead of lumping the cells into two morphological classes? On the back end of the paper, when the authors apply kinase inhibitors to validate some of the claimed pathways, it would be nice for the reader to see the morphological effects of these inhibitors. And to relate the kinase induced shifts to the morphological heterogeneity that is the basis for the study driving, initial correlation analysis? At the end of the day, the proof is in the pudding.

Finally, cell morphology regulation is a pretty foundational process of life. One therefore wonders whether the pathways the authors pulled out of their analysis work also in other cell types, beyond breast cancer cells? What if they pooled data from different cell types that cover the morphological state space more broadly?

Significance

The premise of this manuscript is very exciting and interesting: Is it possible to identify from a correlation of cell morphology and single cell gene expression the underlying cell signaling states that control morphology? Answers to this will begin to shed some light on the black box relation of morphology as an informant of cell states, which has been exploited by pathologists, physiologists, and cell biologists for more than a century, and which has seen a sharp revival recently thanks to deep learning, which is exceedingly good at finding correlations between data patterns.

This paper would have a broad audience in quantitative cell biology, systems biology, and perhaps also life data science and cancer (although the cancer aspect is marginal).

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Referee #1

Evidence, reproducibility and clarity

The submitted manuscript 'Identification of phenotype-specific networks from paired gene expression-cell shape imaging data' of Barker et al. uses a convolute of different bioinformatics tools (see Key Resource Table) to analyze reported RNA sequencing data and to correlate derived pathways with imaging features of breast cancer cell lines based on specific pathway constructions. The thin red line of the data presentation in the manuscript is not obvious.

Major concerns:

1. The main biological 'finding' of the study RAP1 'as a potential mediator between the sensing of mechanical stimuli and regulation of NFkB activity' is reported and therefore the assumption 'how exactly extra-cellular mechanical cues are sensed by the cell and passed on to NFkB in breast cancer is not understood' is misleading. Please review: https://www.nature.com/articles/ncb2080 (human breast cancers with NF-κB hyperactivity show elevated levels of cytoplasmic Rap1. Similar to inhibiting NF-κB, knockdown of Rap1 sensitizes breast cancer cells to apoptosis) https://pubmed.ncbi.nlm.nih.gov/17510404/ (RAP1 is a crucial element in organizing acinar structure and inducing lumen formation), and https://pubmed.ncbi.nlm.nih.gov/21429211/. Besides, Fig. 2 and 3 are unrelated to this main statements.
2. The spotted RAP1 (by TFs JARD2 and RUNX2) finding is not obvious without Fig. 4 results, a network propagation of functional TFs in differentially activated processes (basal vs. luminal) in the cell shape regulatory network. Please show that RAP1 could be not identified without the network based on TF and DEG only.
3. More complex fluorescence phenotypes are available and do not match the complexity of the RNASeq data, data input and pathway construction with only 10 simple cell shape features. Conversely, relative 'monoclonal' breast cancer cell lines may are the only application for this workflow. Image features Fig. 1 and 5 do not match, with Fig. 5 being a rather indirect 'proof' of usability.
4. Fig. 1a has not achieved a visual descriptive state and asking a lot.

Significance

The 'Review Commons' efficiently facilitates the reviewing process for the corresponding journals due to the broader 'audience'. On the other hand, authors face less restrictions and pressure for the same reason. Although I really like the idea of pulling the reviews upstream into the preprint process, I would like to answer here also with a kind of pre-review to avoid entering partly immature manuscript to 'Review Commons'. Review Commons might install an automated 'sanity check' of manuscripts in the future to keep the quality of submissions higher?

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Reply to the reviewers

Review Commons Reviews for Refereed Preprint RC-2021-00693

Ferrari G. et al., DLL4 and PDGF-BB regulate migration of human iPSC-derived skeletal myogenic progenitors.

Reviewer #1 (Evidence, reproducibility and clarity): Summary:

The paper presented by Ferrari et al., aims to improve the migration capacity of hiPSC- derived myogenic progenitors. For this purpose, the authors used a previously published well characterized hiMPs model and focussed on the modulation of NOTCH and PDGF signaling pathways. The rational to target these pathways was based on muscle cells migrations molecular events observed during developmental described in the literature.

Major comments: Are the key conclusions convincing?

This is a very interesting paper. Few clarifications as suggested below need to be done before being fully convincing. Enrichment test and heat maps and the network analysis are not well explained in terms of which genes were selected and why, and in terms of which gene set were selected and why. In some cases, the information may be given in the paper, but it is not easy for the reader to find it. It should be stated more clearly. For example, in Fig2C why these eight were chosen for the heat maps and why not other genes known to be involved in myogenesis, cell migration etc. Similar comment for figure 3 A, D and G. Another example, in Fig 2E, on what basis are some gene sets chosen to be shown in this figure when there are many more significant in the supplementary table.

We thank the Reviewer for their positive feedback and for this comment. Although some answers to the queries could be found within the figure legends, we agree that figures could have been more self-explanatory, and we will amend them accordingly. We will also add additional information into the main text to clarify those specific points.

In response to the specific queries:

• All enrichment heat maps were generated from GO lists or KEGG pathways.
• 2C: these were chosen instead of other myogenic or cell migration markers for consistency with our previous study (Figure 2C in Gerli et al Stem Cell Reports 2019).
• 3A, D, G: details of the GO lists used to generate heat maps were available in the relative figure legend.
• 2E: enrichment pathways – we listed pathways shared between at least 2 of the three groups and with relevance to cellular migration.

  Figure 4F is impossible to interpret without a clear description of how the subnetwork is extracted, was a list of gene list submitted to string, if so which genes and why? Secondly, why are there many nodes with no edges? Is it all of the nodes that are in that GO-Term, if so it needs to be clarified? Was this the most strongly deregulated go-Term according to string analysis?

We thank the Reviewer for this comment. This specific GO list was selected for its highly relevant title/topic, i.e.: “positive regulation of cell migration”. Details on this point could also be found in the specific figure legend, where we specified how the network is extracted and constructed. There are several nodes with no edges as the edges represent predicted functional association and therefore, a lack of edges suggests a lack of interaction.

Figure 4 B, C, D and E: (1) The authors should clarify what figure 4B is? Is 1,2,3,4 different time point? Treated or untreated cells?

We apologise with the Reviewer for not having provided enough information on this point. 1,2,3 and 4 are four sequential time points of untreated cells. We will amend the figure to make this clearer.

(2) Figure C: Is the graph showing the cell distribution of both treated and untreated cells? If yes is it possible to give a different shape for the control cells and see if indeed more control green shape would be observed in this plot? (In the supplementary data there is the distribution showing the treated v untreated, but the clusters are not visible)

We thank the Reviewer for this helpful comment. We agree that this will increase the quality of the figure. We will distinguish treated and control cells within figure 4C by replacing dots with different shapes for treated and untreated samples.

(3) Would it be possible to take some of the parameters in Figure 4D and show the distribution in treated vs untreated and perform the statistical analysis? (eg is there a significant difference for the parameter total distance between control and treated?). Or, may be just show some of the results in figure S4C and E in the main text.

We thank the Reviewer for this comment. We agree that it will be better to move S4C into the main figure and we will action this point in the revised version of the manuscript.

(4) Why pooling the 3 independent experiment together? Looking at the data in Figure S4, it seems that one treated sample is very similar to the control, thus weakening the conclusion. The replicates in this figure are biological replicates. Yet the papers present 4/5 different cell lines, so why only 3 of them are used here? Is there some explanation regarding the outsider (cell line age, number of division etc). Might be worth adding data from the other cell lines (1 or 2 more).

We thank the Reviewer for this point. The experiment shown in figure S4E has been performed with one cell line (N5) and independent experimental replicates were assessed for the statistical analysis. We are not sure why there appears to be an outlier in some cases, and this is why it was important to replicate this experiment three times. However, we will also repeat this experiment with another cell line applying more stringent conditions to strengthen this point.

(5) Figure 4 H and I: What are the statistic actually comparing: treated v untreated for each cell lines or different cell lines against each other? If the former, then how is it possible to have a 139 fold change with such a weak p value of 0.042? If the latter, then why is a p-value given for each of the 3 cell lines? Also, the number and source of replicates is unclear - N=3 is stated, so was each cell line done in triplicate? If so, how many fields per replicate?

We are happy to clarify this point for the Reviewer. The statistical analysis compares treated vs. untreated samples within the same genotype. The high fold change observed is likely due to the large standard deviation of the dataset, which was also highlighted as raw data in the figure panel (bottom part of each picture in white colour font). For this reason, we have repeated this experiment multiple times and validated it across three independent cell lines.

Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. It would important to also show the migratory capacity of these cells in vivo.

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. Human muscle cells engraftment and tracking in immunodeficient mice could be easily done. Engrafted muscle can be harvested 2-3 weeks after engraftment, and measurement of the distance from the engraftment point could be done (Site of injection could be labelled with tattoo die). This would be a month/month and half of work. Immunodeficient mice would cost around £1500 (n=6 mice per group => total of 12 mice) plus the cost of housing.

Are the data and the methods presented in such a way that they can be reproduced? Are the experiments adequately replicated and statistical analysis adequate? See comments in first paragraph. The authors should probably be able to answer easily to the different concerns raised above.

We thank the Reviewer for these comments. We agree that the suggested in vivo experiment might strengthen our work and we are currently sourcing all required materials to perform it. Additionally, we will perform a similar, quasi-vivo, experiment to study migration in a species-specific setting by delivering cells in 3D models in vitro (e.g. Maffioletti SM et al., Cell Reports 2018). This strategy will provide a solid alternative to the in vivo assay, in the eventuality that the xenogeneic setting will limit the resolution of the proposed transplantation experiment.

Minor comments: typo "Onthology" should be "Ontology" in figure 2E. Some of the data in Figure S4E should be moved to the main text.

Thank you for highlighting these minor comments. We will correct the typo and move data from figure S4 into the main figure 4.

Reviewer #2 (Evidence, reproducibility and clarity): In this manuscript, Ferrari and colleagues provide solid data indicating that the Notch ligand DLL4 and PDGF-BB regulate the migration of myogenic progenitors derived from human pluripotent stem cells (PSC). These studies built from recent work by the same group (Gerli et al, Stem Cell Reports, 12:461, 2019), in which the authors documented that Notch and PDGF-BB signaling enhances migration and expression of stem cell markers while inducing perivascular cell features in muscle satellite cells. Here the authors perform similar in vitro studies in PSC-derived myogenic progenitors and conclude that the same effect is observed in this population of cells. The results are clear and well presented.

Throughout the manuscript, the authors emphasize the importance of such findings for the future therapeutic application of a PSC-based therapy to treat patients with muscular dystrophy since multiples skeletal muscles need to be targeted in this group of diseases. Unfortunately, the authors do not provide transplantation data. The results would be highly meaningful if they show that observed in vitro changes (transcriptomes and chamber assay) result in meaningful migration in vivo using the systemic delivery, but as it is, the data do not support the claims and conclusions.

We thank Reviewer 2 for their comments. We were pleased to read that they found our study and data solid, clear and well presented. Although we agree with the Reviewer that in vivo evidence would strengthen our findings, we would like to highlight that our study did not aim to be a translational investigation of the therapeutic potential of treated hPSC derivatives for muscle cell therapy (we believe our manuscript’s title reflects this). We see this work more as a foundational study to establish the required evidence for future, follow up transplantation studies focused on the therapeutic potential of this approach (something requiring a dedicated project, funding and months/years of work).

Moreover, we believe that xenogeneic transplants are of limited use to investigate a complex species-specific phenomenon such as transendothelial cell migration. For this very reason we moved back to intraspecific transplantsin past studies (e.g.. Tedesco et al Sci Transl Med 2012). However, as a key aim of our study is to obtain data specific to human cells and given that we already performed mouse-in-mouse in vivo intra-arterial delivery experiments using DLL4 and PDGFBB treated primary cells in Gerli et al. Stem Cell Reports 2018, we are therefore proposing and planning to:

• Test transendothelial migration with another quasi-vivo microfluidic assay orthogonal to the reported transwell experiments. This will model intraspecific (i.e., human-in-human) transendothelial migration under flow conditions.
• Assess evidence of migration in human 3D muscles setting up a novel invasion assay in our in vitro 3D muscle models.
• Perform intramuscular delivery of treated vs. untreated cells as per Reviewer 1 request to assess migration in skeletal muscle in vivo. This approach will optimise in vivo experiments in a 3Rs compliant fashion, avoiding invasive procedures in animals to study intravascular delivery.

Reviewer #2 (Significance): Significance is limited if only in vitro data are provided. However if the authors are able to show enhanced engraftment upon systemic transplantation of human PSC-derived myogenic progenitors upon DLL4 and PDGF-BB treatment, the significance would be high.

Please see our reply to the previous point.

In terms of existing literature, there are publications reporting systemic delivery of murine PSC-derived myogenic progenitors as well as transcriptome and in vitro migration studies. It would probably be appropriate to cite them.

We apologies to the Reviewer for this oversight. We will add the following papers which include systemic delivery of murine PSC-derived myogenic progenitors as well as transcriptome and migration studies: Matthias N et al., Exp Cell Res 2015; Incitti T et al., PNAS 2019.

If systemic engraftment is observed, the manuscript would be of interest to the skeletal muscle and stem cell biology/regenerative medicine community.

Please see our reply to the initial point.

Reviewer #3 (Evidence, reproducibility and clarity):

In this manuscript, the authors exploited the signal-mediated activation of NOTCH and PDGF pathways, by one week-long delivery of DLL4 and PDGF-BB to cultures of hiPSC-derived myogenic progenitors in vitro, to improve their migration ability. They performed transcriptomic and functional analyses across human and mouse primary muscle stem cells and human hiPSC-derived myoblasts, including genetically corrected hiPSC derivatives, to show that DLL4 and PDGF-BB treatment modulates pathways involved in cell migration, including enhanced trans-endothelial migration in transwell assays.

The increased migratory ability, and in particular enhancing extravasation, is a fundamental property required for optimal performance of hiPSC myogenic derivatives, upon their intravascular delivery; hence, the finding reported here are of extremely high potential interest in term of solution of one of the major bottle-neck of cell therapy. However, there are important issues that need to be resolved by the authors with additional experimentation, that I recommend performing, in order to improve this manuscript.

We sincerely thank the Reviewer for acknowledging the extremely high relevance and potential of our paper for muscle gene and cell therapies and for providing constructive feedback to improve our manuscript.

1) The most critical issue here is that the authors fail to provide evidence that DLL4/PDGF-BB-treated cultures of hiPSC-derived myogenic progenitors do not lose their myogenic potential and are able to form myotubes, upon interruption of treatment. It would be also important to determine when (how many days after withdrawal of DLL4/PDGF-BB) the full myogenic properties of these cells are recovered. From the RNAseq datasets shown by the authors, it appears that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express the key genes of myogenic identity (MyoD) and early differentiation (myogenin), while expressing genes of mesenchymal/vessel-derived lineages. It is imperative that the authors show that these changes are reversible, upon withdrawal of DLL4/PDGF-BB. This should be show by an unbiased transcriptomic analysis (RNAseq) of hiPSC-derived myoblasts after withdrawal of DLL4/PDGF-BB, that should be integrated with functional evidence showing that these cells can resume their ability to form differentiated myotubes, upon exposure to myogenic culture cues in vitro.

We thank the Reviewer for this comment. We agree that this is an important and feasible experiment which will add important information to our work. We performed similar work in our previous study and already observed phenotype reversion of treated cells upon release of the stimuli within a few passages in cultures. However, we agree that this requires systematic assessment and quantification. To this aim, we will assess the reversibility of the DLL4 & PDGF-BB effect by stopping treatment at day 7 and then assessing skeletal myogenic differentiation capacity of target cells at sequential passages and time points post-treatment. Analysis of the differentiation index at different time points will provide functional evidence on the myogenic potential of hiPSC-derived myogenic progenitors post-withdrawal of DLL4 & PDGF-BB. We believe that the Reviewer’s suggestion for transcriptomic analysis via RNA-seq might be overly costly for the purpose of identifying the myogenic potential of treated cells post-withdrawal of treatment, and that qPCR panels alongside immunofluorescence staining may be sufficient.

2) A parallel evidence in vivo should be also provided, showing that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express MyoD and myogenin when delivered intravascularly, but regain their expression after they have crossed the vessel endothelium and have entered the skeletal muscles.

We thank the Reviewer for suggesting this experiment. We agree that this would be a very interesting point to address; however, it might be very challenging to address this question with the proposed in vivo experiment. Nonetheless, we believe that with a combination of in vitro and in vivo assays we will be able to satisfactorily answer the question: Do DLL4 and PDGF-BB-treated myogenic progenitors re-gain myogenic potential upon entering skeletal muscle tissue? To this aim, we aim to analyse muscles following intramuscular transplantation of treated and untreated cells. Moreover, to model intra-vascular delivery and have high resolution imaging, we aim to adapt a microfluidic platform to perform trans-endothelial assays and selectively differentiate cells that successfully cross the blood vessel layer. Although likely to be very challenging, we will attempt to capture or stain those very cells in order to assess the expression of myogenic markers as requested by the Reviewer.

If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal.

We thank the Reviewer for this constructive feedback and for seeing the great potential of our work in terms of basic and translational biology. We assume there was a typo in the sentence in brackets with a missing “as” (“..not demonstrated as in previous work...”): we indeed demonstrated the effect of DLL4 and PDGFBB in vivo extensively in our previous work.

Other points:

• Fig. 2A. it looks like there are some outlier RNAseq sample replicates that might negatively impact at the statistical level on the subsequent analysis. This issue is likely due to the heterogeneity of the samples (both untreated and treated) and could be resolved by replacing outlier samples with new replicates.

We thank the Reviewer for this comment. Although we agree that replacing those samples with new replicates might improve our statistical analyses, this will be financially challenging at this stage and perhaps also not completely reflecting the real variability of the experimental setup.

• Along the same line as above, sample heterogeneity following treatment might be resolved by a better understanding of optimal doses of DLL4/PDGF-BB and time of exposure, which I recommend the authors to define by additional experiments.

We thank the Reviewer for this comment. This is a potentially interesting experiment, which we have not performed as we took advantage of previous knowledge and dose-response on primary mouse and human myoblasts. Overall, we believe that this experiment might not be strictly required at this stage, given that we have already solid evidence of response in hiMPs with a defined concentration and exposure time of DLL4 and PDGFBB.

Reviewer #3 (Significance):

If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal and could be interesting for a wide audience in regenerative medicine.

We thank the Reviewer once again for this constructive feedback and for seeing the great potential of our work in terms of basic and translational biology, as well as for regenerative medicine.

Please note that the following statement will be added to the Acknowledgements section of our revised manuscript: "For the purpose of Open Access, the author has applied a CC BY public copyright licence to any Author Accepted Manuscript version arising from this submission. This work was supported by the Francis Crick Institute which receives its core funding from Cancer Research UK, the UK Medical Research Council, and the Wellcome Trust (FC001002)".

Once again, we sincerely thank all Reviewers for their positive, constructive and insightful comments, which motivate us to further improve our work. We also thank the Review Commons editorial team for guidance and assistance.

Prof. Francesco Saverio Tedesco, University College London and The Francis Crick Institute, London, UK.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors exploited the signal-mediated activation of NOTCH and PDGF pathways, by one week-long delivery of DLL4 and PDGF-BB to cultures of hiPSC-derived myogenic progenitors in vitro, to improve their migration ability. They performed transcriptomic and functional analyses across human and mouse primary muscle stem cells and human hiPSC-derived myoblasts, including genetically corrected hiPSC derivatives, to show that DLL4 and PDGF-BB treatment modulates pathways involved in cell migration, including enhanced trans-endothelial migration in transwell assays. The increased migratory ability, and in particular enhancing extravasation, is a fundamental property required for optimal performance of hiPSC myogenic derivatives, upon their intravascular delivery; hence, the finding reported here are of extremely high potential interest in term of solution of one of the major bottle-neck of cell therapy. However, there are important issues that need to be resolved by the authors with additional experimentation, that I recommend performimg, in order to improve this manuscript.

1) The most critical issue here is that the authors fail to provide evidence that DLL4/PDGF-BB-treated cultures of hiPSC-derived myogenic progenitors do not lose their myogenic potential and are able to form myotubes, upon interruption of treatment. It would be also important to determine when (how many days after withdrawal of DLL4/PDGF-BB) the full myogenic properties of these cells are recovered. From the RNAseq datasets shown by the authors, it appears that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express the key genes of myogenic identity (MyoD) and early differentiation (myogenin), while expressing genes of mesenchymal/vessel-derived lineages. It is imperative that the authors show that these changes are reversible, upon withdrawal of DLL4/PDGF-BB. This should be show by an unbiased transcriptomic analysis (RNAseq) of hiPSC-derived myoblasts after withdrawal of DLL4/PDGF-BB, that should be integrated with functional evidence showing that these cells can resume their ability to form differentiated myotubes, upon exposure to myogenic culture cues in vitro.

2) A parallel evidence in vivo should be also provided, showing that DLL4/PDGF-BB-treated hiPSC-derived myoblasts do not express MyoD and myogenin when delivered intravascularly, but regain their expression after they have crossed the vessel endothelium and have entered the skeletal muscles. If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal.

Other points:

• Fig. 2A. it looks like there are some outlier RNAseq sample replicates that might negatively impact at the statistical level on the subsequent analysis. This issue is likely due to the heterogeneity of the samples (both untreated and treated) and could be resolved by replacing outlier samples with new replicates.
• Along the same line as above, sample heterogeneity following treatment might be resolved by a better understanding of optimal doses of DLL4/PDGF-BB and time of exposure, which I recommend the authors to define by additional experiments.

Significance

If these experiments could firmly demonstrate that DLL4/PDGF-BB-treatment reversibly promotes migratory properties of hiPSC-derived myoblasts (as predicted, but not demonstrated in previous works from the same group, using mouse or human primary muscle stem cells - Cappellari et al. 2013; Gerli et al. 2019), then this work could be a great interest in term of basic and translational biology and clearly suitable for publication in a top journal and could be interesting for a wide audience in regenerative medicine.

Expertise of this reviewer:

Muscle regeneration; Muscular Dystrophies; Signaling and Epigenetics

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Ferrari and colleagues provide solid data indicating that the Notch ligand DLL4 and PDGF-BB regulate the migration of myogenic progenitors derived from human pluripotent stem cells (PSC). These studies built from recent work by the same group (Gerli et al, Stem Cell Reports, 12:461, 2019), in which the authors documented that Notch and PDGF-BB signaling enhances migration and expression of stem cell markers while inducing perivascular cell features in muscle satellite cells. Here the authors perform similar in vitro studies in PSC-derived myogenic progenitors and conclude that the same effect is observed in this population of cells. The results are clear and well presented.

Throughout the manuscript, the authors emphasize the importance of such findings for the future therapeutic application of a PSC-based therapy to treat patients with muscular dystrophy since multiples skeletal muscles need to be targeted in this group of diseases. Unfortunately, the authors do not provide transplantation data. The results would be highly meaningful if they show that observed in vitro changes (transcriptomes and chamber assay) result in meaningful migration in vivo using the systemic delivery, but as it is, the data do not support the claims and conclusions.

Significance

Significance is limited if only in vitro data are provided. However if the authors are able to show enhanced engraftment upon systemic transplantation of human PSC-derived myogenic progenitors upon DLL4 and PDGF-BB treatment, the significance would be high.

In terms of existing literature, there are publications reporting systemic delivery of murine PSC-derived myogenic progenitors as well as transcriptome and in vitro migration studies. It would probably be appropriate to cite them.

If systemic engraftment is observed, the manuscript would be of interest to the skeletal muscle and stem cell biology/regenerative medicine community.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The paper presented by Ferrari et al., aims to improve the migration capacity of hiPSC- derived myogenic progenitors. For this purpose, the authors used a previously published well characterized hiMPs model and focussed on the modulation of NOTCH and PDGF signaling pathways. The rational to target these pathways was based on muscle cells migrations molecular events observed during developmental described in the literature.

Major comments:

• Are the key conclusions convincing? This is a very interesting paper. Few clarifications as suggested below need to be done before being fully convincing. Enrichment test and heat maps and the network analysis are not well explained in terms of which genes were selected and why, and in terms of which gene set were selected and why. In some cases, the information may be given in the paper, but it is not easy for the reader to find it. It should be stated more clearly. For example, in Fig2C why these eight were chosen for the heat maps and why not other genes known to be involved in myogenesis, cell migration etc. Similar comment for figure 3 A, D and G. Another example, in Fig 2E, on what basis are some gene sets chosen to be shown in this figure when there are many more significant in the supplementary table. Figure 4F is impossible to interpret without a clear description of how the subnetwork is extracted, was a list of gene list submitted to string, if so which genes and why? Secondly, why are there many nodes with no edges? Is it all of the nodes that are in that GO-Term, if so it needs to be clarified? Was this the most strongly deregulated go-Term according to string analysis? Figure 4 B, C, D and E:

(1) The authors should clarify what figure 4B is? Is 1,2,3,4 different time point? Treated or untreated cells?

(2) Figure C: Is the graph showing the cell distribution of both treated and untreated cells? If yes is it possible to give a different shape for the control cells and see if indeed more control green shape would be observed in this plot? (In the supplementary data there is the distribution showing the treated v untreated, but the clusters are not visible)

(3) Would it be possible to take some of the parameters in Figure 4D and show the distribution in treated vs untreated and perform the statistical analysis? (eg is there a significant difference for the parameter total distance between control and treated?). Or, may be just show some of the results in figure S4C and E in the main text.

(4) Why pooling the 3 independent experiment together? Looking at the data in Figure S4, it seems that one treated sample is very similar to the control, thus weakening the conclusion. The replicates in this figure are biological replicates. Yet the papers present 4/5 different cell lines, so why only 3 of them are used here? Is there some explanation regarding the outsider (cell line age, number of division etc). Might be worth adding data from the other cell lines (1 or 2 more).

(5) Figure 4 H and I: What are the statistic actually comparing: treated v untreated for each cell lines or different cell lines against each other? If the former, then how is it possible to have a 139 fold change with such a weak p value of 0.042? If the latter, then why is a p-value given for each of the 3 cell lines? Also, the number and source of replicates is unclear - N=3 is stated, so was each cell line done in triplicate? If so, how many fields per replicate?

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. It would important to also show the migratory capacity of these cells in vivo. -Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. Human muscle cells engraftment and tracking in immunodeficient mice could be easily done. Engrafted muscle can be harvested 2-3 weeks after engraftment, and measurement of the distance from the engraftment point could be done (Site of injection could be labelled with tattoo die). This would be a month/month and half of work. Immunodeficient mice would cost around £1500 (n=6 mice per group => total of 12 mice) plus the cost of housing.
• Are the data and the methods presented in such a way that they can be reproduced? Are the experiments adequately replicated and statistical analysis adequate?

See comments in first paragraph. The authors should probably be able to answer easily to the different concerns raised above.

Minor comments:

typo "Onthology" should be "Ontology" in figure 2E. Some of the data in Figure S4E should be moved to the main text.

Significance

Describe the nature and significance of the advance, existing literature, audience: Generating iPSC cell lines with an improved capacity to migrate will be of high interest for the neuromuscular field, and could be a potential therapeutic strategy applicable for many neuromuscular disorders.

Muscle cell engraftment is quite challenging as the capacity of these cells to populate different muscles is very poor. Improving the cell migration, survival and proliferation may thus help to improve the muscle cell engraftment strategy.

Expertise:

I have an expertise in neuromuscular disorders, muscle stem cells (human and murine, in vitro and in vivo), as well as an expertise in omics analysis.

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Reply to the reviewers

Point-by-point response to reviewer comments

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Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In the current manuscript, Millarte et al reports a novel role of Rabaptin5 in selectively clearing damaged endosomes via canonical autophagy. They have identified FIP200 as a novel interactor of Rabaptin5 under basal conditions using yeast-two hybrid screening and further confirmed the interaction of Rabaptin5 with FIP200 with immunoprecipitation. They next used Chloroquine and monitored colocalization of the Rabaptin5 with WIPI2, ATG16L1 and LC3B to demonstrate the potential interaction of Rabaptin5 with the autophagic machinery. They have primarily used Gal-3 as a marker of membrane damage after 30 minutes of Chloroquine treatment. In order to further elucidate the role of Rabaptin5 in autophagic induction mediated by Chloroquine, they have silenced Rabaptin5, FIP200, ULK1 and ATG13 and observed a decrease in the number of LC3 or WIPI2 autophagosome formation. Based on these observations they tested if Rabaptin5 interacts with ATG16L1 upon Chloroquine treatment and confirmed their interaction with potential interaction sites of both Rabaptin5 with ATG16L1 with IP. The authors confirmed the interaction of Rabaptin5 with ATG16L1 by complementing the KO line with the mutant form of Rabaptin5 containing alanine residues in its consensus motif. Finally, they have used Salmonella and SCV as a model to study the role of Rabaptin5 in endomembrane damage and monitored a 50% decrease in the removal of Salmonella in Rabaptin5 KO or KD cells.

Major concerns One of the major concerns is the membrane damage reported by chloroquine which is known to induce lysosomal swelling and further targeting of the swollen compartments to degradation by direct conjugation of LC3 onto single membrane as a form of non-canonical autophagy. The evidence regarding membrane damage by Gal3 colocalization on the Rabaptin5 vesicles is preliminary. As suggested by the authors the canonical autophagy pathway recognizing damaged membranes recruits also ALIX to the damaged membrane which was not observed in Supplementary Figure 2. The link to membrane damage by chloroquine and monensin with Rabaptin5 is not convincing as there is not sufficient evidence of membrane damage. In relation to this issue authors should consider using other damage markers as Gal8, p62 or NDP52 to provide additional claim with respect to membrane damage induced by chloroquine.

To expand on the question of CQ treatment damaging early endosomes, we also tested for Gal8 on Rabaptin5-positive enlarged endosomes and quantified the fraction of Rabaptin5-positive rings positive for Gal3 and Gal8 after 30 min of CQ treatment. We propose to include this data in Figure 2:

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We have tested the importance of Gal3 and p62 by siRNA-mediated knockdown where we found a robust inhibition of induction of WIPI2 puncta with CQ, but not with Torin1. Formation of LC3 puncta was less reduced, similar to knockdowns of FIP200, ATG13, or Rabaptin5.

We propose to add these knockdown experiments as a supplementary figure:

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One of the main claims here is that Rabaptin5 regulates the targeting of damaged endosomes to autophagy. Clearly, these are early endosomes as stated in the abstract. However, the evidence presented here showing these are early endosomes is not convincing. Analysing Gal3 and Gal8 positive vesicles that are Rabaptin5 positive and an early endosomal marker will be important in this context. For example, there need to be additional evidence showing that early endosomes are targeted to autophagy. Is the degradation of TfR affected by this targeting? Did the authors look at the effect of Bafilomycin A1? If this process affects exclusively early endosomes, it should be BafA1 independent. This will direct more into the cellular function of this process.

Rabaptin5 is a bona fide marker of Rab5-positive early sorting endosomes. As a control, we confirmed colocalization of Rabaptin5 with transferrin receptor, another endosomal marker, on CQ-induced rings (Fig. 2B). We now also analyzed swollen endosomes with triple-staining for Rabaptin5, transferrin receptor, and Gal3 as shown in this gallery (30 min CQ, as in Fig. 2). All Rabaptin5-positive swollen endosomes (rings) were positive for transferrin receptor and ~80% for mCherry-Gal3.

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We further tested transferrin receptor levels with and without CQ. Since CQ inhibits autophagic flux, this assay may not be very sensitive. Nevertheless, we found a significant reduction of ~15% and ~30% after overnight incubation with CQ in parental HEK293A cells and in Rbpt5-KO cells re-expressing wild-type Rabaptin5, resp., but no reduction in Rbpt5-KO cells expressing the Rabaptin5-AAA mutant defective in binding to ATG16L1:

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As to the effect of BafA1, see our general response on top. The osmotic effect of CQ or Mon on endosomes that leads to membrane breakage requires an acidic pH. Preincubation with BafA1 neutralizes the pH, prevents osmotic swelling by CQ/Mon, and was shown to block LC3 lipidation (Florey et al., 2015, Jacquin et al., 2017). When BafA1 was added simultaneously, CQ was found to induce LC3 despite the presence of BafA1 (Mauthe et al., 2018), and Mon was shown to still be able to break endosomal membranes and recruit LC3 to EEA1-positive endosomes (Fraser et al., 2019). However, CQ-induced LC3 recruitment to latex bead-containing phagosomes or entotic vacuoles, i.e. LAP-like autophagy, was blocked (Florey et al., 2015). Consistent with this literature, we found increased LC3B lipidation already within 30 min of CQ treatment independently of BafA1 (no preincubation).

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Upon longer incubations, LC3B lipidation is very strong already with BafA1 alone so that the effect of CQ cannot be assessed anymore, since both drugs inhibit autophagic flux.

Furthermore, we found a CQ-dependent increase in WIPI2- and LC3B-positive puncta to be insensitive to BafA1 (panel A below). Colocalization of Rabaptin5 to LC3B and LC3B to Rabaptin5 significantly increased upon CQ treatment independently of the presence of BafA1 (no pretreatment), indicating that at least a large part of CQ-induced LC3B puncta is not due to LAP-like autophagy.

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Minor concerns Both for Figure 2 and Supplementary Figure 7 it will be clearer to have the images in colour rather than black and white for better interpretation.

We thought the grayscale images were clearer, but are happy to provide color images.

The interaction of FIP200 and ATG16L1 with Rabaptin5 is well characterized with immunoprecipitation and imaging but the interaction of Rabaptin5 in presence of chloroquine with FIP200 and ATG16L1 DWD are missing and it will be important to include if in the presence of chloroquine these interactions will increase or not.

We can do co-IP experiments also upon CQ treatment.

In order to further support the role of Rabaptin5 for LC3 lipidation upon chloroquine induced membrane damage, western blots of WT, +Rabaptin5, Rabaptin5 KO, Rabaption5 KO +WT or +AAA cell lines were analysed. However, the lysates were collected upon 30 minutes of chloroquine treatment which does not correlate with the imaging performed in Figure 2 as the number of LC3 vesicles did not show an increase upon 30 minutes of chloroquine treatment. The authors should include the 150 minutes time point for the LC3 lipidation in these conditions.

Because CQ inhibits autophagic flux, LC3-II accumulates after longer times in all cell lines. The differences can only be seen early.

The experiments with Salmonella are of great quality. The relationship of Rabaptin5 with SCV and the endomembrane damage induced by Salmonella could be further elucidated with Rabaptin5 positive vesicles at early infection stages. It is not very clear from the text how authors link the endosomal network previously described for chloroquine with infection. It would be important here to show that Salmonella mutants unable to damage endosomal membranes do not have an effect. In Figure 7 panel C, the time points on graphs are in hours but it should be in minutes. corrected.

Since Salmonella require T3SS for infection of HEK cells and T3SS causes the membrane damage, the proposed experiment is difficult.

The events of targeting the damaged membranes for degradation was well characterized by the recognition of these membranes by Gal3, Gal8 and recruitment of autophagic receptors to the site of damage (Chauhan et al. 2016; Jia et al. 2019; Thurston et al. 2012; Maejima et al. 2013; Kreibich et al. 2015). This manuscript introduces a new potential platform for the formation of autophagic machinery on endosomes with the interaction of Rabaptin5 with FIP200 and ATG16L1, however more evidence is required to link this to the clearance of damaged membranes. Previously it was shown that endolysosomal compartments that were neutralized and swollen by monensin and chloroquine had been directed to degradation by direct conjugation of LC3 to single membranes via noncanonical autophagy, but here authors propose another mechanism for this event via canonical autophagy.

As discussed in the general response above, the literature reports CQ and Mon to initiate both canonical autophagy and LAP-like autophagy, the latter particularly on phagosomes containing latex beads or entotic vacuoles. Our results – including the additional data above –concern the effects of CQ and Mon damaging early endosomes and causing recruitment of galectins and ubiquitination, triggering autophagy dependent on the ULK complex and WIPI2 as hallmarks of canonical autophagy, and Rabaptin5. The reviewer comments highlighted the possibility of LAP-like autophagy occurring in parallel, perhaps on endosomes that are not broken, which might explain the relative insensitivity of LC3 puncta induced by CQ and Mon – compared to the strong and robust reduction of WIPI2 puncta – on the knockdown of FIP200, ATG13, or Rabaptin5. In an alternative explanation, inhibition of autophagic flux causes remaining canonical autophagy to accumulate, while WIPI2 puncta are strongly inhibited. In support of the latter interpretation, ULK inhibition by MRT68921 (Fig. 4C and D) or FIP200 knockout (Fig. 6B and C) abolished CQ-induced LC3 structures, suggesting that – unlike on phagosomes or entotic vacuoles – there is little LAP-like autophagy. We propose to revise the manuscript to discuss these considerations more clearly.

Reviewer #1 (Significance (Required)):

Overall this work is very novel and shows some evidence of early endosomal autophagy. It could be relevant for some for of receptor-mediated signalling (although it is not discussed by the authors) My experience is in intracellular trafficking of pathogens and membrane damage.

**Referee Cross-commenting**

In my opinion, the only way you can distinguish between double or single membrane is by EM. For me, the important part is to show this is targeting of early endosomes to autophagy, either using other early endosomal markers, analysing by WB some early endosome receptors such as TfR or other inhibitors. If the authors are able to address some these comments, I agree the paper will be in a better position for publication.

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Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Millarte et al study the role of Radaptin-5 (Rbpt5) during early endosome damage recognition by autophagy. The authors focus on using chloroquine (CQ) as an agent to induce endosomal swelling/damage and suggest that Rbpt5 is required for the recruitment of the autophagy machinery to perturbed endosomes. They further use salmonella infection as a model to confirm the role of Rbpt5 in this process. The authors initially show that Rbpt5 binds to FIP200 and subsequently focus on its interaction with ATG16L1 and identify a mutant that is unable to bind ATG16L1 or mediate the recognition of early endosomes by autophagy. Overall, this is an interesting study which provides molecular insights of how early endosomes can be targeted by the autophagy machinery where Rbpt5 may act as an autophagy receptor. Some specific comments are as follows:

Fig.3A: siRbpt5 seems to induce the localization of LC3 to ring-like structures during CQ treatment. Are these LAP-like structures (e.g. sensitive to BafA1 treatment)? And were they included in the quantification in Fig.3C?

Ring-like LC3 structures were also counted.

As discussed in the general remarks above, it is a possibility that knockdown-resistent LC3 recruitment (particularly rings) is due to a CQ-induced LAP-like process. The alternative explanation is that there is residual canonical autophagy upon knockdown of Rabaptin5, ATG13, or FIP200: while WIPI2 puncta are strongly reduced, LC3-positive structures accumulate due to inhibition of autophagic flux. In support of the latter interpretation, ULK inhibition by MRT68921 (Fig. 4C and D) or FIP200 knockout (Fig. 6B and C) abolished CQ-induced LC3 puncta or rings.

We can also test BafA1 treatment. Certainly, we will revise the text to discuss this point in more detail.

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Fig.4A&B: Since Rbpt5 KD has a weak effect on LC3 puncta formation (Fig.3) and to distinguish the effects of CQ in inducing LAP, the effects of ATG13 and ULK1 KD should be assessed by localising Rbpt5 with WIPI2 or ATG16L1.

We can do that.

Fig.4: It is not clear why ULK1 KD would affect Torin1-induced autophagy but not LC3/WIPI2 localisation during CQ induced early endosome-damage. As the ULK inhibitors can target other pathways, the authors should confirm this finding in ULK1/2 double KO or KD cells.

We have used **MRT68921, because it is frequently used in the literature for this purpose with high specificity. It was used for example by Lystad et al. (2019) together with VPS34IN1 to block all canonical autophagy to analyze exclusively noncanonical effects of monensin treatment. We could perform ULK1/2 double knockdowns, but since ULK2 cannot be detected on immunoblots in HEK293 cells, the result would be interpretable only when there is an effect.

Fig.5: The contribution of FIP200 in the interaction between Rbpt5 and ATG16L1 is unclear. Is binding between Rbpt5 and ATG16L1 mediated by ATG16L1's interaction with FIP200? The plasmid details describing the delta-WD40 deletion plasmid used in this study are missing and could be important to confirm that the detla-WD40 still retains binding to FIP200.

We will of course include the details on the deletion plasmid, which were missing by mistake. Our WD deletion construct of ATG16L1 consists of residues 1–319, precisely deleting just the WD40 repeats, but retaining the FIP200 interaction sequence and the second membrane binding segment (b).

We did a co-immunoprecipitation experiment and found both wild-type ATG16L1 and the ∆WD mutant to co-immunoprecipitate with FIP200:

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Fig.5E: the authors should test Rbpt5 AAA mutant binding to FIP200. Since the mutant appears to express less, its binding to ATG16L1 should be quantified or repeated with more comparable expression levels.

We will quantify the immunoblots and perhaps attempt getting more equal expression levels.

Fig.6: CQ treatment can induce various endosomal damage (in addition to early endosomes) and LC3 lipidation processes (e.g. LAP-like). The authors show that Rbpt5 is specifically involved in damaged early endosome autophagy. In this figure, it would be important to distinguish CQ-induced LC3 puncta as a result of early endosome damage or other lipidation processes (e.g. canonical or non-canonical autophagy). The use of FIP200 KO cells shows that LC3 puncta is inhibited. However, here a specific readout to look at early endosome recognition by autophagy is important. The authors can localize early endosome markers (EEA1) with autophagy players (e.g. WIPI2 and LC3). This is also relevant to other figures (e.g. supplementary figure 7E).

Rabaptin5 is a bona fide marker of Rab5-positive early sorting endosomes. As a control, we confirmed colocalization of Rabaptin5 with transferrin receptor, another endosomal marker, on CQ-induced rings (Fig. 2B). We also analyzed swollen endosomes with triple-staining for Rabaptin5/ transferrin receptor/ Gal3 as shown in this gallery (30 min CQ, as in Fig. 2). All Rabaptin5-positive swollen endosomes (rings) were positive for transferrin receptor and ~80% for mCherry-Gal3.

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Our results are in agreement with Fraser et al. (2019) where they use EEA1 as an endosomal marker upon monensin treatment.

We also performed a colocalization analysis for Rabaptin5 and LC3B, showing enhanced colocalization after CQ treatment for 150 min: ~20% of LC3B is (still) pos for Rabaptin5 after 150 min of CQ treatment:

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Fig.6F&G: the authors should show representative images of these localization images quantified here. These can be added in the supplementary figures.

We are happy to do this.

**Minor comments:**

Fig.2E: FIP200 seems to be highly overexpressed in this image. Commercial antibodies that recognise endogenous FIP200 are widely used and should be tested to confirm the colocalisation between FIP200 and Rbpt5.

We plan to do this.

Fig.7C image: the different setting denoted by +/-, +/+ ..etc are not clearly defined.

We will improve this.

Reviewer #2 (Significance (Required)):

This is a interesting study and provides important mechanistic insights underlying the recognition of perturbed early endosomes by the autophagy machinery. Researchers interested in endosomal trafficking or autophagic substrate recognition are likely to benefit from this study.

**Referee Cross-commenting**

In my opinion, the authors have attempted to distinguish single membrane from double membrane LC3 lipidation by looking at the ULK complex requirement. As other reviewers suggested, this can be further confirmed by using ATG16L1 mutants. It is important however that these experiments are supplemented by co-localising autophagy proteins with alternative early endosome markers when Rbpt5 is inhibited.

I think if the authors are able to address the suggested experiments, this would help improve the manuscript and make it suitable for publication.

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Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Millarte and colleagues find that Rabaptin5, a critical regulator of Rab5 activity, and a protein localized to early endosomes, interacts with FIP200 and ATG16L1. This interaction is confirmed and validated by a number of approaches (yeast 2 H, co-immunoprecipitation) and the binding sites of Rabaptin5 are mapped on FIP200 and ATG16L1. More precisely the binding site for ATG16L1 is nicely mapped on Rabaptin 5 by analogy with other ATG16L1 binders. The authors investigate the significance of this binding of Rabaptin5 to the autophagy proteins by proposing this interaction is required for targeting "autophagy to damaged endosomes". Endosomes are damaged with short treatments of chloroquine, a well studied compound previously shown to inhibit autophagy by disrupting fusion of autophagosomes with lysosomes. They propose the recruitment of autophagy (proteins) to the damaged endosomes may allow them to be eliminated. They use another model (phagocytosis of salmonella) to probe the role for rabaptin5 and its partners FIP200 and ATG16L1 in the well-documented role of autophagy on the elimination of salmonella in SCVs (Salmonella containing vacuole) formed from endosomes. Using short infection time points, and the Rabaptin5 mutants which prevent ATG16L1 binding they suggest Rabaptin5 binding contributes to elimination and killing of Salmonella by recruitment of ATG16L1.

**Major comments:**

1. The authors make an unfortunate and confusing choice of wording in the title and the text of "autophagy being recruited" to damaged early endosomes. A protein can recruit another protein but it can not recruit a process or pathway to a membrane.

In the title we use the term "target". It is OK for us to avoid the expression "recruiting autophagy".

The authors conclude that Rabaptin5 may have a role in autophagy directed to damaged early endosomes. The conclusion that Rabaptin5 binds FIP200 and ATG16L1 are convincing. The main issue is however in identifying what sort of process they are following. They have shown WIPI2 and LC3 can be recruited to early endosomes after 30 min chloroquine treatment but there is no data to explain the consequences of the binding of these proteins. They do not provide proof that canonical autophagosomes are formed which engulf and remove the damaged endosomes, nor do they show that the recruitment of WIPI2 is to a single membrane (presumably damaged early endosomes) which would be a non-canonical pathway. They often use the terminology "chloroquine-induced autophagy" (see Figure 4) but have virtually no proof they have induced either canonical or non-canonical pathways in their experiments. The only evidence they provide that there is some alteration in a membrane-mediated event is increase in lipidation of LC3 in Figure 6. The authors must follow either an early endosome protein or cargo to demonstrate lysosome-mediated degradation indicative of autophagy, or demonstrate the process is a variation on non-canonical autophagy.

We analyzed transferrin receptor levels with and without CQ to test degradation of an early endosomal marker protein. Since CQ inhibits autophagic flux, this assay may not be very sensitive. Nevertheless, we found a significant reduction of ~15% and ~30% after overnight incubation with CQ in parental HEK293 cells and in Rbpt5-KO cells re-expressing wild-type Rabaptin5, resp., but no reduction in Rbpt5-KO cells expressing the Rabaptin5-AAA mutant defective in binding to ATG16L1:

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There are concerns about the replicates done for many experiments in particular the co-immunoprecipitations which are not quantified (Figure 1 and 5).

We will quantify these blots.

The rescue experiments, even if done with stable cells lines made in the parental HEK293 cell line should be viewed with caution because of the very different amounts of Rabaptin5 (see Figure 6A). The overexpression of Rabaptin5 has not been well studied and comparisons with the mutants are therefore preliminary (Figure 6F and G).

Fig 6A shows that Rabaptin5 levels are similar except for +Rbpt, where they are higher, and R-KO, which has none. Additional Rabaptin5 seems not to significantly enhance early WIPI and ATG16L1 colocalization.

Conclusions about the role of the ULK complex, or ULK1 versus ULK2, should be expanded by studying the activity of the complex (phosphorylation of ATG13 for example) in order to make the conclusions more significant.

We consider this to be beyond the scope of this study. Rabaptin5-dependent autophagy depends on the components of the ULK complex.

**Minor comments:**

1. Much of the labelling in the immunofluorescence images is not visible even on the screen version.

We were careful to have the signals within the dynamic range of the image, but we can enhance the signals for better visibility.

The LC3-lipidation experiment (Figure 6D) should be re-analysed by normalization to the loading control. The result may be significantly different and is open to re-interpretation. The quality of this western blot is also very poor.

Quantitation was based on the ratio between LC3B-I and -II or the **percentage of II of the total, always within the same lane and therefore largely independent of loading.

Reviewer #3 (Significance (Required)):

This manuscript topic fits into the field of study of canonical versus non-canonical autophagy. This literature is best described as "LAP" first discovered by Doug Green, (Sanjuan in 2009) but more recently as a phenomena induced by monesin, and viral infection amongst others. Most relevant to this study are the references (in the text) by Florey (Autophagy 2015), Fletcher (EMBO J, 2018) and others. However, this manuscript fails to cite and consider the critical findings in a key study published by Lystad et al., Nature Cell Biology 2019, which examines the role of ATG16 in both canonical and non-canonical autophagy. The current study if placed into the context of the Lystad study would have significantly more value, and potentially make the findings more significant.

We did not refer to Lystad et al. (2019), because they analyzed different ATG16L1 mutants on their contribution to monensin-induced processes on LC3 lipidation after completely blocking canonical autophagy with the ULK inhibitor MRT68921 and the VPS34 inhibitor VPS34IN1. The Rabaptin5-dependent CQ-induced processes are blocked by MRT68921 (Fig. 4C). We plan to refer to this study in the revision.

Furthermore, the short chloroquine treatments used here could be of interest to the field if using the cited study of Mauthe et al., (which very clearly defines the effect of chloroquine after long (5 hrs treatment)) the authors would to revisit and repeat some of the key experiments in order to demonstrate the effects of 30 minute treatment. Does such short treatment block fusion? Does it affect the pH of the acidic compartments? Does it inactivate the endocytitic pathway? As the manuscript stands the lack of this understanding of the effect of chloroquine at short times, makes the observations difficult to be place into any biological context.

This reviewer has expertise in autophagy, autophagosome formation and is familiar with the areas of endocytosis and infection.

**Referee Cross-commenting**

I think a major concern about the manuscript which is present in all reviews is the lack of clarity about what type of membrane LC3 is added to- is this the damaged endosome or a forming autophagosome? This leads to the question of what type of process is being observed here? non-canonical versus canonical autophagy.

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Referee #3

Evidence, reproducibility and clarity

Millarte and colleagues find that Rabaptin5, a critical regulator of Rab5 activity, and a protein localized to early endosomes, interacts with FIP200 and ATG16L1. This interaction is confirmed and validated by a number of approaches (yeast 2 H, co-immunoprecipitation) and the binding sites of Rabaptin5 are mapped on FIP200 and ATG16L1. More precisely the binding site for ATG16L1 is nicely mapped on Rabaptin 5 by analogy with other ATG16L1 binders. The authors investigate the significance of this binding of Rabaptin5 to the autophagy proteins by proposing this interaction is required for targeting "autophagy to damaged endosomes". Endosomes are damaged with short treatments of chloroquine, a well studied compound previously shown to inhibit autophagy by disrupting fusion of autophagosomes with lysosomes. They propose the recruitment of autophagy (proteins) to the damaged endosomes may allow them to be eliminated. They use another model (phagocytosis of salmonella) to probe the role for rabaptin5 and its partners FIP200 and ATG16L1 in the well-documented role of autophagy on the elimination of salmonella in SCVs (Salmonella containing vacuole) formed from endosomes. Using short infection time points, and the Rabaptin5 mutants which prevent ATG16L1 binding they suggest Rabaptin5 binding contributes to elimination and killing of Salmonella by recruitment of ATG16L1.

Major comments:

1. The authors make an unfortunate and confusing choice of wording in the title and the text of "autophagy being recruited" to damaged early endosomes. A protein can recruit another protein but it can not recruit a process or pathway to a membrane.
2. The authors conclude that Rabaptin5 may have a role in autophagy directed to damaged early endosomes. The conclusion that Rabaptin5 binds FIP200 and ATG16L1 are convincing. The main issue is however in identifying what sort of process they are following. They have shown WIPI2 and LC3 can be recruited to early endosomes after 30 min chloroquine treatment but there is no data to explain the consequences of the binding of these proteins. They do not provide proof that canonical autophagosomes are formed which engulf and remove the damaged endosomes, nor do they show that the recruitment of WIPI2 is to a single membrane (presumably damaged early endosomes) which would be a non-canonical pathway. They often use the terminology "chloroquine-induced autophagy" (see Figure 4) but have virtually no proof they have induced either canonical or non-canonical pathways in their experiments. The only evidence they provide that there is some alteration in a membrane-mediated event is increase in lipidation of LC3 in Figure 6. The authors must follow either an early endosome protein or cargo to demonstrate lysosome-mediated degradation indicative of autophagy, or demonstrate the process is a variation on non-canonical autophagy.
3. There are concerns about the replicates done for many experiments in particular the co-immunoprecipitations which are not quantified (Figure 1 and 5).
4. The rescue experiments, even if done with stable cells lines made in the parental HEK293 cell line should be viewed with caution because of the very different amounts of Rabaptin5 (see Figure 6A). The overexpression of Rabaptin5 has not been well studied and comparisons with the mutants are therefore preliminary (Figure 6F and G).
5. Conclusions about the role of the ULK complex, or ULK1 versus ULK2, should be expanded by studying the activity of the complex (phosphorylation of ATG13 for example) in order to make the conclusions more significant.

Minor comments:

1. Much of the labelling in the immunofluorescence images is not visible even on the screen version.
2. The LC3-lipidation experiment (Figure 6D) should be re-analysed by normalization to the loading control. The result may be significantly different and is open to re-interpretation. The quality of this western blot is also very poor.

Significance

This manuscript topic fits into the field of study of canonical versus non-canonical autophagy. This literature is best described as "LAP" first discovered by Doug Green, (Sanjuan in 2009) but more recently as a phenomena induced by monesin, and viral infection amongst others. Most relevant to this study are the references (in the text) by Florey (Autophagy 2015), Fletcher (EMBO J, 2018) and others. However, this manuscript fails to cite and consider the critical findings in a key study published by Lystad et al., Nature Cell Biology 2019, which examines the role of ATG16 in both canonical and non-canonical autophagy. The current study if placed into the context of the Lystad study would have significantly more value, and potentially make the findings more significant.

Furthermore, the short chloroquine treatments used here could be of interest to the field if using the cited study of Mauthe et al., (which very clearly defines the effect of chloroquine after long (5 hrs treatment)) the authors would to revisit and repeat some of the key experiments in order to demonstrate the effects of 30 minute treatment. Does such short treatment block fusion? Does it affect the pH of the acidic compartments? Does it inactivate the endocytitic pathway? As the manuscript stands the lack of this understanding of the effect of chloroquine at short times, makes the observations difficult to be place into any biological context.

This reviewer has expertise in autophagy, autophagosome formation and is familiar with the areas of endocytosis and infection.

Referee Cross-commenting

I think a major concern about the manuscript which is present in all reviews is the lack of clarity about what type of membrane LC3 is added to- is this the damaged endosome or a forming autophagosome? This leads to the question of what type of process is being observed here? non-canonical versus canonical autophagy.

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Referee #2

Evidence, reproducibility and clarity

Millarte et al study the role of Radaptin-5 (Rbpt5) during early endosome damage recognition by autophagy. The authors focus on using chloroquine (CQ) as an agent to induce endosomal swelling/damage and suggest that Rbpt5 is required for the recruitment of the autophagy machinery to perturbed endosomes. They further use salmonella infection as a model to confirm the role of Rbpt5 in this process. The authors initially show that Rbpt5 binds to FIP200 and subsequently focus on its interaction with ATG16L1 and identify a mutant that is unable to bind ATG16L1 or mediate the recognition of early endosomes by autophagy. Overall, this is an interesting study which provides molecular insights of how early endosomes can be targeted by the autophagy machinery where Rbpt5 may act as an autophagy receptor. Some specific comments are as follows:

Fig.3A: siRbpt5 seems to induce the localization of LC3 to ring-like structures during CQ treatment. Are these LAP-like structures (e.g. sensitive to BafA1 treatment)? And were they included in the quantification in Fig.3C?

Fig.4A&B: Since Rbpt5 KD has a weak effect on LC3 puncta formation (Fig.3) and to distinguish the effects of CQ in inducing LAP, the effects of ATG13 and ULK1 KD should be assessed by localising Rbpt5 with WIPI2 or ATG16L1.

Fig.4: It is not clear why ULK1 KD would affect Torin1-induced autophagy but not LC3/WIPI2 localisation during CQ induced early endosome-damage. As the ULK inhibitors can target other pathways, the authors should confirm this finding in ULK1/2 double KO or KD cells.

Fig.5: The contribution of FIP200 in the interaction between Rbpt5 and ATG16L1 is unclear. Is binding between Rbpt5 and ATG16L1 mediated by ATG16L1's interaction with FIP200? The plasmid details describing the delta-WD40 deletion plasmid used in this study are missing and could be important to confirm that the detla-WD40 still retains binding to FIP200.

Fig.5E: the authors should test Rbpt5 AAA mutant binding to FIP200. Since the mutant appears to express less, its binding to ATG16L1 should be quantified or repeated with more comparable expression levels.

Fig.6: CQ treatment can induce various endosomal damage (in addition to early endosomes) and LC3 lipidation processes (e.g. LAP-like). The authors show that Rbpt5 is specifically involved in damaged early endosome autophagy. In this figure, it would be important to distinguish CQ-induced LC3 puncta as a result of early endosome damage or other lipidation processes (e.g. canonical or non-canonical autophagy). The use of FIP200 KO cells shows that LC3 puncta is inhibited. However, here a specific readout to look at early endosome recognition by autophagy is important. The authors can localize early endosome markers (EEA1) with autophagy players (e.g. WIPI2 and LC3). This is also relevant to other figures (e.g. supplementary figure 7E).

Fig.6F&G: the authors should show representative images of these localization images quantified here. These can be added in the supplementary figures.

Minor comments:

Fig.2E: FIP200 seems to be highly overexpressed in this image. Commercial antibodies that recognise endogenous FIP200 are widely used and should be tested to confirm the colocalisation between FIP200 and Rbpt5.

Fig.7C image: the different setting denoted by +/-, +/+ ..etc are not clearly defined.

Significance

This is a interesting study and provides important mechanistic insights underlying the recognition of perturbed early endosomes by the autophagy machinery. Researchers interested in endosomal trafficking or autophagic substrate recognition are likely to benefit from this study.

Referee Cross-commenting

In my opinion, the authors have attempted to distinguish single membrane from double membrane LC3 lipidation by looking at the ULK complex requirement. As other reviewers suggested, this can be further confirmed by using ATG16L1 mutants. It is important however that these experiments are supplemented by co-localising autophagy proteins with alternative early endosome markers when Rbpt5 is inhibited.

I think if the authors are able to address the suggested experiments, this would help improve the manuscript and make it suitable for publication.

Referee Cross-commenting

In my opinion, the authors have attempted to distinguish single membrane from double membrane LC3 lipidation by looking at the ULK complex requirement. As other reviewers suggested, this can be further confirmed by using ATG16L1 mutants. It is important however that these experiments are supplemented by co-localising autophagy proteins with alternative early endosome markers when Rbpt5 is inhibited.

I think if the authors are able to address the suggested experiments, this would help improve the manuscript and make it suitable for publication.

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Referee #1

Evidence, reproducibility and clarity

In the current manuscript, Millarte et al reports a novel role of Rabaptin5 in selectively clearing damaged endosomes via canonical autophagy. They have identified FIP200 as a novel interactor of Rabaptin5 under basal conditions using yeast-two hybrid screening and further confirmed the interaction of Rabaptin5 with FIP200 with immunoprecipitation. They next used Chloroquine and monitored colocalization of the Rabaptin5 with WIPI2, ATG16L1 and LC3B to demonstrate the potential interaction of Rabaptin5 with the autophagic machinery. They have primarily used Gal-3 as a marker of membrane damage after 30 minutes of Chloroquine treatment. In order to further elucidate the role of Rabaptin5 in autophagic induction mediated by Chloroquine, they have silenced Rabaptin5, FIP200, ULK1 and ATG13 and observed a decrease in the number of LC3 or WIPI2 autophagosome formation. Based on these observations they tested if Rabaptin5 interacts with ATG16L1 upon Chloroquine treatment and confirmed their interaction with potential interaction sites of both Rabaptin5 with ATG16L1 with IP. The authors confirmed the interaction of Rabaptin5 with ATG16L1 by complementing the KO line with the mutant form of Rabaptin5 containing alanine residues in its consensus motif. Finally, they have used Salmonella and SCV as a model to study the role of Rabaptin5 in endomembrane damage and monitored a 50% decrease in the removal of Salmonella in Rabaptin5 KO or KD cells.

Major concerns One of the major concerns is the membrane damage reported by chloroquine which is known to induce lysosomal swelling and further targeting of the swollen compartments to degradation by direct conjugation of LC3 onto single membrane as a form of non-canonical autophagy. The evidence regarding membrane damage by Gal3 colocalization on the Rabaptin5 vesicles is preliminary. As suggested by the authors the canonical autophagy pathway recognizing damaged membranes recruits also ALIX to the damaged membrane which was not observed in Supplementary Figure 2. The link to membrane damage by chloroquine and monensin with Rabaptin5 is not convincing as there is not sufficient evidence of membrane damage. In relation to this issue authors should consider using other damage markers as Gal8, p62 or NDP52 to provide additional claim with respect to membrane damage induced by chloroquine.

One of the main claims here is that Rabaptin5 regulates the targeting of damaged endosomes to autophagy. Clearly, these are early endosomes as stated in the abstract. However, the evidence presented here showing these are early endosomes is not convincing. Analysing Gal3 and Gal8 positive vesicles that are Rabaptin5 positive and an early endosomal marker will be important in this context. For example, there need to be additional evidence showing that early endosomes are targeted to autophagy. Is the degradation of TfR affected by this targeting? Did the authors look at the effect of Bafilomycin A1? If this process affects exclusively early endosomes, it should be BafA1 independent. This will direct more into the cellular function of this process.

Minor concerns Both for Figure 2 and Supplementary Figure 7 it will be clearer to have the images in colour rather than black and white for better interpretation.

The interaction of FIP200 and ATG16L1 with Rabaptin5 is well characterized with immunoprecipitation and imaging but the interaction of Rabaptin5 in presence of chloroquine with FIP200 and ATG16L1 WD are missing and it will be important to include if in the presence of chloroquine these interactions will increase or not.

In order to further support the role of Rabaptin5 for LC3 lipidation upon chloroquine induced membrane damage, western blots of WT, +Rabaptin5, Rabaptin5 KO, Rabaption5 KO +WT or +AAA cell lines were analysed. However, the lysates were collected upon 30 minutes of chloroquine treatment which does not correlate with the imaging performed in Figure 2 as the number of LC3 vesicles did not show an increase upon 30 minutes of chloroquine treatment. The authors should include the 150 minutes time point for the LC3 lipidation in these conditions.

The experiments with Salmonella are of great quality. The relationship of Rabaptin5 with SCV and the endomembrane damage induced by Salmonella could be further elucidated with Rabaptin5 positive vesicles at early infection stages. It is not very clear from the text how authors link the endosomal network previously described for chloroquine with infection. It would be important here to show that Salmonella mutants unable to damage endosomal membranes do not have an effect. In Figure 7 panel C, the time points on graphs are in hours but it should be in minutes.

The events of targeting the damaged membranes for degradation was well characterized by the recognition of these membranes by Gal3, Gal8 and recruitment of autophagic receptors to the site of damage (Chauhan et al. 2016; Jia et al. 2019; Thurston et al. 2012; Maejima et al. 2013; Kreibich et al. 2015). This manuscript introduces a new potential platform for the formation of autophagic machinery on endosomes with the interaction of Rabaptin5 with FIP200 and ATG16L1, however more evidence is required to link this to the clearance of damaged membranes. Previously it was shown that endolysosomal compartments that were neutralized and swollen by monensin and chloroquine had been directed to degradation by direct conjugation of LC3 to single membranes via noncanonical autophagy, but here authors propose another mechanism for this event via canonical autophagy.

Significance

Overall this work is very novel and shows some evidence of early endosomal autophagy. It could be relevant for some for of receptor-mediated signalling (although it is not discussed by the authors) My experience is in intracellular trafficking of pathogens and membrane damage.

Referee Cross-commenting

In my opinion, the only way you can distinguish between double or single membrane is by EM. For me, the important part is to show this is targeting of early endosomes to autophagy, either using other early endosomal markers, analysing by WB some early endosome receptors such as TfR or other inhibitors. If the authors are able to address some these comments, I agree the paper will be in a better position for publication.

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Reply to the reviewers

We would like to thank our reviewers for their critical reading and constructive comments. We have addressed all of their points and have included below a detailed reference to the changes we made accordingly. We have also added an additional supplemental figure.

Reviewer #1 :

**Major comments:**

1. The authors highlight in their conclusion that the new Python library has the potential to accelerate and expand microscopy development. I agree with this statement since classes and methods do not need to be written in Python from scratch anymore. However, I would recommend that the authors include in their conclusion the value of the library for reproducibility if the final python acquisition code is shared along with publications. Nowadays, scientists frequently write in their publications that LabView or a specific commercial scope's acquisition software was used without any acquisition code. Python-Microscope would have the potential to change this trend, and the authors need to stress this aspect and its value for reproducibility in science accordingly. This is a good point. We have added the following to the discussion section.

“A further advantage of the approach provided by Microscope is in increasing reproducibility in science. Scientists frequently write in their publications that LabView or a specific commercial scope's acquisition software was used without any specific acquisition settings, code or macros to assist with reproduction. This is especially critical in complex experimental setups where specifics of acquisition are particularly important. Microscope has the potential to change this trend, allowing authors to freely publish simple code demonstrating exactly how their control and acquisition operates. Additionally, the defined device interfaces allow such code to be ported to other specific hardware with minimal changes.”

The authors need to provide a more comprehensive overview of the currently used data acquisition strategies in their introduction. Currently, they highlight the acquisition software provided by vendors for data acquisition (mainly used by life scientists and not necessary scope builders/developers), Micro-Manager (mainly used by life scientists; currently also restricted to wide-field systems), and LabView (for advanced microscope systems; used by advanced developers).

However, most advanced microscope builders use MatLab (Chmyrov et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2556, Ta et al. Nature Communications (2015) - https://doi.org/10.1038/ncomms8977 , etc.), Python (York et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2687, etc.), and LabView to write their acquisition software. Since the manuscript focused on advanced microscopes, the authors need to position their library with respect to Matlab and Python's current use as well.

We thank the reviewer for pointing out the omission of Matlab control solutions and extending the references to other Python based approaches. We have also added a reference to the Pycro-Manager framework for Micro-Manager which has been published since our original submission.

We have added Matlab to the LabVIEW generalised control software section which now reads:

“custom control software often in LabVIEW or Matlab, both proprietary software. LabVIEW offers a visual programming environment that is commonly used for building instruments in the physical sciences, whereas Matlab is a programming platform with a focus on numeric computing.”

And extended the description sections in the introduction with the following paragraphs and references:

“Matlab is a numerical focused programming environment that scientists are often familiar with for data processing. It has frequently been used for microscopy, leveraging a number of available Matlab sub packages to provide GUI’s and easy access to complex data processing steps. The use of Matlab for microscope control is common in the field but the actual code is rarely shared and often custom to a single microscope setup and associated to image reconstruction (Chmyrov et al., 2013, Ta et al., 2015). Exceptions are ScanImage for the control of laser scanning microscopes (Pologruto et al., 2003), and Matlab Instrument Control (MIC) for the control of individual microscope components (Pallikkuth et al., 2018). Matlab provides a textual programming language simplifying code sharing and version control, however, Matlab is proprietary closed source software and the general requirement of many extensions significantly adds to the cost of implementing many systems.”

“There is currently an increasing number of software options for microscope control in Python, many of which are in the form of custom scripts specific to a microscope (Alvelid and Testa, 2019, York et al., 2013) but some provide a fully integrated microscope control environments, namely PYME https://www.python-microscopy.org/ for SMLM and ACQ4 (Campagnola et al., 2014) for electrophysiology. While this code is freely available and can be modified, their design around a specific setup, technique, or environment reduces its potential for code reuse in other projects.”

The authors need to give (a) software provided by vendors, (b) LabView, and (c) Micro-Manager, more credit.

(a) Several microscope vendors (e.g., Abberior Instruments - https://imspectordocs.readthedocs.io/en/latest/specpy.html ) allow their scopes can be externally controlled to enable the execution of customer-driven acquisition strategies which the vendor's acquisition software itself might not have implemented with. The authors might want to include that scope vendors aim for more customer modifiable acquisition software.

The reviewer makes a good point, especially in the fact that a number of microscope vendors provide Python interfaces for their systems. We have added the following text:

Several microscope vendors, such as Abberior Instruments and Zeiss, provide Python interfaces to enable instrument control from Python. These are all very useful additions to proprietary systems, however they have a fundamental draw back that each manufacture produces their own abstractions meaning code from one system is not compatible with another. Although these interfaces leverage the substantial Python infrastructure they are not generalisable and hence fail to enhance portability or reproducibility.

The fact that these companies are providing Python interfaces to their instruments indicates the general interest of the community in Python as a programming language to extend hardware capabilities. This demonstrates the potential benefit of an entirely Python based interface to a wide range of hardware.

(b) The authors criticize that LabView code can be hard to understand, reproduce and maintain. However, similar to writing good code in general, there are best practice strategies for writing good LabView code to ensure scalability, readability, and maintainability available as well (https://learn.ni.com/learning-paths/labview-core-3-2016-english ). The primary problem might lie more on the side of lousy coding practice than on LabView's side to perform appropriately.

This is a fair point and we have revised the manuscript as indicated below. However, it remains true that it is much harder for a non-expert to write high quality code in LabView than in Python. This is particularly evident in complex systems.

We have changed the section about LabView to read:

“The visual nature of the programming environment makes simple projects easy but systems with a large number of hardware components or complicated control architecture can become hard to understand, reproduce, and maintain. Although this complication can be reduced with good programming practices, it is not uncommon to outsource such work to a commercial company \citep{chhetri2020software} because good code writing in LabView is significantly more challenging than in popular general purpose languages such as Python. Additionally, the LabView work flow does not integrate well into modern distributed source control infrastructure such as mercurial or git, a necessity for modern open source development.”

(c) The authors should include the current effort by Pinkard et al. (Pinkard et al. Nature Methods (2021) - https://doi.org/10.1038/s41592-021-01087-6 ) in their discussion.

A pre-print version of this paper was available on arXiv and cited in our original submission. Now this paper is published we have included the published reference and the following text has been added to our discussion section.

“As mentioned in the introduction, micromanager has a recently introduced Python interface, Pycro-Manager (Pinkard et al. 2021). This simplifies connections between micromanager based hardware interfaces and Python based analysis and control. Although this reduces the effort in using Python for control and online analysis compared to other approaches it does not provide direct access to the hardware via Python. This interface keeps the existing micromanager infrastructure. Particularly new hardware interfaces still need code in both C/C++ and Java before they are accessible via the Python interface.”

The authors might want to explain how they plan to facilitate the library's adoption and the long-term maintenance within the microscopy community. Do they plan to create a new category on Image.sc, which would allow the community to interact with the developers? etc. Furthermore, who will keep writing wrappers to the libraries provided by the vendors? etc

This is a critical point, as the reviewer states, community involvement is essential to continuation of the project and provide a useful tool going forward. We have already published several systems utilising this software platform and are working hard to expand its user base. We have asked for people to post question on the image.sc forums (https://image.sc/) and we also interact with developers and users on the github issue pages (https://github.com/python-microscope/microscope/issues). We have recently implemented a fully automated microscope on a simple motorized stand from Zaber. This provides a fully automated microscopy solution for a very low cost.

We have edited the end of the discussion to read

Microscope is a free and open source project currently being used in several labs with an open development approach. Our aim is that the microscope development community will find it a useful tool and engage in this development to increase its general usefulness. With that aim in mind, we perform our development conversations and user support in the open as github issues and the project is an image.sc community partner. In particular, expanding the number of devices supported by Microscope would be extremely beneficial. However, adding support for a device requires physical access to the device and the current list of supported devices echoes the devices we and our collaborators have access to. This is a chicken and egg problem. Python-Microscope needs broad device support to be widely adopted by the community but it needs contributions from the community to support those devices. We believe that, Microscope currently provides enough devices and infrastructure to support adoption by more developers. There are contribution guidelines within the ``Get Involved' section of the documentation, available online at https://www.python-microscope.org/doc/get-involved.

The authors stress using their library for complex scopes but do not provide an example of complex implementation (they only provide paper references). Only a code for a simple time-series is provided. It would be very beneficial to provide the code for implementing a complex microscope and its GUI with the author's library as separate figures or in the paper's supplement. This would also support point 1 in the review.

The GUI elements provided by Python-Microscope are deliberately minimal implementations to allow basic connectivity and functionality of specific hardware to be tested. Python-Microscope is specifically designed to provide a hardware interface layer separate from the user interface. We provide a very simple examples to demonstrate how easily devices can be controlled. For more complete examples we have developed two associated packages providing GUIs, both are referenced in the text, BeamDelta is an optical alignment tool, while Microscope-Cockpit provides a full user interface to complex microscope systems. We have added a supplemental figure demonstrating the full GUI provided by Cockpit.

**Minor comments:**

It would help the paper if several phrases would be changed: Title: 'Python-Microscope: High-performance control of arbitrarily complex and scalable bespoke microscopes." To: e.g., Python-Microscope: A new open-sources Python library for the control of microscopes

Why? The authors use the word "high-performance" to address their Python library's trigger feature within the text. Unfortunately, that is not how most people would use the term for. Therefore, it should be avoided not only in the title but throughout the text. Furthermore, the word "complex" combined with microscopes should be avoided. A complex microscope is, for most microscope builders, a microscope that needs precise times and synchronization, includes several feedback active feedback loops, incorporates several devices, is very stable, etc. The context in which the term "complex microscopes" is used here is when the authors talk about the library's features to connect devices to servers either locally or remotely. I agree that the library can connect devices over arbitrary complex networks, but using the term "arbitrary complex microscopes" would be misleading considering the library's current speed limitations, the limited number of currently integrated devices, etc.

We have changed the title to:

Python-Microscope: A new open-source library for the control of microscopes

1. Various section titles: "Library features" would be more suitable than "Use Cases" since the individual new features at the new library are described in this section. Also, the description of the individual features should be mentioned more accurately. The following list might be a better, more accurate fit: (1) "Device modularity" instead of "Device independence."

Also, the current title "Write once, run with any device" is inaccurate since the wrapper for multiple devices has not been implemented. (2) "Experiment- and scope-specific layout" instead of "Experiments as programs." (3) "Complex network integration" instead of "Easy implementation of complex systems and scalability" (see reasoning under point a). (4) "Hardware and software trigger integration" instead of "High performance, " (5) "Developer-friendly programming features" instead of "Simple development tool."

We have renamed the specified sections and subsections title and expanded the description in the list of use cases to be more accurate.

1. The authors should avoid using the term "Microscope" when talking about "Python-Microscope." It facilitates the manuscript's readability since it is occasionally not evident in the paper if they refer to the library or a microscope. We have changed “Microscope” to “Python-Microscope” in multiple places of the manuscript where it was unclear whether we were referring to the software or to a physical microscope.

2. The authors should avoid the phrase "pythonic software platform" in the abstract since Python-Microscope is a library / Python package and not a software platform. Furthermore, the term "pythonic" describes the desired way to write Python code. It means code that does not just get the syntax right but follows the Python community conventions and uses the language in the way it is intended to be used. Instead, it might be advisable to write, "Python-Microscope offers elegant Python-based tools to control microscopes...". We have changed the abstract as suggested.

Figure 1 should be supported by comments, e.g., #Load packages, #Parameter Initialization, #Create Devices, # Set camera parameters, etc.

Comments have been added the sample code.

The paragraph under the section "Experiments as programs" about the advantages of using Python (starting from "We have developed the software in Python, ...") should be moved into the Introduction section.

We have moved this segment to the end of the introduction.

Reviewer #2:

1)The introduction does a good job describing the current situation (using multiple software from multiple vendors simultaneously, Micro-Manager, Labview), although it could be highlighted a bit more that several groups have created custom Python code for microscope control (such as https://github.com/ZhuangLab/storm-control, https://github.com/Ulm-IQO/qudi, https://github.com/fedebarabas/tormenta, https://github.com/AndrewGYork/tools), some with at least the hope that their code will be generally usable. It also could be noted that the Micro-Manager device abstraction layer has been accessible from Python for more than a decade (currently the Python 3 interface is at https://github.com/micro-manager/pymmcore).

We have significantly expanded the references to previous Python code and made other changes to the relevant sections as detailed in the response to reviewer #1 and quoted below. We have made reference to the recently published Pycro-Manager package (the previous version referenced the arXiv preprint of this paper. It should be noted that although the Python bindings for mmcore have been available for more than a decade, they have been rarely used, the only published paper referencing them appears to be the whitepaper from a workshop on microscope control software published on arXiv in 2020 (https://arxiv.org/abs/2005.00082).

“There is currently an increasing number of software options for microscope control in Python, many of which are in the form of custom scripts specific to a microscope (Alvelid and Testa, 2019, York et al., 2013) but some provide a fully integrated microscope control environments, namely PYME https://www.python-microscopy.org/ for SMLM and ACQ4 (Campagnola et al., 2014) for electrophysiology. While this code is freely available and can be modified, their design around a specific setup, technique, or environment reduces its potential for code reuse in other projects”

2) Manuscripts describing software tools have to balance the goal to "announce" and advertise the software package with the goal to objectively explain the design principles and choices made. In my opinion, this manuscript finds a nice balance, and leaves the reader with a decent understanding of the capabilities, advantages, limitations and high level architecture of the Python-Microscope package. Possible exceptions are the use of the word "elegant" in the abstract, and extensive use of the word "bespoke" that I mainly know from real estate agent language and that likely is confusing to many readers for whom English is a second language.

We have reworded the abstract to say

“Python-Microscope offers simple to use Python-based tools to control microscopes…”

We use the term “bespoke” to refer to the construction of novel optical microscopes, as opposed to controlling existing integrated systems from commercial vendors. We have reworded paper to refer to custom built microscopes and optical systems to clarify this point.

As far as I am aware, "Microscope" is the most developed microscope abstraction layer written in pure Python. Remarkably, its design (device classes that inherit from a device-base class and have their own function calls, supplemented with "Settings" that can be declared by each device), is extremely similar to that of the Micro-Manager device abstraction layer (where "Settings" are called "Properties"), with the main difference being that one is written in Python and the other in C++ with C bindings. Writing these device classes in Python hopefully brings the advantage that more people can write them, however, the Micro-Manager C interface has the advantage that it can be used from any programming language on any platform, hence is more future proof than pure Python code. The downside of having multiple microscope device abstraction layers is that resources will be diluted and confuse partners in industry (which toolkit should they support with their limited resources?). The number of devices supported is currently much, much greater in the Micro-Manager platform than in Microscope, and a translation layer to make Micro-Manager device adapters in Microscope does not seem out of the question, and could possibly benefit many.

We are aware of the similarity between our approach and that in micromanager. There is therefore significant overlap and possible duplication of effort, however when we started this project we reviewed the Python bindings of micromanager core and felt that using this approach would add significantly, not only to our development effort, but also to end user effort as they would also have to install Micro Manager and its Python bindings. In addition, we believe that there is significant value in having a pure Python implementation. As the reviewer suggests "Python is at the moment probably the most widely used computer programming language by scientists". Having Python-Microscope in a language that the end user can code, invites them to look into the “box” and eases the process for these, possible casual, Python users to contribute with fixes and support for new devices.

Reviewer #3:

• I miss more information regarding the latency of the device-server and software triggering, how fast can it be? How much delay would you have between computers/devices? For example, could we have the devices sincronized at the microsecond range? I think this is super important so that the reader knows if it's worth using a software triggering approach with Python-Microscope or they should buy a DAQ instead. We generally expect high performance hardware to require hardware triggering, software triggers are very unlikely to be performant, or reliable enough to achieve ms, yet alone, µs timing accuracy and reproducibility. Software triggering is implemented as a basic approach to allow simple low speed hardware control, such as basic image snapping. Our systems all utilise external timing devices to provide digital triggering and, in some cases, analogue voltage control. This is becoming increasingly easy with high performance microprocessors such as the ardiuno or higher spec solutions such as National Instruments DAQ boards. We are currently investigating the recently released Raspberry Pi Pico boards, which provide very high performance digital triggering at very low cost (~£4). We are passionately promoting open source, low cost solutions, so requiring a NI DAQ board and LabView licenses goes against the spirit of this project.

1b) It's good though that they don't want to limit themselves to software triggering but also mention hardware triggering, but it's important to better explain where are the limitations.

This is a significant issue but we feel it is beyond the scope of this paper. We utilise microscope as a low level interface to hardware for our systems. The hardware control software has no internal knowledge of device connectivity eg which filter wheel might be in front of what camera, so any integrated control, such as synchronising light sources and cameras is beyond the scope of this package. We use the cockpit package as a GUI and to provide this higher level control integration. We then utilise hardware timing devices interfaced to cockpit to run experiments. We feel that this is a relatively cheap and approachable solution while allowing high performance from even complex systems.

1c) Needs info adding to the text, but in general python-microscope doesn’t concern itself with this, just allows setting of trigger types and you are then responsible for triggering.

As suggested by the reviewer, Python-Microscope does not generally concern itself with triggering. It allows setting of trigger types in a consistent manner, and on relevant devices can initiate a software trigger event. The end of the section “Fast and furious” now reads:

“The microscope interface was designed with the concept of triggers that activate the individual devices and software triggers are handled as simply another trigger type. This approach provides an interface that supports software triggers but is easily upgraded to hardware triggers. The source of such hardware triggers can be other devices --- typically a camera --- or a dedicated triggering device. The recommended procedure is to prepare an experiment template that is then loaded on a dedicated timing device which triggers all other devices, as described in Carlton 2010.

The existence of fast and cheap microprocessors and single board computers mean providing a dedicated hardware timing to sequence and synchronise a number of devices is relatively easy and extremely cost effective. We would recommend systems are designed around using an external device to provide hardware triggers to devices. This provides reliable timing and much more flexible sequencing than directly connecting outputs from one device to trigger inputs for another.”

1d) I also miss information about the triggering, do the software offer a platform that can synchronize devices, or that's more left to the developer to do? They say they can generalize to arbitrarily complex devices so therefore I think it needs to be specified how. Same with the server feature, how fast is that link?

The software triggering depends very much upon the individual devices and delays such as context switching within the OS. We offer no solution to synchronise devices. Our claim to generalise to arbitrarily complex systems is based on the fact that you can trivially run devices on different computers to allow horizontal scaling. If you wish to have 25 cameras, simply run them on different computers, then none will be speed limited by computational resources. Synchronisation can be achieved by an external hardware timing device as described above.

The server link is passed over standard ethernet, likely now 1GB/s, however data packets must be serialised before transmission and deserialised on receipt by Python, as well as standard network overhead and latency. We have only seen network limitations on image transfer from cameras to remote server computers. This has not been a significant issue as the cameras drivers typically have memory buffers, which can be enlarged to cope with backlogs, as well as the Python-Microscope image transmission processes acting on a FIFO memory queue. Possibly long experiments utilising fast, high pixel count cameras could saturate these buffers, but such a specialised application could use specialised solutions such as multi-path networking or a computer with a very large amount of RAM for temporary buffering.

2a) Some critical comments are that, first of all there are not so many drivers yet available (for example Hamamatsu camera).

The reviewer is correct, device support is critical. There are two components to this, a) the resources to implement new devices, and b) the physical hardware to enable testing and debugging of these devices. We have focused on the hardware that we own and use but hardware support is expanding. As described in our reply to reviewer #1, we hope that a community of experienced hardware and software developers will evolve and help support new devices. We have instructions on how to support new hardware devices and are happy to help interested parties. We also plan to apply for continuing funding to enable us to further develop Python-Microscope, especially to expand its range of supported hardware,

The well defined interface with the abstract base class in Python enforces what is required for a minimal implementation of a specific device type. Most devices are relatively easily supported by reference to existing devices of the same type. For instance, a stage is likely to be communicated to by serial over USB, taking simple text commands and returning easy to interpret responses. Adding a new device simply involves defining what commands to send and how to deal with the replies from the hardware. With a suitable manual this can typically be done with a few hours of programming and testing.

2b) I guess this paper is also to show proof of concept and then upon interest they will include more devices, but in that case it should be more documented how one can contribute to the project and generate new drivers. For example, if we want to try it tomorrow in our setups, and we have a specific device such as an Hamamatsu camera, What should we do? Should we contact the authors, write an issue in the github page or write the driver ourself?

We have added the following paragraph on contributing to the project at the end of discussion section of the paper:

Microscope is a free and open source project currently being used in several labs with an open development approach. Our aim is that the microscope development community will find it a useful tool and engage in this development to increase its general usefulness. With that aim in mind, we perform our development conversations and user support in the open as github issues and the project is an image.sc community partner. In particular, expanding the number of devices supported by Microscope would be extremely beneficial. However, adding support for a device requires physical access to the device and the current list of supported devices echoes the devices we and our collaborators have access to. This is a chicken and egg problem. Python-Microscope needs broad device support to be widely adopted by the community but it needs contributions from the community to support those devices. We believe that, Microscope currently provides enough devices and infrastructure to support adoption by more developers. There are contribution guidelines within the ``Get Involved' section of the documentation, available online at https://www.python-microscope.org/doc/get-involved.

• Second, the graphical interface is maybe good enough for developers and builders but in order to have a solid microscope that biologists are going to use it needs a bit more work in that direction. The GUI in microscope is extremely basic and designed for quick testing. For a microscope system aimed at biological users we would recommend using Microscope-Cockpit, our paper is now referenced and a supplemental figure shows an example of its interface, or implementing an alternative more specialised GUI. We have released Python-Microscope as a separate package to separate low level hardware control from a GUI front end, enable relatively easy automated control of microscope systems directly from Python, or allow others to create GUI base interfaces without having to deal with interfacing to specific hardware.

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Referee #3

Evidence, reproducibility and clarity

Pinto et al present a new python based software to control microscopes. Overall the work is very interesting and will help microscopists to accelerate their development by providing new tool to integrate the different hardwares.

A few aspects commented below need to be clarified to help potential future users to integrate the software for the correct microscopes/hardware.

In general the software is mostly targeted to developers that want to build microscopes, as they mention in the discussion. Some positive features are (1) the ability to have experiments as scripts, (2) the software triggering, (3) the device-server structure, and (4) the ability to have virtual devices to try out the code and the testing I see in the github page. I think it's robust especially and mostly for the device-layer of the software. It's also positive that one can install it in python and import it in your programs, so it can be incorporated into other software fairly easy.

I miss more information regarding the latency of the device-server and software triggering, how fast can it be? How much delay would you have between computers/devices? For example, could we have the devices sincronized at the microsecond range? I think this is super important so that the reader knows if it's worth using a software triggering approach with Python-Microscope or they should buy a DAQ instead. It's good though that they don't want to limit themselves to software triggering but also mention hardware triggering, but it's important to better explain where are the limitations.

I also miss information about the triggering, do the software offer a platform that can synchronize devices, or that's more left to the developer to do? They say they can generalize to arbitrarily complex devices so therefore I think it needs to be specified how. Same with the server feature, how fast is that link?

Some critical comments are that, first of all there are not so many drivers yet available (for example Hamamatsu camera). I guess this paper is also to show proof of concept and then upon interest they will include more devices, but in that case it should be more documented how one can contribute to the project and generate new drivers. For example, if we want to try it tomorrow in our setups, and we have a specific device such as an Hamamatsu camera, What should we do? Should we contact the authors, write an issue in the github page or write the driver ourself?

Second, the graphical interface is maybe good enough for developers and builders but in order to have a solid microscope that biologists are going to use it needs a bit more work in that direction.

Significance

Microscope control software, especially is open source, can help the rapid integration of new hardware and accelerate overall microscopy development.

I see this paper as an important starting point platform for future more user friendly Python-microscope controlling software.

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Referee #2

Evidence, reproducibility and clarity

This manuscript describes Python-Microscope, a library/framework written in Python to control custom-built microscopes. Modern light microscopes consist of many computer controllable components and data sensors, and software has become an integral component of such systems. Microscopy is such a fast moving and diverse technology that a significant (>25%?) fraction of microscope systems can not be cookie-cutter, standardized systems, but are custom-built, assembled using commercial microscope stands and/or hardware from vendors such as Thorlabs. For many, creating the software to control such custom-built systems is more laborious and difficult than building the actual optical setup, and software toolkits to make this easier (such as the one presented in this manuscript) are of great interest to everyone working in this area. Python is at the moment probably the most widely used computer programming language by scientists, and a well-thought-out environment for microscope control from the Python language is a welcome addition.

The introduction does a good job describing the current situation (using multiple software from multiple vendors simultaneously, Micro-Manager, Labview), although it could be highlighted a bit more that several groups have created custom Python code for microscope control (such as https://github.com/ZhuangLab/storm-control, https://github.com/Ulm-IQO/qudi, https://github.com/fedebarabas/tormenta, https://github.com/AndrewGYork/tools), some with at least the hope that their code will be generally usable. It also could be noted that the Micro-Manager device abstraction layer has been accessible from Python for more than a decade (currently the Python 3 interface is at https://github.com/micro-manager/pymmcore).

Manuscripts describing software tools have to balance the goal to "announce" and advertise the software package with the goal to objectively explain the design principles and choices made. In my opinion, this manuscript finds a nice balance, and leaves the reader with a decent understanding of the capabilities, advantages, limitations and high level architecture of the Python-Microscope package. Possible exceptions are the use of the word "elegant" in the abstract, and extensive use of the word "bespoke" that I mainly know from real estate agent language and that likely is confusing to many readers for whom English is a second language.

As far as I am aware, "Microscope" is the most developed microscope abstraction layer written in pure Python. Remarkably, its design (device classes that inherit from a device-base class and have their own function calls, supplemented with "Settings" that can be declared by each device), is extremely similar to that of the Micro-Manager device abstraction layer (where "Settings" are called "Properties"), with the main difference being that one is written in Python and the other in C++ with C bindings. Writing these device classes in Python hopefully brings the advantage that more people can write them, however, the Micro-Manager C interface has the advantage that it can be used from any programming language on any platform, hence is more future proof than pure Python code. The downside of having multiple microscope device abstraction layers is that resources will be diluted and confuse partners in industry (which toolkit should they support with their limited resources?). The number of devices supported is currently much, much greater in the Micro-Manager platform than in Microscope, and a translation layer to make Micro-Manager device adapters in Microscope does not seem out of the question, and could possibly benefit many.

Expected audience:

This manuscript will be of interest to those scientists who build/assemble their own microscope systems and write software code to control their operation.

Field of expertise:

I think a lot about microscope control software and how it can help scientists do their experiments.

Significance

see above.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, Pinto et al. report Python-Microscope, a new open-source Python library for microscopy control. The new library lets microscope builders implement individual microscope devices as Python Classes with devices specific parameters and methods. Furthermore, the new Python library supports remote procedural calls and turns individual devices into a resource accessible over a network. Moreover, it has been designed to support hardware as well as software triggers. Finally, it provides several developer-friendly features; it is equipped with simple GUI programs for different device types, and it can simulate devices without the need for physical access to the hardware.

Major comments:

1. The authors highlight in their conclusion that the new Python library has the potential to accelerate and expand microscopy development. I agree with this statement since classes and methods do not need to be written in Python from scratch anymore. However, I would recommend that the authors include in their conclusion the value of the library for reproducibility if the final python acquisition code is shared along with publications. Nowadays, scientists frequently write in their publications that LabView or a specific commercial scope's acquisition software was used without any acquisition code. Python-Microscope would have the potential to change this trend, and the authors need to stress this aspect and its value for reproducibility in science accordingly.
2. The authors need to provide a more comprehensive overview of the currently used data acquisition strategies in their introduction. Currently, they highlight the acquisition software provided by vendors for data acquisition (mainly used by life scientists and not necessary scope builders/developers), Micro-Manager (mainly used by life scientists; currently also restricted to wide-field systems), and LabView (for advanced microscope systems; used by advanced developers). However, most advanced microscope builders use MatLab (Chmyrov et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2556, Ta et al. Nature Communications (2015) - https://doi.org/10.1038/ncomms8977 , etc.), Python (York et al. Nature Methods (2013) - https://doi.org/10.1038/nmeth.2687, etc.), and LabView to write their acquisition software. Since the manuscript focused on advanced microscopes, the authors need to position their library with respect to Matlab and Python's current use as well.
3. The authors need to give (1) software provided by vendors, (2) LabView, and (2) Micro-Manager, more credit. (1) Several microscope vendors (e.g., Abberior Instruments - https://imspectordocs.readthedocs.io/en/latest/specpy.html ) allow their scopes can be externally controlled to enable the execution of customer-driven acquisition strategies which the vendor's acquisition software itself might not have implemented with. The authors might want to include that scope vendors aim for more customer modifiable acquisition software. (2) The authors criticize that LabView code can be hard to understand, reproduce and maintain. However, similar to writing good code in general, there are best practice strategies for writing good LabView code to ensure scalability, readability, and maintainability available as well (https://learn.ni.com/learning-paths/labview-core-3-2016-english ). The primary problem might lie more on the side of lousy coding practice than on LabView's side to perform appropriately. (3) The authors should include the current effort by Pinkard et al. (Pinkard et al. Nature Methods (2021) - https://doi.org/10.1038/s41592-021-01087-6 ) in their discussion.
4. The authors might want to explain how they plan to facilitate the library's adoption and the long-term maintenance within the microscopy community. Do they plan to create a new category on Image.sc, which would allow the community to interact with the developers? etc. Furthermore, who will keep writing wrappers to the libraries provided by the vendors? etc Several useful software packages have been written in the past, but their existence was often not for long (after 2-3 years, most packages simply can not be used anymore). The concept of software maintenance is frequently not addressed/considered. Therefore, could the authors expand this aspect in an additional section of their paper?
5. The authors stress using their library for complex scopes but do not provide an example of complex implementation (they only provide paper references). Only a code for a simple time-series is provided. It would be very beneficial to provide the code for implementing a complex microscope and its GUI with the author's library as separate figures or in the paper's supplement. This would also support point 1 in the review.

Minor comments:

1. It would help the paper if several phrases would be changed: a. Title: 'Python-Microscope: High-performance control of arbitrarily complex and scalable bespoke microscopes." To: e.g., Python-Microscope: A new open-sources Python library for the control of microscopes Why? The authors use the word "high-performance" to address their Python library's trigger feature within the text. Unfortunately, that is not how most people would use the term for. Therefore, it should be avoided not only in the title but throughout the text. Furthermore, the word "complex" combined with microscopes should be avoided. A complex microscope is, for most microscope builders, a microscope that needs precise times and synchronization, includes several feedback active feedback loops, incorporates several devices, is very stable, etc. The context in which the term "complex microscopes" is used here is when the authors talk about the library's features to connect devices to servers either locally or remotely. I agree that the library can connect devices over arbitrary complex networks, but using the term "arbitrary complex microscopes" would be misleading considering the library's current speed limitations, the limited number of currently integrated devices, etc. b. Various section titles: "Libraray features" would be more suitable than "Use Cases" since the individual new features at the new library are described in this section. Also, the description of the individual features should be mentioned more accurately. The following list might be a better, more accurate fit: (1) "Device modularity" instead of "Device independence." Also, the current title "Write once, run with any device" is inaccurate since the wrapper for multiple devices has not been implemented. (2) "Experiment- and scope-specific layout" instead of "Experiments as programs." (3) "Complex network integration" instead of "Easy implementation of complex systems and scalability" (see reasoning under point a.) (4) "Hardware and software trigger integration" instead of "High performance, " (5) "Developer-friendly programming features" instead of "Simple development tool." c. The authors should avoid using the term "Microscope" when talking about "Python-Microscope." It facilitates the manuscript's readability since it is occasionally not evident in the paper if they refer to the library or a microscope. d. The authors should avoid the phrase "pythonic software platform" in the abstract since Python-Microscope is a library / Python package and not a software platform. Furthermore, the term "pythonic" describes the desired way to write Python code. It means code that does not just get the syntax right but follows the Python community conventions and uses the language in the way it is intended to be used. Instead, it might be advisable to write, "Python-Microscope offers elegant Python-based tools to control microscopes...".
2. Figure 1 should be supported by comments, e.g., #Load packages, #Parameter Initialization, #Create Devices, # Set camera parameters, etc.
3. The paragraph under the section "Experiments as programs" about the advantages of using Python (starting from "We have developed the software in Python, ...") should be moved into the Introduction section.

Significance

The field of microscopy emphasizes more and more openness and transparency of methods and tools being used to accelerate science, but also to guarantee reproducibility.

The authors' library is another step in the right direction. It is open, transparent, tries to satisfy multiple tool developers' needs to make the development of microscopes faster, easier, and more approachable/user-friendly. Although it can not yet be used for arbitrarily complex microscopes, it has the potential to do so in the future. For now, the authors need to manage to incorporate and involve microscopy developers' needs and requirements in the best possible way to be able to design the library as holistic as possible.

I am a physicist and microscope builder and have so far used MatLab, LabView, and Imspector as well as Python scripts to control microscopes, and I will definitely test the authors' library on my own.

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Reply to the reviewers

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We thank the reviewers for their constructive and critical feedback on our original manuscript.

Reviewer #1 (Evidence, reproducibility and clarity (Required)): In this study, the authors explored the tissue-specific regulation of DT size using both global and targeted deletion of Fgf9. They found cell hypertrophy and mineralization dynamics of the DT, as well as transcriptional signatures from skeletal muscle but not bone, were influenced by the global loss of Fgf9. Deletion of Fgf9 in skeletal muscle leads to postnatal enlargement of the DT. However, the innovation of this paper is not enough, the phenotypes of global deletion of Fgf9 were previously reported, most of the data in this paper are mainly descriptive analysis of the phenotypes, and internal cellular and molecular mechanisms were not well investigated.

Here are the major issues:

1.The data showed that fewer osteoclasts were present at both E16.5 and P0 in Figure 2R, V. Whether FGF9 affects both osteogenesis and osteoclast formation?

• Authors’ response to Reviewer: Thank you for your feedback. We revised this manuscript to reflect the concerns of Reviewer 1 related to the lack of cellular and molecular mechanisms as described below. **Based on this question from the Reviewer, we have revised our discussion to clarify our findings as follows: “From our EdU proliferation assays, we observed a decline in cell proliferation in Fgf9null attachments, suggesting an accelerated chondrocyte maturation. Though we saw similar levels of Pthlh expression (a chondrocyte hypertrophy suppressor) in both WT and Fgf9null attachments, we also saw increased expression of Gli1 (a marker of chondrocyte hypertrophy) localized to the attachment in Fgf9null embryos compared to WT embryos. This decrease in proliferation was in parallel with increased hypertrophy of chondrocytes adjacent to the attachment cells within the Fgf9null DT, which may have led to a rapid expansion of matrix in the DT. Even though the DT was enlarged in Fgf9null mutants, we found fewer Sost+ cell clusters in their DTs compared to WT mice. Mature osteocytes express Sost (Winkler et al., 2003), and fewer Sost+ cells may indicate an impaired ability of Fgf9null osteoblasts to embed and mature into osteocytes. Overexpression of FGF9 in the perichondrium has been previously shown to suppress chondrocyte proliferation and limit bone growth in the limb (Karuppaiah et al., 2016); in our study, we found that loss of Fgf9 globally leads to an accelerated enlargement of chondrocytes in the tuberosity. This accelerated enlargement may limit the ability of these cells to deposit matrix and mineral and therefore limit osteocyte differentiation. We also found fewer osteoclasts in the Fgf9null DT which mirrors previous reports using the same mutation to study the length and vascularity of developing limb (Hung et al., 2007). Because the DT is enlarged and resides on the surface of a shortened bone, this phenotype may elucidate a divergent role of FGF9 in patterning of an arrested (e.g., attachment) growth plate compared to a regular (e.g., long bone) growth plate. This includes unexplored roles of FGF9 in vascularity of the tendon attachment and formation of bone ridges that overlap with or deviate from its role in growth plate development that are beyond the scope of the current study.”

1. RNA-sequencing analysis showed the decreased expression of mitochondria/ energy and lipid associated genes in Fgf9 null muscle compared to WT muscle, how does this relate to the enlargement of the DT? What are the detailed molecular mechanisms?

• Authors’ response to Reviewer:
• Based on this question from the Reviewer, we have revised our discussion to reflect the potential molecular mechanisms related to muscle mitochondria, fiber type, and metabolism as follows:

“Fgf9 is expressed in muscle during embryonic stages, which we and others have observed using ISH (Colvin et al., 1999; Garofalo et al., 1999; Hung et al., 2007; Yang and Kozin, 2009). Previous work has established a connection between Fgf9 and muscle, as treatment of muscle and muscle progenitor cells with FGF9 slows maturation, enhances proliferation, and decreases expression of various myogenic genes (Huang et al., 2019). This study found supporting evidence that Fgf9 expression in muscle may be a limiting factor in tuberosity growth. However, it remains unknown how other FGFs and their receptors, FGFRs, regulate superstructure and attachment formation. In this study, we identified potential mediators of skeletal muscle metabolism in Fgf9null muscle, including downregulated mitochondrial-related genes associated with oxidative respiration and proton transport (i.e., Slc36a2 and Ucp1, amongst others). In cultured myoblasts, FGF9 can inhibit myogenic differentiation potentially via increased production of Myostatin (Huang et al., 2019), a well-established mediator of fast glycolytic muscle fibers (Girgenrath et al., 2005; Hennebry et al., 2009). While the role of FGF9 in myoblast fusion has been investigated in vitro, its effect on muscle fiber type and fiber metabolism (i.e., oxidative vs. glycolytic) has not yet been explored. Our findings from bulk RNA-seq of Fgf9null muscle point to potential mechanisms in muscle metabolism that may contribute to the enlarged phenotype that is mimetic of that found in Myostatin deficient mice and other animals (Elkasrawy and Hamrick, 2010; Hamrick et al., 2002). Additionally, further investigations are needed to investigate the potential role of Fgf9 in mitochondrial function and lipid metabolism. Recent work by Huang et al. also identified FGF9 as a potent regulator of calcium signaling and homeostasis in myoblast culture in vitro, and calcium release from the sarcoplasmic reticulum in muscle plays a critical role during embryonic skeletal myogenesis via ryanodine receptor 1 (RYR1). Although Ryr1 was not significantly different in between Fgf9null and WT muscle in the present study, we did find that calmodulin-associated genes (e.g., Calm4, Calml3, Camsap3, Calm5) were all significantly upregulated in Fgf9null muscle compared to WT muscle. Calmodulin interacts with RYR1 and its activation is required for intracellular binding of calcium (Newman et al., 2014, 1). Calmodulin is a crucial component of the calcium signal transduction pathway and also plays an important role in lipid and glucose metabolism (Nishizawa et al., 1988). Taken together, our findings along with recent work by Huang et al. support more mechanistic studies to investigate the metabolic effects of loss and gain of function of Fgf9 on skeletal muscle as well as the muscle secretome.”

Reviewer #1 (Significance (Required)):

R1 The authors compared the phenotypes between globally and muscle-specifically deletion of Fgf9 in mice, and found that Fgf9 secreted by muscle may induced the enlargement of the DT. However, the detailed molecular mechanisms were not well investigated.

**Referees cross-commenting**

R2 I do not disagree with Rev 1, but I do not think such a task is so trial reason why I don't suggest; it could take years to determine molecular mechanisms of anything. The authors could expand the discussion, offer some possibilities. If they had some RNAseq data they maybe could suggest some of the key signaling pathways involved.

**Referees cross-commenting**

R1 We still suggested that the internal cellular and molecular mechanisms should be well investigated in this papaer.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

• This paper deals with an important topic which is exact molecular mechanisms regulating the growth of bony tuberosities; because this region is essential for force transmission and movement.
• Based on the previous information they had that in the global KO of the gene FGF9 the deltoid muscle is enlarged; and this muscle is in a very important tuberosity; they decided to look at FGF9 as a potential genetic regulator.

• The manuscript is clear, objective, concise. Very clear. Authors used both the global and targeted deletions, very high reproducibility. Reviewer #2 (Significance (Required)):

• This manuscript advances several areas since we know little about the mechanisms controlling local mechanisms of tuberosities. It also advances our knowledge of FGF9. There were several studies before mostly in vitro showing that FGF9 when added to muscle cells could arrest myogenesis, but the types of experiments in vivo had not been performed yet. The authors used an array of methods; the studies are unbiased and very rigorous and also they always show all experimental points, which is excellent. The conclusions are supported by the data.

• The main suggestion for authors: They essentially do not discuss the nature of the potential muscle to bone signaling occurring when they target the deletion of FGF9 in skeletal muscles and muscles enlarge and there is a series of adaptions in the tuberosity. Do the authors believe this to be all the genetic changes or potentially through secreted myokines? In the paper of Huang et al, 2019 the authors document an effect of FGF9 in intracellular calcium homeostasis/signaling; could this be part of the mechanism? Perhaps the authors could propose a model?

Authors’ response to Reviewer:

• Future studies could investigate the secretome of muscle in Fgf9null or muscle-specific knockouts, as well as assess calcium signaling homeostasis in Fgf9 mutant muscles. We did find calcium- and ion-associated genes in the RNAseq and revised the discussion to include this information.
• Based on this question from the Reviewer, we have revised our discussion to reflect the potential molecular mechanisms related to muscle mitochondria, fiber type, and metabolism as follows: “Fgf9 is expressed in muscle during embryonic stages, which we and others have observed using ISH (Colvin et al., 1999; Garofalo et al., 1999; Hung et al., 2007; Yang and Kozin, 2009). Previous work has established a connection between Fgf9 and muscle, as treatment of muscle and muscle progenitor cells with FGF9 slows maturation, enhances proliferation, and decreases expression of various myogenic genes (Huang et al., 2019). This study found supporting evidence that Fgf9 expression in muscle may be a limiting factor in tuberosity growth. However, it remains unknown how other FGFs and their receptors, FGFRs, regulate superstructure and attachment formation. In this study, we identified potential mediators of skeletal muscle metabolism in Fgf9null muscle, including downregulated mitochondrial-related genes associated with oxidative respiration and proton transport (i.e., Slc36a2 and Ucp1, amongst others). In cultured myoblasts, FGF9 can inhibit myogenic differentiation potentially via increased production of Myostatin (Huang et al., 2019), a well-established mediator of fast glycolytic muscle fibers (Girgenrath et al., 2005; Hennebry et al., 2009). While the role of FGF9 in myoblast fusion has been investigated in vitro, its effect on muscle fiber type and fiber metabolism (i.e., oxidative vs. glycolytic) has not yet been explored. Our findings from bulk RNA-seq of Fgf9null muscle point to potential mechanisms in muscle metabolism that may contribute to the enlarged phenotype that is mimetic of that found in Myostatin deficient mice and other animals (Elkasrawy and Hamrick, 2010; Hamrick et al., 2002). Additionally, further investigations are needed to investigate the potential role of Fgf9 in mitochondrial function and lipid metabolism. Recent work by Huang et al. also identified FGF9 as a potent regulator of calcium signaling and homeostasis in myoblast culture in vitro, and calcium release from the sarcoplasmic reticulum in muscle plays a critical role during embryonic skeletal myogenesis via ryanodine receptor 1 (RYR1). Although Ryr1 was not significantly different in between Fgf9null and WT muscle in the present study, we did find that calmodulin-associated genes (e.g., Calm4, Calml3, Camsap3, Calm5) were all significantly upregulated in Fgf9null muscle compared to WT muscle. Calmodulin interacts with RYR1 and its activation is required for intracellular binding of calcium (Newman et al., 2014, 1). Calmodulin is a crucial component of the calcium signal transduction pathway and also plays an important role in lipid and glucose metabolism (Nishizawa et al., 1988). Taken together, our findings along with recent work by Huang et al. support more mechanistic studies to investigate the metabolic effects of loss and gain of function of Fgf9 on skeletal muscle as well as the muscle secretome.

In conclusion, this work established a new role of skeletal muscle derived Fgf9 during skeletal development and tuberosity growth. Additionally, our unbiased transcriptomic approaches and rigorous analyses identified new potential mechanisms associated with muscle development, mitochondrial bioenergetics, and muscle metabolism that warrant further investigation into the role of FGF9 in muscle-bone crosstalk.”

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Referee #2

Evidence, reproducibility and clarity

This paper deals with an important topic which is exact molecular mechanisms regulating the growth of bony tuberosities; because this region is essential for force transmission and movement. Based on the previous information they had that in the global KO of the gene FGF9 the deltoid muscle is enlarged; and this muscle is in a very important tuberosity; they decided to look at FGF9 as a potential genetic regulator.

The manuscript is clear, objective, concise. Very clear. Authors used both the global and targeted deletions, very high reproducibility.

Significance

This manuscript advances several areas since we know little about the mechanisms controlling local mechanisms of tuberosities. It also advances our knowledge of FGF9. There were several studies before mostly in vitro showing that FGF9 when added to muscle cells could arrest myogenesis, but the types of experiments in vivo had not been performed yet. The authors used an array of methods; the studies are unbiased and very rigorous and also they always show all experimental points, which is excellent. The conclusions are supported by the data.

The main suggestion for authors: They essentially do not discuss the nature of the potential muscle to bone signaling occurring when they target the deletion of FGF9 in skeletal muscles and muscles enlarge and there is a series of adaptions in the tuberosity. Do the authors believe this to be all the genetic changes or potentially through secreted myokines? In the paper of Huang et al, 2019 the authors document an effect of FGF9 in intracellular calcium homeostasis/signaling; could this be part of the mechanism? Perhaps the authors could propose a model?

Referees cross-commenting

I do not disagree with Rev 1, but I do not think such a task is so trial reason why I don't suggest; it could take years to determine molecular mechanisms of anything. The authors could expand the discussion, offer some possibilities. If they had some RNAseq data they maybe could suggest some of the key signaling pathways involved.

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Referee #1

Evidence, reproducibility and clarity

In this study, the authors explored the tissue-specific regulation of DT size using both global and targeted deletion of Fgf9. They found cell hypertrophy and mineralization dynamics of the DT, as well as transcriptional signatures from skeletal muscle but not bone, were influenced by the global loss of Fgf9. Deletion of Fgf9 in skeletal muscle leads to postnatal enlargement of the DT. However, the innovation of this paper is not enough, the phenotypes of global deletion of Fgf9 were previously reported, most of the data in this paper are mainly descriptive analysis of the phenotypes, and internal cellular and molecular mechanisms were not well investigated.

Here are the major issues:

1.The data showed that fewer osteoclasts were present at both E16.5 and P0 in Figure 2R, V. Whether FGF9 affects both osteogenesis and osteoclast formation?

2.RNA-sequencing analysis showed the decreased expression of mitochondria/ energy and lipid associated genes in Fgf9 null muscle compared to WT muscle, how does this relate to the enlargement of the DT? What are the detailed molecular mechanisms?

Significance

The authors compared the phenotypes between globally and muscle-specifically deletion of Fgf9 in mice, and found that Fgf9 secreted by muscle may induced the enlargement of the DT. However, the detailed molecular mechanisms were not well investigated.

Referees cross-commenting

We still suggested that the internal cellular and molecular mechanisms should be well investigated in this papaer.

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Reply to the reviewers

Dear Dr. Monaco,

Thank you for reviewing our manuscript entitled ‘Discovery of re-purposed drugs that slow SARS-CoV-2 replication in human cells’. We are pleased to see that the reviewers make suggestions that will strengthen the paper. With cases of COVID-19 rising at dramatic levels in some parts of the world, we are anxious to see our results published in a peer-review journal.

Please find below a detailed response to the comments is shown in bold. We can perform the additional experiments and make changes to the manuscript within 3 weeks of a journal agreeing to consider our paper.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

**Summary:**

Pickard et al. present in the manuscript entitled "Discovery of re-purposed drugs that slow SARS-CoV-2 replication in human cells" a new screen of FDA approved drugs against SARS-CoV-2. The authors based their screen on Vero and HUH7 cell lines. The methods applied for screening including the SARS-Cov-2-ΔOrf7a-NLuc modified virus are properly designed and preformed. This is an interesting study that finds several potential drugs that might be effective as anti SARS-CoV-2 therapies. However, such experiments have been done throughout the last year and the novelty and importance of these findings are questionable.

Regarding this point, there are several studies that have attempted to identify compounds that impact on SARS-Cov2 infection; however, these do not specifically focus on the replication of the virus (studies have used viability markers and staining of viral proteins but many of the compounds identified exert their effects on the virus uptake). Whilst SARS-CoV2-Nluc viruses have been developed these have been used for infection studies to measure the amount of virus taken up by cells and have not further explored how they impact on virus replication. Therefore, we feel that our study shows that a reporter virus can be used to reflect virus replication.

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**Major comments:**

1. Most the experiments presented are only done twice, while in the screen itself it should not be a problem, for verifying the drugs identified at least three experiments are suggested (Figure 5 and Supplemental Figure 6) At the time of submission there was an urgent need to make our data accessible to the scientific community. Therefore, we performed some experiments with n=2. We used n=2 to validate the screen and each time we got the same experimental outcome. We would perform further repeats for the figures mentioned for publication.

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To strengthen the results of the screen, the wild type virus should also be tested for plaque reduction assay with these nine drugs.

We will perform these experiments and present these data in the manuscript. We have already performed immunostaining of WT-virus infected cells and could include this as an alternative.

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Identification of antivirals is important for SARS-CoV-2 and other coronaviruses, regardless of the presence or effectiveness of vaccines. I think the abstract and introduction should be written to emphasize this point (instead of trying to underestimate the vaccine effectiveness). Similarly, the authors ignore the relative failures of known antivirals (known to inhibit SARS-CoV-2 replication in vitro like Remdesavir) in clinical trials and suggest starting clinical trials with their screen results. I think that this suggestion is premature and require several more studies (including animals studies) before initiating clinical trials.

We will re-write this section of the manuscript. We have identified all compounds that have been evaluated in the AGILE clinical trial, and these compounds failed to show a patient benefit and also failed to impact on virus replication in human cells.

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**Minor comments.**

1. The errors bars are not defined throughout all the figures. I am not sure that error bars are even meaningful if experiments only done twice, I recommend showing the two results for each point. We will add additional repeats or as the reviewer suggests we could add the two points.

Figure 1E and the tables especially supp tables 3 and 4? don't have legends.

Apologies, this will be amended.

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Most graphs will benefit from presenting the results in logarithmic scale (all Luc counts/ qPCRs).

This can be changed if editors agree.

P6 in the Generation of functional SARS-CoV-2 virus section - a reference is missing "It has been reported that this aids the recovery of replicative virus (Insert ref 3)"

Apologies, this will be amended.

Reviewer #1 (Significance (Required)):

This is a well performed drug screen on two cell lines that identified new potential FDA approved drugs as anti-SARS-CoV-2 inhibitors. There are several studies that already been published or distributed as preprints that have done similar experiments in other cells lines including more relevant lung epithelial cells (for example PMC743673). This study does not verify the screen results by additional methods. However, in the current pandemic situation this study could be important and interesting to follow up.

I am a virologist; my expertise is in viral host interactions within infected cell.

We were unable to identify the paper which is referred to in the reviewer’s comments. We would aim to highlight further in the text that using the reporter virus, we are able to screen and identify compounds that impact on virus replication unlike many of the other studies.

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**Referee Cross-commenting**

No problem with the other comments

Reviewer #2 (Evidence, reproducibility and clarity (Required)): **Summary:**

In this manuscript, the authors report on the creation of a luciferase-encoding SARS-CoV-2 (deleted for orf7a) and the use of this virus to test infectability of multiple cell lines as well as perform a drug repurposing screen in two cell lines (Vero E6 and Huh7). Of the 35 drugs that blocked the virus replication they further identify 9 drugs that have a (mild) effect on replication when administered 24 hours post infection.

An important note here is that many studies which have identified potential therapeutics for SARS-Cov2 have performed experiments whereby cells are pre-treated with compounds prior to infection. We have been able to performed the same experiments and many of the drugs were unable to prevent replication after infection. The 9 compounds we have identified retain the ability to inhibit replication when applied post-infection. This sets our study apart from other screens that have been conducted for SARS-Cov2.

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**Major comments:**

1. Figure 2: What's the difference between "Luminescence counts above noise" in Fig 2B and "Luminescence counts per second" in Figure 2C,D ? It seems like there is no difference in luminescence between 1 PFU and 100 PFU (and if anything, the bassline for 1PFU is higher, >1.5M, compared to 100 PFU where is below 1M). One would expect more luminescence in the 100 PFU experiment, as seen in Fig 2B. Also in Fig 2B it does not mention how many replicates, or what does the **** stands for. Thank you for the comment. The difference in “luminescence counts above noise” and “luminescence counts per second” is set out in Figure 2A. When adding more virus the baseline level should increase, as also demonstrated in Supplemental Figure 3. However, the degree of background luminescence varies between virus batches, presumably due to the degree of cell lysis in each sample. You will note in the Supplemental figure that the baseline levels for our P4 viral stock is lower than P1. We performed the experiments in Figure 2C using virus P1 virus stocks and for Figure 2D we used P4 virus. For clarity this information will be included in the figure legend and the data presented at luminescence over background.

The authors do not explain why deleting orf7a was needed to generate the NLuc virus. Was there a rational for this?

Orf7a has been successfully removed from SARS-CoV and SARS-CoV2 in order to incorporate traceable proteins such as fluorescent or bioluminescent proteins. We describe this at the start of the results section. “Orf7a has previously been removed in SARS-CoV and SARS-CoV-2 and yielded infectious and replicative virus particles (Thi Nhu Thao et al, 2020; Xie et al, 2020a; Xie et al, 2020b)”.

Figure 5C - IC50 should be properly determined from compounds where the lowest concentration tested was still inhibitory (such as LY2835219 and panobinostat).

These experiments can be conducted, within 2 weeks. However we do not feel that this would provide additional information to the reader. The aim of these figures is to demonstrate that there are dose dependent effects of these compounds on the replication of SARS-CoV2.

Supplementary tables must be provided in an excel or similar file format. The PDF version is both unreadable and does not allow other researchers to probe the dataset for their own interests.

This would be amended during revision of our submission.

**Minor comments:**

1. Intro: "SARS-CoV-2 infection in patients with COVID-19 can result in pulmonary distress, inflammation, and broad tissue tropism". Broad tissue tropism is not a result of infection, please rephrase. Patients with COVID-19 are reported to have liver and kidney damage. This could be a direct result of SARS-CoV2 infection or indirectly via the cytokine storm. Our data shows that kidney and liver cells are highly susceptible to SARS-CoV2 infection and support replication, in culture. We thank the reviewer for their comment and we will rephrase this statement and cite relevant literature.

Fig S1D - why are the MOI different for WT (moi 0.1) and NLuc mutant (moi 1) ?

This was used to demonstrate the lack of replication of the WT virus in lung epithelial cells, the same MOI used in Vero cells demonstrates that the levels of the nucleocapsid protein increases when compared to other cell types. We have also used an MOI of 10 for the NLuc virus to be able to detect the NLuc protein. This information would be added to the figure legend.

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Fig S3 - using volume of virus in ul is problematic, as it doesn't allow for proper comparison between the passages. The author would express the virus amount in PFU or MOI.

This will be amended

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Fig S5 - in panel A - what do the colors represent? What is 0-1?. The number of repetitions for each panel should be indicated.

Apologies, relative expression should have been added alongside the scale. N=3 for this experiments this will be added to the figure legend.

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The "NLuc activity as a marker of virus replication" and "SARS-CoV-2 replication screen validation" are largely overlapping and should be edited.

We would combine these sections.

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Methods: "Generation of functional SARS-CoV-2 virus" - the author confuse "virus" with "plasmid". They should also include the reference marked "(Insert ref 3)"

Apologies, this will be amended

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Reviewer #2 (Significance (Required)):

1. My main concern is that a very similar, if not identical, NLuc encoding virus has been reported in October 2020 (https://www.nature.com/articles/s41467-020-19055-7#Sec9). While the authors cite this paper, they only do so to say that "Orf7a has previously been removed in SARS-CoV and SARS-CoV-2 and yielded infectious and replicative virus particles", without mentioning this was done to generate the same NLuc carrying virus reported in their work. Thus the generation of this virus is not a "new tool" as the authors would seem to suggest. Whilst this is not the first use of a NLuc SARS-CoV2 virus, this is the first time that the virus has been utilised to screen for compounds that effect replication. The study mentioned does not screen nor monitor the replication of the virus, the authors do monitor the capability of the virus to infect cells only during the first 24 hours.

While drug repurposing screens have been performed, the addition validation in Vero E6 and Huh7 cells is of some interest to those working on anti-viral therapies, given that the authors change their supplementary tables to a format that can be accessible by other researchers.

This will be amended for the submission.

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My expertise: I study virus-host interactions (not coronaviruse). In the last year I have been involved in several drug repurposing efforts against SARS-CoV-2.

**Referee Cross-commenting**

No problem with the other comments.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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---

Referee #2

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors report on the creation of a luciferase-encoding SARS-CoV-2 (deleted for orf7a) and the use of this virus to test infectability of multiple cell lines as well as perform a drug repurposing screen in two cell lines (Vero E6 and Huh7). Of the 35 drugs that blocked the virus replication they further identify 9 drugs that have a (mild) effect on replication when administered 24 hours post infection.

Major comments:

1. Figure 2: What's the difference between "Luminescence counts above noise" in Fig 2B and "Luminescence counts per second" in Figure 2C,D ? It seems like there is no difference in luminescence between 1 PFU and 100 PFU (and if anything, the bassline for 1PFU is higher, >1.5M, compared to 100 PFU where is below 1M). One would expect more luminescence in the 100 PFU experiment, as seen in Fig 2B. Also in Fig 2B it does not mention how many replicates, or what does the ** stands for.
2. The authors do not explain why deleting orf7a was needed to generate the NLuc virus. Was there a rational for this?
3. Figure 5C - IC50 should be properly determined from compounds where the lowest concentration tested was still inhibitory (such as LY2835219 and panobinostat).
4. Supplementary tables must be provided in an excel or similar file format. The PDF version is both unreadable and does not allow other researchers to probe the dataset for their own interests.

Minor comments:

1. Intro: "SARS-CoV-2 infection in patients with COVID-19 can result in pulmonary distress, inflammation, and broad tissue tropism". Broad tissue tropism is not a result of infection, please rephrase.
2. Fig S1D - why are the MOI different for WT (moi 0.1) and NLuc mutant (moi 1) ?
3. Fig S3 - using volume of virus in ul is problematic, as it doesn't allow for proper comparison between the passages. The author would express the virus amount in PFU or MOI.
4. Fig S5 - in panel A - what do the colors represent? What is 0-1?. The number of repetitions for each panel should be indicated.
5. The "NLuc activity as a marker of virus replication" and "SARS-CoV-2 replication screen validation" are largely overlapping and should be edited.
6. Methods: "Generation of functional SARS-CoV-2 virus" - the author confuse "virus" with "plasmid". They should also include the reference marked "(Insert ref 3)"

Significance

1. My main concern is that a very similar, if not identical, NLuc encoding virus has been reported in October 2020 (https://www.nature.com/articles/s41467-020-19055-7#Sec9). While the authors cite this paper, they only do so to say that "Orf7a has previously been removed in SARS-CoV and SARS-CoV-2 and yielded infectious and replicative virus particles", without mentioning this was done to generate the same NLuc carrying virus reported in their work. Thus the generation of this virus is not a "new tool" as the authors would seem to suggest.
   1. While drug repurposing screens have been performed, the addition validation in Vero E6 and Huh7 cells is of some interest to those working on anti-viral therapies, given that the authors change their supplementary tables to a format that can be accessible by other researchers.

My expertise: I study virus-host interactions (not coronaviruse). In the last year I have been involved in several drug repurposing efforts against SARS-CoV-2.

Referee Cross-commenting

No problem with the other comments.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

Pickard et al. present in the manuscript entitled "Discovery of re-purposed drugs that slow SARS-CoV-2 replication in human cells" a new screen of FDA approved drugs against SARS-CoV-2. The authors based their screen on Vero and HUH7 cell lines. The methods applied for screening including the SARS-Cov-2-ΔOrf7a-NLuc modified virus are properly designed and preformed. This is an interesting study that finds several potential drugs that might be effective as anti SARS-CoV-2 therapies. However, such experiments have been done throughout the last year and the novelty and importance of these findings are questionable.

Major comments:

1. Most the experiments presented are only done twice, while in the screen itself it should not be a problem, for verifying the drugs identified at least three experiments are suggested (Figure 5 and Supplemental Figure 6)
2. To strengthen the results of the screen, the wild type virus should also be tested for plaque reduction assay with these nine drugs.
3. Identification of antivirals is important for SARS-CoV-2 and other coronaviruses, regardless of the presence or effectiveness of vaccines. I think the abstract and introduction should be written to emphasize this point (instead of trying to underestimate the vaccine effectiveness). Similarly, the authors ignore the relative failures of known antivirals (known to inhibit SARS-CoV-2 replication in vitro like Remdesavir) in clinical trials and suggest starting clinical trials with their screen results. I think that this suggestion is premature and require several more studies (including animals studies) before initiating clinical trials.

Minor comments.

1. The errors bars are not defined throughout all the figures. I am not sure that error bars are even meaningful if experiments only done twice, I recommend showing the two results for each point.
2. Figure 1E and the tables especially supp tables 3 and 4? don't have legends.
3. Most graphs will benefit from presenting the results in logarithmic scale (all Luc counts/ qPCRs).
4. P6 in the Generation of functional SARS-CoV-2 virus section - a reference is missing "It has been reported that this aids the recovery of replicative virus (Insert ref 3)"

Significance

This is a well performed drug screen on two cell lines that identified new potential FDA approved drugs as anti-SARS-CoV-2 inhibitors. There are several studies that already been published or distributed as preprints that have done similar experiments in other cells lines including more relevant lung epithelial cells (for example PMC743673). This study does not verify the screen results by additional methods. However, in the current pandemic situation this study could be important and interesting to follow up.

I am a virologist; my expertise is in viral host interactions within infected cell.

Referee Cross-commenting

No problem with the other comments

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Reply to the reviewers

Reviewer response

We thank the reviewers for their response. All reviewers find our study (potentially) interesting and/or a resource to gain further understanding on BAP1 molecular functions. They also have some common comments.

The reviewers would prefer to see further characterization of the interactions and their functional effects. We would have liked to address this but found for COPI that knockdown of these genes is lethal, whereas on the BAP1 side the interactions are mapped to the functionally critical C-terminus, making these experiments technically extremely challenging. These issues, unfortunately, preclude further validation studies at this point. Nevertheless, we do feel that the quality of our interaction dataset is such that it is be worth publishing these finding for this important tumor suppressor.

Most reviewers would like us to place the data more in context. To address this, we have extended the discussion, highlighting the essence of our findings and how we envisage this could impact BAP1 function.

Finally, both reviewer 1 and 3 would like the results section to be more succinct and we have shortened it to improve readability.

Other points are addressed in the point-by-point response to individual reviewers below.

Point-by-point response to reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Very interesting study on BAP1 tumor suppressor. The work needs further characterization of the interacting partners identified.

Reviewer #1 (Significance (Required)):

BAP1 is an important tumor suppressor mutated in several malignancies and the mechanism of action of this deubiquitinase are far from being completely understood.

This interesting work aimed at identifying novel cytoplasmic partners of BAP1 which can highly relevant to its tumor suppressor function. BAP1 is predominantly nuclear, but can also be found in the cytoplasm. New insights into the cytoplasmic functions of BAP1 are needed.

The manuscript is overall well written and the data are very solid.

The manuscript would need additional work before acceptance

**Comments**

Reviewer #1 1) The abstract can be improved to reflect the data of the manuscript.

Unfortunately, we do not understand what part of the abstract is meant by the reviewer, which makes it hard to address.

2) The result section, manuscript could emphasize the results rather that the technical aspects

We've improved readability of this part of the manuscript by moving technical parts that are not required for interpretation of the results to the material and method section, a supplementary text and a new supplemental figure 1 (causing the original numbering to shift).

3) It would be interesting to further investigate the significance of some key interactions

We agree that these questions are of importance (see reviewer 2 point 2, reviewer 3 point 1). We have tried to address these questions using gene knockdown techniques. However, the importance of regulation of protein transport and vesicle formation by COPI translates to lethal effects on cell viability upon knockdown of these genes making these experiments technically impossible to execute. Further functional investigation is technically and financially beyond the scope and possibilities of this paper.

4) The discussion is quite short and can put the findings in perspective

We've extended the discussion to place results into perspective, also regarding the potential role of BAP1 activity towards potential substrates (point 8). This will help to highlight the important findings of the research.

5) It would be interesting to test some cancer-associated mutations

The interaction is in the C-terminus of BAP1, which combines several functions[1, 2]. This would dramatically complicate the interpretation of results. Particularly the presence of the NLS, a major regulatory posttranslational modification[3] and the recruitment signal for nucleosomes could all interfere with BAP1 function independently.

6) Figure 4 can be improved

Thanks for this comment. We have increased readability of the figure by addition of schematic representations of the used constructs, a legend that explains the color-coding of the interactors. We have also removed dotted lines to make it less busy.

7) Yu et al MCB 2010 is one of the key papers on BAP1 purification and can be cited

We apologize for omitting this reference and have included it in the revised manuscript.

8) The authors can discuss potential substrates of BAP1 and mechanism of deubiquitination

We've extended the discussion to this extent.

**Referee Cross-commenting**

I agree with the comments of Reviewer #2

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

**Summary:**

BAP1 is a deubiquitinase that mainly functions to control H2Aub levels in nucleus. BAP1 is a tumor suppressor with mutations or deletions in several human cancers. Previous studies have identified many interacting proteins with BAP1, most notably its binding partners involved in PR-DUB complex, such as ASXL1/2, FOXK1/2, HCFC1, OGT etc. In this study, by using FRT-mediated recombination, the authors generated tagged-BAP1 expressed from its endogenous promoter and conducted AP-MS analysis to identify BAP1 interacting proteins in both nuclear and cytoplasmic fractions. These analyses identified several new BAP1-interacting proteins in cytoplasmic fractions, including histone acetyltransferase 1 (HAT1) and the heptameric coat protein complex I (COPI, which is involved in protein sorting and trafficking). The authors further confirmed the interactions between BAP1 and HAT1 (as well as a COPI subunit) at the endogenous level.

**Major comments:**

Overall, the current study has relatively limited data with limited scopes: basically a proteomic study focusing on one single protein (which has already been subjected to several proteomic studies in previous publications). There is a significant room for authors to improve this potentially interesting study (see below for specific comments), although this may take substantial additional efforts.

1. In the current manuscript, there is no data to further characterize the interactions between BAP1 and HAT1 (or COPI). For protein-protein interaction studies, readers generally are interested in information such as whether these bindings are direct or indirect (particularly for COPI because it contains multiple subunits), and which regions mediate the interactions?

Our mass spectrometry data suggests binding of BAP1 to be mediated through its C-terminus. Mutations of the KxKxx domain have shown that this motif is not involved. Mapping the interaction any more specifically is likely to be very difficult as the C-terminus of BAP1 is involved in many different functions and contains many important elements (ULD domain, CTE, NLS) required for its function. Mutational analysis aimed to map the interaction will induce many secondary effects as the protein localization and substrate targeting will be severely affected as shown by us and other research groups. Identifying what subunit of the COPI complex is mediating the interaction requires purification of these proteins along with purified full length active BAP1, for which attempts have been made but were still unsuccessful. Further investigation is technically and financially beyond the scope and possibilities of this paper.

No data to study the functional significance of the identified protein-protein interactions. This is a major weakness of the current study. For example, HAT1 is a histone acetyltransferase and mainly functions in the nucleus. Does the BAP1-HAT1 interaction in cytoplasm suggest that they have functions in cytoplasm independent of their canonical function in regulating transcription in the nucleus? Likewise, does BAP1-COP1 interaction suggest that somehow BAP1 is involved in regulating protein sorting and trafficking?

Please see our general response and reviewer 1 point 3.

The identified interactions appear to be weak. These proteins are located near the edge of the significance curve in volcano plots (Fig. 1C-1D and others). The IP data also appear to be weak; for example, see Fig. 5D, it's hardly to see COPA blot in BAP1 IP. The COPA IB signal from 5% input WCL is probably hundred-fold stronger than that from BAP1 IP. Weak interactions do not necessarily mean they are not important; however, there is no functional data to support this claim (see the point above).

The essence of our paper is that the interactions which are barely visible in figure 1, gain significance in the absence of endogenous BAP1 to the point where all COPI subunits are as confidently identified as previously validated BAP1 interactors like ASXL, FOXK and HCFC proteins (figure 4). Our quantifications indicate that the new interactors have lower stoichiometry, and this may explain why they were harder to identify. This observation is discussed in the discussion section.

It seems that the entire study focuses on one specific cell line. Repeat the analyses in other cell lines can help boost the robustness and significance of the study.

As discussed under the previous point, the removal of endogenous BAP1 was important for significance, and since BAP1 is a common essential gene, we don't have any other cell lines in which this would be possible. However, we have been able to confirm the HAT1 interaction with BAP1 in U2OS on endogenous levels (Fig 1E,F).

The major interacting proteins they identified from the cytoplasmic fraction are still those mainly localized in nucleus (such as HCFC1, FOXK1/2). A western blotting to show nuclear vs cytoplasmic fraction is required.

Our immunoblot containing cytoplasmic and nuclear input samples used for figure 4 show proper separation of fractions without major leakage as shown in supplemental figure 4 (Tubulin and Abraxas lane as cytoplasmic and nuclear markers respectively), while iBAQ data show a substantial amount of protein to be bound (stoichiometry.xls). This is corroborating with the sample correlation data shown in supplemental figure 5B which shows very little correlation between cytoplasmic and nuclear samples in the mass spectrometry experiment. These data show that the interactions of the cytoplasmic partners that are mainly localized in the nucleus are real interaction and are not due to mixing of cellular compartments.

**Minor comments:**

1. page 9 "A GFP coIP experiment of both GFP-BAP1 and the catalytic-dead BAP1 C91S mutant shows coimmunoprecipitation of HAT1 (Figure 1F)." here Fig. 1F should be Fig. 1E.

The Figure was indeed mislabeled. Because of the addition of a new supplemental figure for reviewer 1 point 2 some figure numbers have shifted. The old figure 1E has now become 1C and is now numbered accordingly.

Reviewer #2 (Significance (Required)):

The current study is limited in scope. Without functional data for these interactions, the overall significance of the study is likely limited.

**Referee Cross-commenting**

My overall assessment is similar to the other two reviewers (particularly reviewer 3): the study is rather descriptive, limited in scope, and lacks mechanistic understanding of BAP1 functions: for example, see reviewer 1 comment "it would be interesting to further investigate the significance of some key interactions"; reviewer 3 comment "The present manuscript contained very little information beyond description of BAP1 interactomes and subsequent validation of BAP1-COPI interaction. In the very least, I would recommend for the authors to explore contextual significances and/or regulations of the novel BAP1-COP1 interaction."

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In the present manuscript, Baas and colleagues seek to identify novel BRCA1-associated protein 1 (BAP1) interacting partners. To do so, the authors performed affinity purifications of different GFP-tagged BAP1 constructs in combination with mass spectrometry from either wild-type HeLa or those, which endogenous BAP1 expression had been knocked-out using CRISPR/Cas9. MS analysis of the pull-downs revealed COPI as a novel cytoplasmic interactor for the full-length GFP-BAP1 in addition to to other previously known BAP1 interactors such as HAT1, ASXL1/2, FOXK1/K2, OGT.

The authors subsequently went on to validate the BAP1-COPI interaction and observed that such interaction was independent of the canonical COPI binding motifs KxKxx present in the BAP1 C-terminus.

**Major comments:**

The present manuscript contained very little information beyond description of BAP1 interactomes and subsequent validation of BAP1-COPI interaction. In the very least, I would recommend for the authors to explore contextual significances and/or regulations of the novel BAP1-COP1 interaction.

Please see our general response and reviewer 1 point 3.

The present manuscript could be written in more concise manner.

We have shortened the results section as discussed under reviewer 1 point 2 to make it more concise.

Reviewer #3 (Significance (Required)):

While the present study may provide a resource to gain further understanding on BAP1 molecular functions, it is very difficult to appreciate the significance of the presence manuscript in the current descriptive form.

We have expanded the discussion to better explain the significance of our findings.

1. Sahtoe, D.D., et al., BAP1/ASXL1 recruitment and activation for H2A deubiquitination. Nat Commun, 2016. 7: p. 10292.
2. Ventii, K.H., et al., BRCA1-associated protein-1 is a tumor suppressor that requires deubiquitinating activity and nuclear localization. Cancer Res, 2008. 68(17): p. 6953-62.
3. Mashtalir, N., et al., Autodeubiquitination protects the tumor suppressor BAP1 from cytoplasmic sequestration mediated by the atypical ubiquitin ligase UBE2O. Mol Cell, 2014. 54(3): p. 392-406.

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Referee #3

Evidence, reproducibility and clarity

In the present manuscript, Baas and colleagues seek to identify novel BRCA1-associated protein 1 (BAP1) interacting partners. To do so, the authors performed affinity purifications of different GFP-tagged BAP1 constructs in combination with mass spectrometry from either wild-type HeLa or those, which endogenous BAP1 expression had been knocked-out using CRISPR/Cas9. MS analysis of the pull-downs revealed COPI as a novel cytoplasmic interactor for the full-length GFP-BAP1 in addition to to other previously known BAP1 interactors such as HAT1, ASXL1/2, FOXK1/K2, OGT.

The authors subsequently went on to validate the BAP1-COPI interaction and observed that such interaction was independent of the canonical COPI binding motifs KxKxx present in the BAP1 C-terminus.

Major comments:

The present manuscript contained very little information beyond description of BAP1 interactomes and subsequent validation of BAP1-COPI interaction. In the very least, I would recommend for the authors to explore contextual significances and/or regulations of the novel BAP1-COP1 interaction.

The present manuscript could be written in more concise manner.

Significance

While the present study may provide a resource to gain further understanding on BAP1 molecular functions, it is very difficult to appreciate the significance of the presence manuscript in the current descriptive form.

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Referee #2

Evidence, reproducibility and clarity

Summary:

BAP1 is a deubiquitinase that mainly functions to control H2Aub levels in nucleus. BAP1 is a tumor suppressor with mutations or deletions in several human cancers. Previous studies have identified many interacting proteins with BAP1, most notably its binding partners involved in PR-DUB complex, such as ASXL1/2, FOXK1/2, HCFC1, OGT etc. In this study, by using FRT-mediated recombination, the authors generated tagged-BAP1 expressed from its endogenous promoter and conducted AP-MS analysis to identify BAP1 interacting proteins in both nuclear and cytoplasmic fractions. These analyses identified several new BAP1-interacting proteins in cytoplasmic fractions, including histone acetyltransferase 1 (HAT1) and the heptameric coat protein complex I (COPI, which is involved in protein sorting and trafficking). The authors further confirmed the interactions between BAP1 and HAT1 (as well as a COPI subunit) at the endogenous level.

Major comments:

Overall, the current study has relatively limited data with limited scopes: basically a proteomic study focusing on one single protein (which has already been subjected to several proteomic studies in previous publications). There is a significant room for authors to improve this potentially interesting study (see below for specific comments), although this may take substantial additional efforts.

1. In the current manuscript, there is no data to further characterize the interactions between BAP1 and HAT1 (or COPI). For protein-protein interaction studies, readers generally are interested in information such as whether these bindings are direct or indirect (particularly for COPI because it contains multiple subunits), and which regions mediate the interactions?
2. No data to study the functional significance of the identified protein-protein interactions. This is a major weakness of the current study. For example, HAT1 is a histone acetyltransferase and mainly functions in the nucleus. Does the BAP1-HAT1 interaction in cytoplasm suggest that they have functions in cytoplasm independent of their canonical function in regulating transcription in the nucleus? Likewise, does BAP1-COP1 interaction suggest that somehow BAP1 is involved in regulating protein sorting and trafficking?
3. The identified interactions appear to be weak. These proteins are located near the edge of the significance curve in volcano plots (Fig. 1C-1D and others). The IP data also appear to be weak; for example, see Fig. 5D, it's hardly to see COPA blot in BAP1 IP. The COPA IB signal from 5% input WCL is probably hundred-fold stronger than that from BAP1 IP. Weak interactions do not necessarily mean they are not important; however, there is no functional data to support this claim (see the point above).
4. It seems that the entire study focuses on one specific cell line. Repeat the analyses in other cell lines can help boost the robustness and significance of the study.
5. The major interacting proteins they identified from the cytoplasmic fraction are still those mainly localized in nucleus (such as HCFC1, FOXK1/2). A western blotting to show nuclear vs cytoplasmic fraction is required.

Minor comments:

1. page 9 "A GFP coIP experiment of both GFP-BAP1 and the catalytic-dead BAP1 C91S mutant shows coimmunoprecipitation of HAT1 (Figure 1F)." here Fig. 1F should be Fig. 1E.

Significance

The current study is limited in scope. Without functional data for these interactions, the overall significance of the study is likely limited.

Referee Cross-commenting

My overall assessment is similar to the other two reviewers (particularly reviewer 3): the study is rather descriptive, limited in scope, and lacks mechanistic understanding of BAP1 functions: for example, see reviewer 1 comment "it would be interesting to further investigate the significance of some key interactions"; reviewer 3 comment "The present manuscript contained very little information beyond description of BAP1 interactomes and subsequent validation of BAP1-COPI interaction. In the very least, I would recommend for the authors to explore contextual significances and/or regulations of the novel BAP1-COP1 interaction."

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Referee #1

Evidence, reproducibility and clarity

Very interesting study on BAP1 tumor suppressor. The work needs further characterization of the interacting partners identified.

Significance

BAP1 is an important tumor suppressor mutated in several malignancies and the mechanism of action of this deubiquitinase are far from being completely understood.

This interesting work aimed at identifying novel cytoplasmic partners of BAP1 which can highly relevant to its tumor suppressor function. BAP1 is predominantly nuclear, but can also be found in the cytoplasm. New insights into the cytoplasmic functions of BAP1 are needed.

The manuscript is overall well written and the data are very solid.

The manuscript would need additional work before acceptance

Comments

1) The abstract can be improved to reflect the data of the manuscript.

2) The result section, manuscript could emphasize the results rather that the technical aspects

3) It would be interesting to further investigate the significance of some key interactions

4) The discussion is quite short and can put the findings in perspective

5) It would be interesting to test some cancer-associated mutations

6) Figure 4 can be improved

7) Yu et al MCB 2010 is one of the key papers on BAP1 purification and can be cited

8) The authors can discuss potential substrates of BAP1 and mechanism of deubiquitination

Referee Cross-commenting

I agree with the comments of Reviewer #2

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Reply to the reviewers

Reviewer #1

Summary:

In this work the authors present a simple mathematical model for the distribution of morphogen molecules that travel via cytonemes through a 1- dimensional system. This model is used as a basis for a software package called Cytomorph that takes as an input a set of experimentally measured distributions of cytoneme dynamics as well as experimenter determined parameters such as contact probability and method of cytoneme growth and retraction. The Cytomorph package then outputs spatial and temporal information on the distribution of morphogen as well as cytonemes and their contacts with cells and other cytonemes, all obtained over thousands of simulation runs. A number of in silico experiments are then performed to show that these outputs agree with experimentally measured morphogen distributions of Hedgehog in the imaginal wing disc and abdominal histoblast nest. Further in silico experimentation is done to study how this distribution is affected by a wide array of parameters such as producer row number, cytoneme connection method, and connection probability function. Comparisons to the traditional diffusion based model are also made. The authors find a suite of results based on these experiments and accordingly present the Cytomorph software package as a useful and adaptable tool for the community.

Major comments:

While the various in silico experiments present an expansive and exhaustive study of the different ways in which Cytomorph can be used to examine a cytoneme based distribution system, the machinery behind the software is left notably underdescribed. The authors do not sufficiently make clear what exactly happens within each iteration of the simulations run by Cytomorph, leaving the results irreproducible without the reader going into and deciphering the software code itself.

In order to improve the description of the mathematical and computational steps behind the software, we have created a visual organigram (new Supplementary Figure S.1) with a detailed depiction of the steps. We have also included a short description in the main text and an extended explanation in the Supplementary Material section.

Some of the specific details left undiscussed are how it is determined when and where a cytoneme will spawn or what its maximum length will be, the dynamics of morphogen transport within the cytonemes, the effects of one cytoneme making multiple connections on how much morphogen is delivered through each connection, and where exactly stochasticity is introduced so as to allow for variations between simulation runs; amongst others.

In the new description of the software steps, we have tried to address the Referee’s comments about the dynamics and stochasticity in more detail. In order to help the understanding of the variables, we have also tried to improve their description in the main text.

Additionally, when the authors investigate the diffusion model their stated boundary conditions do not match those presented at the end of the Materials and Methods section. The initial condition u(x,0)=0 and boundary condition du(L,t)/dt=0 represent a perfectly absorbing molecule sink at the x=L end of the system, not the reflecting boundary condition du(L,t)/dx=0 that would correspond to a zero morphogen flux.

We thank the Referee for noticing this annotation mistake since the equation is really dx instead of dt. We have corrected this error and included in the Supplementary Materials the exact lines of code used in Matlab pdepe to certify the conditions used in the resolution of the diffusion equation (new Supplementary Figure S.10).

Finally, while the authors spend a great deal of effort analyzing signal variability between simulation runs, there is no effort made to account for the inherently stochastic nature of molecular production, movement, and degradation. Particularly if molecule numbers are small, fluctuations in these processes could greatly increase signal variability. The authors should either address why these fluctuations are negligible or include them in the modelling.

This work is mainly focused on the transport of the morphogen; other terms as degradation were introduced directly using published experimental data. Regarding the main concern about the negligibility of the fluctuations for cytoneme transport, we agree with the Referee on the importance of this point. Therefore, we have included a detailed description of the variability and fluctuations in a new section of the Supplementary Material. To help its understanding, we have also included a new Supplementary Figure (Supplementary Figure S.11).

The largest fluctuations were found at the tail of the morphogen gradient (last rows of receiving cells). Since this corresponds to the region where the amount of morphogen is low, the absolute fluctuations do not change the activation of the low-threshold target. We then conclude that those fluctuations are biologically negligible for our study.

Minor comments:

The authors should double check all equation and figure references as I noted several instances in which it appeared that the wrong equation or figure was being referred back to. Similarly, the authors should double check the equations themselves, particularly those in the supplemental material.

We thank the Referee for noticing these mistakes. We have reviewed those references in order to fix the wrongly linked ones.

Eqs. SM1.1 and SM1.2 have a plethora of parameters with a wide array of different sub- and superscripts that are left unexplained and possibly incorrectly labelled in some cases,

Equations SM1.1 and SM1.2 described a general form of Triangular and Trapezoidal dynamics and the different sub- and superscripts come from the published experimental data. Nevertheless, in order to make them more intuitive we have simplified the expressions and included a more detailed description of those parameters and their scripts in the revised version.

while the second line of Eq. SM2.2 is nonsensical unless r_I*p=0 and p_i<=1.

We thank the Referee for noticing the uncertainty in this equation, since it was written in an iterative syntax as it is coded in the software. Therefore, in the code we did not have this nonsensical range of data, but we agree that it should be specified with a mathematical syntax as the rest of the equations in the manuscript. Therefore, we redefined the notation and specified better the numerical domains of those variables.

Additionally, the notation used in Figs. 5 and 6 as well as the bottom part of Fig. 7 is confusing. The caption should more explicitly state what the various expressions in the second row of each column represent.

The second row represents the statistical analysis between cases coded in a color matrix, as it is described in the footnote. We thank the Referee for this recommendation because this is not the usual representation. Therefore, we have changed the previous explanation to one hopefully clearer and intuitive; we have also included a specific label in the figures.

In Fig. 5A specifically it is unclear what exactly the variable phi represents.

Phi is a widely used annotation in biology to define cell size diameter and cell position. We didn´t realize it could be unclear. For a better understanding within a multidisciplinary field we have changed this symbol.

Does it have anything to do with the phi that is used as a position variable for the cells, and if it is a ratio of cytoneme length to cell diameter then why does it have units of microns?

We agree that this phi notation is confusing. It has been used to indicate distance position as well as cell diameter. Although these variables are biologically related, in the new version of the manuscript we have changed the notation to separate both concepts and avoid misunderstandings.

Significance:

As the Cytomorph model and software can be applied to a wide variety of systems involving morphogen transport via cytonemes, it provides a technical advance in our ability to analyze and discuss the results of measurements on cytonemes in a more homogenous way. This work and the resulting software is particularly applicable to and build off of studies done by other groups that study the dynamics of cytonemes such as the Kornberg lab (works from which are cited by the authors) and the Scholpp lab (such as Stanganello E, Scholpp

S. Role of cytonemes in Wnt transport. J Cell Sci. 2016; 129(4):665-672), and as such it is experimental labs such as these that will be the most interested in this manuscript and its findings.

My field of expertise lies primarily in stochastic modeling and linear response theory. As such, I feel I do not have sufficient expertise to evaluate the experimental methods outlined in this manuscript and determine their level of scientific rigor.

Reviewer #2

The manuscript "Improving the understanding of cytoneme-mediated morphogen gradients by in silico modelling" addresses the role of in silico modelling in understanding pattern formation via cytonemes: filopodia that transport signalling molecules to and from cells. Investigating the role of cytonemes and, in particular, their dynamics, during development is an important and emerging field in developmental biology, and there is great potential for mathematical modelling to aid in understanding these processes.

The present manuscript attempts to derive a general set of equations describing pattern formation in the context of cytonemes, akin to that of the classic Turing model of morphogenesis. The authors replace the standard diffusion term in the PDE with a non-local term, intended to represent transport via cytonemes. This model is then posed over a one-dimensional domain with a source at one end and no flux boundary conditions at the other and is shown to be able to generate a morphogen gradient profile that could pre-pattern a biological tissue. The model is tested against a key experimental system, namely, Hh signalling in the Drosophila wing imaginal disc and is shown to reproduce some experimental results. Finally, the authors have developed a Matlab-based software package that they claim will be applicable to a wide range of systems. This GUI-based software allows users to input experimentally measured averages of cytoneme properties and explore the effect of these properties on tissue patterning.

My primary concern is that the paper presents itself as a mathematical model of cytoneme formation in general. The authors themselves state in their introduction that the mechanisms for cytoneme generation and maintenance are presently unknown. In fact, it is not even known if they are consistent across biological systems (and in fact, are probably not in general). As such, any present instantiation that connects cytoneme dynamics to tissue patterning can only hope to be specific to a particular system (in this case, the Drosophila wing imaginal disc.

As mentioned in the introduction, the connection of cytonemes with patterning has been described in several works. We had included a list of publications describing the implication of cytoneme-mediated signaling for several morphogens (FGF, Egf, Hh, Dpp, Wnt or Notch) and in many vertebrate and invertebrate systems (Drosophila, chicken, Xenopus, Zebra fish, mouse and human tissue culture cells).

Whilst one may use general models (like the heat equation) to study pattern formation since it requires only specification of parameters, the model here requires specification of families of functions, that are likely to differ from context to context and so the model is not general.

Our model inputs are parameters determined experimentally rather than families of functions. This misunderstanding might derive from the use of triangular and trapezoidal dynamics, which are equations included in the software code but not input functions. To avoid this confusion, we have specified the input data in tables S.1 and S.2 and clarified in the main text that the triangular or trapezoidal family of functions are just the names for the basic dynamics of cytonemes (triangular for elongation and retraction, and trapezoidal when there is a stationary phase in between).

Ultimately, the model is a statistical modelling framework masquerading as a mechanistic one.

In this work, we have not specified the mathematical area to which the model belongs. Furthermore, we always explicitly described the different variables and functions modeled. Therefore, we do not understand what the supposed masquerade is.

As further evidence of the lack of generality of the model, the studied domain is only one dimensional and has signalling sources at one end. This scenario is perfectly adequate for theoretical explorations of pattern-forming systems but is highly unlikely to capture the geometrical intricacies of real-world systems (and I note that even in the diffusive case, boundary conditions are critical for understanding what patterns ultimately arise for a given system).

We agree with the Referee that there are cases in biological systems in which it is required to work in 2D or even 3D to have a full comprehension of the process. Nevertheless, those are mainly related to biological patterns rather than to biological signaling gradients, which usually are studied (experimental and theoretically) in 1D. Therefore, we have limited our model to this case and compared our in silico results with the published experimental data. In any case, we have emphasized in the text that our model is limited to signaling gradients with the source at one end, which is the case of the best studied morphogens: Hh (Sonic-hh), Dpp (BMP) or Wg (Wnt).

Actually, as prove of the generality of the model, we have predicted different properties of Dpp and Wg gradients using our model. We then validated the simulated results using the experimental data obtained from independent publications.

To simulate their model, the authors need to specify triangular and trapezoidal functions, which are unlikely to be generalisable to all contexts. As such, the model is not general and, in particular, there is no way to change the software to make it so.

Cytonemes are filopodial structures based on actin filaments that polymerize and depolymerize to elongate and retract. This is a general process for all filopodial structures and it is why cytonemes were classified in a previous published work as a triangular behavior or, if this dynamic has a stationary phase, as a trapezoidal behavior (Gonzalez-Méndez et al., 2017). Therefore, these functions are just a categorization introduced to better describe the intrinsic dynamics of cytonemes, that could be applied to most of the experimental cases. To attend this Referee’s concern, we have included in the introduction a more detailed description of these behaviors, as well as the references of publications describing the dynamic behaviors of cytonemes for different morphogens and in different organisms.

Trying to make a generalization for all cases, we included in the model those situations in which the cytonemes were static rather than dynamic (detailed simulations comparing dynamic and static cases can be found in the old Supplementary Figure S.5 A (now S.7 A)).

We have concluded that the model can be considered generalizable since it includes the simplest and most general cases in terms of cytoneme dynamics.

Whilst the development of a GUI for this scenario is a nice contribution, I feel that the lack of generalisability will, at best, mean that the software enjoys little use, and at worst, may lead researchers unfamiliar with the modelling context to misuse it in error.

Once we knew the model could be generalized, we were concerned about the misuse of the mathematical model, and that was the reason why we decided to develop a GUI as simple as possible.

Furthermore, in the online repository there is, together with the open software, an user guide of Cytomorph with a full description of parameters, variables and outputs and how to use them properly.

In my opinion, this work would be better suited as a presentation of specific mathematical modelling of tissue patterning in the Drosophila wing imaginal disc. In this case, many of the above concerns would be addressed.

We have rewritten part of the text to indicate the limits of the model and make clear that it has been tested experimentally for the Hh pathway and in two different developing systems: wing imaginal discs and abdominal histoblast nests.

As evidence of a more general use of Cytomorph, we have added in the revised version of the manuscript a new section focused on data prediction for the gradients of Dpp and Wg. We have also included supplementary figures that validate the predictions of our model using published experimental data.

That said, there are still a number of issues with the presentation of the model and results. I shall detail these in the bullet point list below:

1. The domain for Eq. 1 needs to be made explicit. Later, it appears that the domain is a closed one-dimensional interval, but the use of arrows here implies that x is a vector and hence x ∈_ D ⊂ _Rn with n > 1.

We initially described the general equation for morphogens as x ∈ ℝ𝑛 and later we limited it to 1D. This is why at the beginning x, as a vector, contained an arrow, although later it was a scalar variable. Since we were interested in 1D in this work, to avoid this kind of misunderstanding we have rewritten from the beginning the equations as 1D and clearly specified the x domain used: the set of natural numbers x ∈ ℕ0.

1. It is unclear over what the sum in Eq. 2 is being taken.

The sum in Eq. 2 is over the number of producing cell rows. We have changed the notation to clarify this point.

1. The statement "we used the discrete cell position x = φ as spatial coordinate" is vague and does not help the reader understand the discretization._

The number of cell diameters is a widely used discrete unit for position in Developmental Biology. As we expect the readers of this publication to be multidisciplinary, we have changed the notation to avoid misunderstandings and clarify this discretization.

1. p is used both as a probability and as an index for producer cells. This is confusing._

We have changed the notation to avoid misunderstandings.

1. As previously stated, the choice of trapezoidal/triangular cytoneme dynamics is not general. More work needs to be done to showcase how the authors came to the conclusion that this is the best choice, and how the functions (and their associated parameters) describing them were selected.

The names triangular and trapezoidal stand for the published dynamics for elongation and the retraction of cytonemes and we already argued about its generality. As we specified in the manuscript, these types of behaviors have been experimentally observed and, therefore, we considered that the experimental observation was reason enough to include them in the model. If more details are required, the Material and Method section and the Supplementary Table S.3 show that the times measured for triangular and trapezoidal dynamics are statistically different and, consequently, both behaviors have to be considered.

As mentioned in the manuscript, the associated parameters represent the times and velocities for the elongation or retraction that have already been thoroughly analyzed and published (González-Méndez et al., 2017). The question of the Referee about how these functions affect the gradient is answered in the text and in Figure 7 F.

1. I can see how Type 1 and Type 2 cytonemes could be expanded naturally to a higher dimensional case, but it is not clear how Type 3 cytonemes could be, since the probability of any two cytonemes occupying the same space in higher dimensions is likely to be small (if they are imbued with independent dynamics).

We agree with the Referee on this point. It is something that shall be considered for future improvements of the model in higher dimensions. For instance, a complex scenario in 2D will be required of a cytoneme guiding model. Nevertheless, since the present study is limited to 1D, this concern is not applicable for the current model.

1. The statement: "the distance between cells must be smaller than, or equal to, the maximum length of the cytonemes" seems inconsistent with the equations below since λ(t) does not appear to be a maximum length.

The length of the cytonemes is controlled as a dynamic function described by λ(t). Our statement referred to the maximum length for each time step that is given by λ(t). We agree that the initial statement could lead to misunderstanding, so we have suppressed the word “maximum”.

1. I think the authors are confusing probabilities and rates in their discussion of the model. Eq. 1 is a density model and so calling events probabilities here is slightly misleading. As a more general statement, I am currently interpreting contact function C as one defined as a rate, rather than as a set of probabilistic terms. If the latter is true, then Eq. 1 is invalid since it mixes processes at different levels of description._

We thank the Referee for this comment. We have studied in depth this observation but we could not exactly find why the Referee considers that the model is working at different levels. Even though we could not find where in the text we called “probabilities” to the events of eq1, we rewrote the text to make clear what we consider either probability or rate. In addition, in the Supplementary Material section we clarify how the model works and at what levels of modeling we are working.

Significance

In general, the paper is well written, however, the focus of the findings should be on patterning within an epithelium such as the Drosophila wing imaginal disk.

The work will be interesting for the developmental biology community as well as for the upcoming biomathematical modelling community.

Expertise: Developmental biologist with experience in tissue patterning and morphogen gradients

Referees cross-commenting

I agree with Reviewer 3 that the importance of cytoneme-mediated signalling has been described in several systems - invertebrates and vertebrates. However, I think the focus of this work in particular should be on cytoneme signalling in the wing imaginal disc. IMO, this would not limit the conclusion but rather focus it and make it then applicable to epithelial tissues in general. I agree with the other point.

Reviewer #3

There is much to like in this thoughtful and worthwhile study that develops mathematics to describe how cytonemes might generate experimentally observed Hh gradients. Two suggestions:

1. I am not equipped to evaluate the mathematics and as a non-expert would find it helpful if the authors explicitly stated at the outset what assumptions they took, the specific contexts they sought to model, and the parameters that they explored.

We agree with the Referee on the excessively mathematical focus of our interpretation of the results in the old version of the manuscript. We have rewritten part of the text to clarify the biological implications of the variables and simulations explored.

Am I correct that they assume that the Hh gradient correlates with a cytoneme gradient, that all cytoneme contacts have the same duration and exchange equivalent amounts of Hh, and that the variables that were characterized are cytoneme length distributions, cytoneme extension rate, contact duration, and cytoneme density?

Since the mechanism of morphogen exchange is not fully identified, we assumed the simplest case in which all the contacts have the same duration and exchange the same amount of morphogen. Using this approach, we were able to reproduce the gradient and concluded that it is not strictly necessary to propose a more complex mechanism to establish a graded distribution of morphogens. We therefore worked under this assumption.

The variables characterized were the ones pointed out by the Referee, mainly cytoneme features, as the cytoneme length distributions or the different parameters of the temporal dynamics. We tried to define better these variables in the new version of the manuscript.

1. One of the unusual features of the Hh gradient in the wing disc is that the size of the posterior compartment field of Hh-producing cells is large relative to the size and extent of the Hh gradient in the adjacent anterior compartment. Wing discs with large hh mutant clones, wing discs with large smo mutant clones, and wing discs with ttv mutant clones that block Hh uptake provide evidence that the Hh gradient is constituted with Hh that is produced by many cells, some that are far from the compartment border as well as some that are close. Has this been factored into the author's model?

Indeed. Being aware of the importance of the size of the signal source, we simulated how changing the size of the posterior compartment affects the gradient (altering the number of producing cell rows involved, figure 5B). In the old version of the manuscript we had focused on the theoretical approach, so we thank the reviewer for noticing that we should introduce a more biological point of view. Therefore, we included in the revised version of the manuscript a biological interpretation of how our simulations can help to understand the question posed by the reviewer.

Does the fact that the relative size of the posterior compartments and Hh gradients in the histoblasts is not as extreme as it is in the wing disc influence their model?

Following the Referee’s question, we decided to simulate the influence of the relative size of the posterior compartment in the abdominal histoblast nests. We found that in both wing discs and histoblasts, the size of the posterior compartment affects the gradient but in a different scale factor. We have included these data in the revised version of the manuscript (new supplementary figure S.5).

Interestingly, this feature of the Hh gradient in the wing disc is not shared with other gradients in the wing disc such as the Wg, Dpp, and Bnl gradients. I would be interested to know if the author's model can be queried to suggest what properties might contribute to this difference?

In order to answer the reviewer question, we have used our model to tentatively simulate Wg and Dpp gradients. Our preliminary results suggest that considering only cell position and cytoneme length, the Wg and Dpp gradient lengths can be predicted in wing imaginal disc. Nevertheless, each morphogen has its own particularities and further studies are required for a precise simulation of these gradients. We included these results in a new section of the manuscript and in the new Supplementary Figure S.9.

Significance

This is an important contribution to gaining a basic understanding of the role of various properties of dynamic cytonemes to gradient formation.

Referees cross-commenting

I discount the apparently strongly held opinion of Reviewer #2 that "it is not even known if they [cytonemes] are consistent across biological systems (and in fact, are probably not in general)". I do not know where this comes from and do not think that such opinions are appropriate for anonymous reviews.

Cytoneme-mediated signaling has in fact been observed and characterized in many diverse biological systems. I submit that in contrast, mechanisms of dispersion based on diffusion are inferred and lack direct experimental evidence. I do agree that it is fair to ask the authors to carefully describe their work in the context of epithelial signaling, but it is not correct to ask them to limit their conclusions to the wing disc as the authors analyze both wing disc and histoblast signaling. They clearly state that their work is limited to 1D and so we understand that it is inadequate to model 3D morphologies. I do not criticize them for this.

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Referee #3

Evidence, reproducibility and clarity

There is much to like in this thoughtful and worthwhile study that develops mathematics to describe how cytonemes might generate experimentally observed Hh gradients. Two suggestions:

1. I am not equipped to evaluate the mathematics and as a non-expert would find it helpful if the authors explicitly stated at the outset what assumptions they took, the specific contexts they sought to model, and the parameters that they explored. Am I correct that they assume that the Hh gradient correlates with a cytoneme gradient, that all cytoneme contacts have the same duration and exchange equivalent amounts of Hh, and that the variables that were characterized are cytoneme length distributions, cytoneme extension rate, contact duration, and cytoneme density?
2. One of the unusual features of the Hh gradient in the wing disc is that the size of the posterior compartment field of Hh-producing cells is large relative to the size and extent of the Hh gradient in the adjacent anterior compartment. Wing discs with large hh mutant clones, wing discs with large smo mutant clones, and wing discs with ttv mutant clones that block Hh uptake provide evidence that the Hh gradient is constituted with Hh that is produced by many cells, some that are far from the compartment border as well as some that are close. Has this been factored into the author's model? Does the fact that the relative size of the posterior compartments and Hh gradients in the histoblasts is not as extreme as it is in the wing disc influence their model? Interestingly, this feature of the Hh gradient in the wing disc is not shared with other gradients in the wing disc such as the Wg, Dpp, and Bnl gradients. I would be interested to know if the author's model can be queried to suggest what properties might contribute to this difference?

Significance

This is an important contribution to gaining a basic understanding of the role of various properties of dynamic cytonemes to gradient formation.

Referees cross-commenting

I discount the apparently strongly held opinion of Reviewer #2 that "it is not even known if they [cytonemes] are consistent across biological systems (and in fact, are probably not in general)". I do not know where this comes from and do not think that such opinions are appropriate for anonymous reviews.

Cytoneme-mediated signaling has in fact been observed and characterized in many diverse biological systems. I submit that in contrast, mechanisms of dispersion based on diffusion are inferred and lack direct experimental evidence. I do agree that it is fair to ask the authors to carefully describe their work in the context of epithelial signaling, but it is not correct to ask them to limit their conclusions to the wing disc as the authors analyze both wing disc and histoblast signaling. They clearly state that their work is limited to 1D and so we understand that it is inadequate to model 3D morphologies. I do not criticize them for this.

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Referee #2

Evidence, reproducibility and clarity

The manuscript "Improving the understanding of cytoneme-mediated morphogen gradients by in silico modelling" addresses the role of in silico modelling in understanding pattern formation via cytonemes: filopodia that transport signalling molecules to and from cells. Investigating the role of cytonemes and, in particular, their dynamics, during development is an important and emerging field in developmental biology, and there is great potential for mathematical modelling to aid in understanding these processes.

The present manuscript attempts to derive a general set of equations describing pattern formation in the context of cytonemes, akin to that of the classic Turing model of morphogenesis. The authors replace the standard diffusion term in the PDE with a non-local term, intended to represent transport via cytonemes. This model is then posed over a one-dimensional domain with a source at one end and no flux boundary conditions at the other and is shown to be able to generate a morphogen gradient profile that could pre-pattern a biological tissue. The model is tested against a key experimental system, namely, Hh signalling in the Drosophila wing imaginal disc and is shown to reproduce some experimental results. Finally, the authors have developed a Matlab-based software package that they claim will be applicable to a wide range of systems. This GUI-based software allows users to input experimentally measured averages of cytoneme properties and explore the effect of these properties on tissue patterning.

My primary concern is that the paper presents itself as a mathematical model of cytoneme formation in general. The authors themselves state in their introduction that the mechanisms for cytoneme generation and maintenance are presently unknown. In fact, it is not even known if they are consistent across biological systems (and in fact, are probably not in general). As such, any present instantiation that connects cytoneme dynamics to tissue patterning can only hope to be specific to a particular system (in this case, the Drosophila wing imaginal disc. Whilst one may use general models (like the heat equation) to study pattern formation since it requires only specification of parameters, the model here requires specification of families of functions, that are likely to differ from context to context and so the model is not general. Ultimately, the model is a statistical modelling framework masquerading as a mechanistic one.

As further evidence of the lack of generality of the model, the studied domain is only one dimensional and has signalling sources at one end. This scenario is perfectly adequate for theoretical explorations of pattern-forming systems but is highly unlikely to capture the geometrical intricacies of real-world systems (and I note that even in the diffusive case, boundary conditions are critical for understanding what patterns ultimately arise for a given system). To simulate their model, the authors need to specify triangular and trapezoidal functions, which are unlikely to be generalisable to all contexts. As such, the model is not general and, in particular, there is no way to change the software to make it so. Whilst the development of a GUI for this scenario is a nice contribution, I feel that the lack of generalisability will, at best, mean that the software enjoys little use, and at worst, may lead researchers unfamiliar with the modelling context to misuse it in error.

In my opinion, this work would be better suited as a presentation of specific mathematical modelling of tissue patterning in the Drosophila wing imaginal disc. In this case, many of the above concerns would be addressed. That said, there are still a number of issues with the presentation of the model and results. I shall detail these in the bullet point list below:

1. The domain for Eq. 1 needs to be made explicit. Later, it appears that the domain is a closed one-dimensional interval, but the use of arrows here implies that x is a vector and hence x ∈ D ⊂ Rn with n > 1.
2. It is unclear over what the sum in Eq. 2 is being taken.
3. The statement "we used the discrete cell position x = φ as spatial coordinate" is vague and does not help the reader understand the discretization.
4. p is used both as a probability and as an index for producer cells. This is confusing.
5. As previously stated, the choice of trapezoidal/triangular cytoneme dynamics is not general. More work needs to be done to showcase how the authors came to the conclusion that this is the best choice, and how the functions (and their associated parameters) describing them were selected.
6. I can see how Type 1 and Type 2 cytonemes could be expanded naturally to a higher dimensional case, but it is not clear how Type 3 cytonemes could be, since the probability of any two cytonemes occupying the same space in higher dimensions is likely to be small (if they are imbued with independent dynamics).
7. The statement: "the distance between cells must be smaller than, or equal to, the maximum length of the cytonemes" seems inconsistent with the equations below since λ(t) does not appear to be a maximum length.
8. I think the authors are confusing probabilities and rates in their discussion of the model. Eq. 1 is a density model and so calling events probabilities here is slightly misleading. As a more general statement, I am currently interpreting contact function C as one defined as a rate, rather than as a set of probabilistic terms. If the latter is true, then Eq. 1 is invalid since it mixes processes at different levels of description.

Significance

In general, the paper is well written, however, the focus of the findings should be on patterning within an epithelium such as the Drosophila wing imaginal disk.

The work will be interesting for the developmental biology community as well as for the upcoming biomathematical modelling community.

Expertise: Developmental biologist with experience in tissue patterning and morphogen gradients

Referees cross-commenting

I agree with Reviewer 3 that the importance of cytoneme-mediated signalling has been described in several systems - invertebrates and vertebrates. However, I think the focus of this work in particular should be on cytoneme signalling in the wing imaginal disc. IMO, this would not limit the conclusion but rather focus it and make it then applicable to epithelial tissues in general. I agree with the other point.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this work the authors present a simple mathematical model for the distribution of morphogen molecules that travel via cytonemes through a 1-dimensional system. This model is used as a basis for a software package called Cytomorph that takes as an input a set of experimentally measured distributions of cytoneme dynamics as well as experimenter determined parameters such as contact probability and method of cytoneme growth and retraction. The Cytomorph package then outputs spatial and temporal information on the distribution of morphogen as well as cytonemes and their contacts with cells and other cytonemes, all obtained over thousands of simulation runs. A number of in silico experiments are then performed to show that these outputs agree with experimentally measured morphogen distributions of Hedgehog in the imaginal wing disc and abdominal histoblast nest. Further in silico experimentation is done to study how this distribution is affected by a wide array of parameters such as producer row number, cytoneme connection method, and connection probability function. Comparisons to the traditional diffusion based model are also made. The authors find a suite of results based on these experiments and accordingly present the Cytomorph software package as a useful and adaptable tool for the community.

Major comments:

While the various in silico experiments present an expansive and exhaustive study of the different ways in which Cytomorph can be used to examine a cytoneme based distribution system, the machinery behind the software is left notably underdescribed. The authors do not sufficiently make clear what exactly happens within each iteration of the simulations run by Cytomorph, leaving the results irreproducible without the reader going into and deciphering the software code itself. Some of the specific details left undiscussed are how it is determined when and where a cytoneme will spawn or what its maximum length will be, the dynamics of morphogen transport within the cytonemes, the effects of one cytoneme making multiple connections on how much morphogen is delivered through each connection, and where exactly stochasticity is introduced so as to allow for variations between simulation runs; amongst others. Additionally, when the authors investigate the diffusion model their stated boundary conditions do not match those presented at the end of the Materials and Methods section. The initial condition u(x,0)=0 and boundary condition du(L,t)/dt=0 represent a perfectly absorbing molecule sink at the x=L end of the system, not the reflecting boundary condition du(L,t)/dx=0 that would correspond to a zero morphogen flux. Finally, while the authors spend a great deal of effort analyzing signal variability between simulation runs, there is no effort made to account for the inherently stochastic nature of molecular production, movement, and degradation. Particularly if molecule numbers are small, fluctuations in these processes could greatly increase signal variability. The authors should either address why these fluctuations are negligible or include them in the modelling.

Minor comments:

The authors should double check all equation and figure references as I noted several instances in which it appeared that the wrong equation or figure was being referred back to. Similarly, the authors should double check the equations themselves, particularly those in the supplemental material. Eqs. SM1.1 and SM1.2 have a plethora of parameters with a wide array of different sub- and superscripts that are left unexplained and possibly incorrectly labelled in some cases, while the second line of Eq. SM2.2 is nonsensical unless r_I*p=0 and p_i<=1. Additionally, the notation used in Figs. 5 and 6 as well as the bottom part of Fig. 7 is confusing. The caption should more explicitly state what the various expressions in the second row of each column represent. In Fig. 5A specifically it is unclear what exactly the variable phi represents. Does it have anything to do with the phi that is used as a position variable for the cells, and if it is a ratio of cytoneme length to cell diameter then why does it have units of microns?

Significance

As the Cytomorph model and software can be applied to a wide variety of systems involving morphogen transport via cytonemes, it provides a technical advance in our ability to analyze and discuss the results of measurements on cytonemes in a more homogenous way. This work and the resulting software is particularly applicable to and build off of studies done by other groups that study the dynamics of cytonemes such as the Kornberg lab (works from which are cited by the authors) and the Scholpp lab (such as Stanganello E, Scholpp S. Role of cytonemes in Wnt transport. J Cell Sci. 2016; 129(4):665-672), and as such it is experimental labs such as these that will be the most interested in this manuscript and its findings.

My field of expertise lies primarily in stochastic modeling and linear response theory. As such, I feel I do not have sufficient expertise to evaluate the experimental methods outlined in this manuscript and determine their level of scientific rigor.

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Reply to the reviewers

Response to Reviewers "Cell-cell communication through FGF4 generates and maintains robust proportions of differentiated cell types in embryonic stem cells"

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In this manuscript Raina et al. use an in vitro model of PE specification based on the transient overexpression of GATA4 in ESCs to show that the acquisition of primitive endoderm (PE) identity is governed at the population levels by cell-cell interactions mediated by FGF signaling. The authors further argue that the specification of a defined proportion of "PE" and "Epiblast" cells in a differentiating population of ESC is an emergent property of a system where paracrine signaling shifts the balance between two alternative stable states. Overall, the work does not reach radically new conclusions: broadly similar models are outlined in several other publications, including from the authors. Yet this study makes use of elegant genetic models and is particularly well executed. In addition, it includes a very accurate characterisation of the spatial range of FGF signaling activity that is original and adds on the existing knowledge. Moreover, the authors show novel evidence suggesting that GATA factors inhibits Fgf4 transcription and the activity of the FGF signaling pathway in ESCs.

We thank the Reviewer for commending the execution of the experiments, and for highlighting the novel insights that they bring. The Reviewer acknowledges that the specification of a defined proportion of PrE-like and Epiblast-like cells in a differentiating population of ESCs is an emergent property which is mediated by paracrine FGF4 signaling. This has not been experimentally demonstrated before. In contrast to the Reviewer’s assertion, we therefore think that our work does reach a conclusion that is radically different from previous experimental studies, a view that is also shared by Reviewer #3 below. In a revised version of the manuscript we will further emphasize the conceptual differences between published models that focus on single cell dynamics, and our experimental and theoretical demonstration of qualitatively different dynamics that emerge at the population level as a consequence of cell fate coupling.

**Two major points deserve further clarification:**

In this manuscript the authors claim that the proportions of cells acquiring PE fate is, at least in the experimental setup adopted, largely independent from the levels of GATA4 induction, and therefore of the initial state of the gene regulatory network regulating this cell fate transition. However, the authors should discuss how the current findings relate to their previous results, showing that the duration/levels of Gata4 induction, in a similar experimental setting, play an important role in determining the final proportion of cells cell acquiring "PE" fate. Absolute expression levels may be crucial for this distinction, but the authors seem to exclude this possibility (see figure S3).

The different roles of GATA4-mCherry induction levels for determining the final proportion of cells acquiring a PrE-like fate reported in our previous (PMID: 26511924) and the current work is because of important differences in the experimental settings between the two studies. In PMID: 26511924, we assayed PrE-like differentiation in medium supplemented with serum and LIF, which provides exogenous signals that promote PrE-like differentiation. These conditions reveal the function of the cell-autonomous circuit, in which GATA4-mCherry levels do control the probability of PrE-like differentiation. In the current work, we likewise observe that cell type proportions depend on GATA4-mCherry induction levels when we supply exogenous FGF4 during the differentiation of wild type cells (Figures S2C and S3D, lower panel). Differentiation in the absence of exogenous factors in contrast reveals the behavior of the coupled system, in which cell type proportions are independent from GATA4-mCherry induction levels.

Furthermore, in the present manuscript, we use new inducible cell lines in which the majority of cells can be induced above the critical GATA4-mCherry threshold required for PrE-like differentiation, in contrast to our previous study where the distribution of GATA4-mCherry induction levels was straddling this threshold.

In a revised version of the manuscript, we will more explicitly emphasize these important differences in the experimental design between the two studies, and discuss how the specific conditions in the present study lead to new conclusions.

Most importantly, the authors incorporate in their model the notion that GATA6 inhibits FGF signaling. It would be interesting to understand how such inhibition is mechanistically mediated. For instance GATA6 has been shown to bind in proximity of the Fgfr2 gene (Wamaitha et al., Genes and Dev., 2015). Alternatively, the authors show a direct effect on Fgf4 expression. The short time window of the reported repressive transcriptional effects (8h, Fig 2 middle), might suggest a direct regulation. The authors should test this possibility, and discuss what alternative modes of regulation could be envisaged (for instance, indirect effects mediated by Nanog). This is a key result that deserves a more detailed mechanistic characterisation.

The regulation of FGF signaling by GATA factors has been pointed out as a central new result of our study by all three reviewers that we will be happy to further expand on in a revised manuscript. Regulation of Fgfr2 expression by GATA6 as suggested by the ChIP-seq data in Wamaitha et al., 2015 (PMID: 26109048) is one possible mechanistic explanation that we will of course discuss.

Most importantly, we will test possible direct effects of GATA factors on Fgf4 expression that are indicated by the short timescales of the transcriptional effects shown in Fig. 2, as noted by the Reviewer. We have already mined the ChIP-seq data from Wamaitha et al., 2015 (PMID: 26109048) and found a GATA6-binding peak approximately 10 kb upstream of the Fgf4 start codon in a region that is highly enriched for GATA6 consensus binding sites. To test the functional role of this binding region, we propose to delete it by CRISPR-mediated mutagenesis in the inducible lines, and to test its ability to regulate reporter gene expression in heterologous assays.

To address the question of alternative modes of regulation of Fgf signaling through NANOG, we have already performed in situ mRNA stainings for Fgf4 expression in cells grown for 40 h in N2B27 medium. While Nanog expression is much reduced under these conditions, Fgf4 mRNA continues to be expressed, indicating that positive regulation through NANOG is not essential for Fgf4 mRNA expression in ESCs. We will add this data to a revised manuscript, and discuss its implications for the regulation of Fgf4 transcription (see also our response to Reviewer #3 below). As a complementary approach to further test the role of indirect effects mediated through NANOG, we will dissect more closely the timing of Fgf4 downregulation reported in Fig. 2B relative to the upregulation of the inducible GATA4-mCherry protein and the downregulation of NANOG protein.

**Minor points:**

Fig S1: The authors should show quantifications of Nanog and GATA6 levels before the beginning of the differentiation protocol.

We will be happy to add this data in a revised version, as part of a more extensive analysis of GATA4-mCherry and GATA6 expression at early stages of the differentiation protocol. See also our response to the next point.

Line 106: The authors write "the initially large proportion of GATA6+; NANOG+ double positive cells". It appears that at 16h of differentiation ESCs have already partitioned between Gata6 or Nanog expressing cells. The authors should rephrase the sentence to reflect what seems to be an almost total absence of truly double positive cells. Possibly, an analysis conducted at earlier time points could clarify these dynamics.

The Reviewer rightly points out that at 16 h of differentiation, most cells are already associated with one of two clusters in the NANOG/GATA6 expression space. The misleading classification of a large number of cells as double positive at 16 h was caused by applying a single gating strategy to the entire experiment, even though the mean expression levels of NANOG and GATA6 in the two clusters change significantly over time. We will update our gating strategy and rephrase this section to more appropriately describe cell clustering and gene expression dynamics over the time course. We will also extend Figure S1 with analysis of GATA6 and NANOG expression levels at earlier time points of the differentiation protocol, to test whether this allows detecting a truly double positive population.

Line 124: The authors write "... concentration dependent downregulation of NANOG expression". The effects may rather depend on the time of doxycycline stimulation.

We agree with the Reviewer that in isolation, the data shown in Fig. 1 and Fig. S2 leave open the possibility that the stronger downregulation of NANOG at higher GATA4-mCherry expression levels is caused by the extended time of doxycycline stimulation rather than GATA4-mCherry concentration. However, in our opinion, this concern is already addressed by the experiments performed in the four clonal lines with independent integrations shown in Figure S3. Here, the time of doxycycline induction is held constant, and a similar relationship between GATA4-mCherry and NANOG expression levels is observed as in the experiments where we modulate induction time in a single clonal line (compare Fig. S2A to Fig. S3B). In a revised version of the manuscript we will describe more clearly how the experiments shown in Figure S3 control for time-dependent effects of doxycycline stimulation.

Line 192: The authors write "...and confined to cells with low GATA4-mCherry expression levels". It would be helpful to have an indication of the cell boundaries, possibly showing localisation of a membrane bound protein.

We agree that more firmly establishing a correlation between GATA4-mCherry expression levels and Fgf4 mRNA expression in single cells would greatly benefit from co-staining with a plasma membrane marker. However, the protocol for mRNA in situ hybridization involves incubation steps with ethanol and formamide and is thus incompatible with staining for commonly used membrane markers. There is one commercially available membrane stain (CellBrite by Biotium) that promises to survive the treatments necessary for in situ hybridization and that we will try to use in our stainings. Should this not be successful, we will resort to identifying a subset of the cytoplasm corresponding to each nucleus by dilating nuclear masks that we will segment based on the DNA stain.

It would be interesting for the authors to discuss how the spatial range of FGF activity measured in culture could affect PE specification in the embryo.

During lineage specification in the embryo, Epi and PrE cells are initially arranged in a salt-and-pepper pattern (PMID: 16678776; PMID: 18725515; PMID: 30514631). In Fig. 4 and Fig. S9 of our manuscript, we show experimentally and theoretically how similar patterns in ESC colonies arise from the short range of FGF activity. In a revised version of the manuscript, we will discuss how the spatial range of FGF activity measured in culture provides a possible mechanistic explanation for the spatial arrangement of cell types in the embryo.

Reviewer #1 (Significance (Required)):

See above.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

In their manuscript entitled "Cell-cell communication through FGF4 generates and maintains robust proportions of differentiated cell types in embryonic stem cells" Raina et al study the effect of Fgf-signalling based local cell-cell communication for the establishment of PrE-like and Epi-like cells. The authors use an elegant, albeit artificial, system to analyse the effect of Fgf signalling on establishing 'normal' lineage proportions after transient induction of Gata4 expression. The main conclusions of the manuscript are: i) Gata6 positive cells emerge through short range Fgf4 based cell-cell cummunication. ii) Fgf4 signalling can compensate a wide range of initial levels of Gata6 expression and produce properly portioned cell identities. The authors also state that this mechanism could operate in a range of developing tissues.

**Major points:**

1. Fgf4 KOS ESCs are deficient in initiating epiblast lineage differentiation (Kunath 2007). Therefore, the effect studied by the authors might be multifactorial and the general inability of Fgf4 deficient cells to enter differentiation might contribute to the observed differentiation defects and defects of cell fate proportioning. Specifically, it could be expected that Nanog regulation is affected in Fgf4 mutants, although, to my knowledge, the specific phenotype of Fgf4 depletion has not been evaluated in Gata4 induced cell programming towards PrE. What steps have the authors taken to exclude an impact of general cell fate change defects in Fgf4 KO ESCs.

While it is true that Fgf4 mutant cells have a general deficiency in initiating epiblast lineage differentiation, it was already shown in the original publication by Kunath et al. (PMID: 17660198) that general differentiation of Fgf4 mutant cells is restored to wild type levels by supplementing the culture medium with 5 ng/ml recombinant FGF4. This is a concentration that is well within the range of concentrations applied in our study. In initial experiments to characterize our Fgf4 mutant lines, we have measured NANOG expression to test the effectiveness of recombinant FGF4 to restore epiblast lineage differentiation. We found that FGF4 treatment of Fgf4 mutant cells in the absence of doxycycline induction leads to a downregulation of NANOG expression, to levels comparable to those seen in wild type cells grown in N2B27. These data indicate that treatment with recombinant FGF4 rescues defects of general cell fate change in Fgf4 KO ESCs. We will add these data to Figure S4 of a revised manuscript, and explicitly mention the function of recombinant FGF4 to rescue lineage differentiation potential more generally.

Increasing the time of Gata4 expression results in increasing levels of Gata4 levels (Fig 1C). This is shown at the overall mean fluorescence level. However, it is important to also quantify how many cells do actually show some increase in Gata4 levels. Fig1D suggests that the number of Gata4 expressing cells is quite similar between 4h and 8h induction, but this needs to be quantified. An explanation for the apparent dosage independence of Gata4 could then be simple threshold effects, such that there is no additional effect of increased Gata4 levels in WT cells without any further requirement of feedback regulation after a certain threshold level of Gata4 is reached. Have the authors considered such a simple model?

The current version of the manuscript already contains quantifications of GATA4-mCherry expression levels in single cells - see Fig. S2A for the experiments where we vary doxycycline induction time, and Fig. S3B for experiments with independent clonal lines. This analysis confirms the Reviewer’s visual impression of Fig. 1D - the number of GATA4-mCherry expressing cells is similar for different induction times and clonal lines, such that the increase in overall mean fluorescence levels is mainly due to an increase in GATA4-mCherry expression levels in single cells. This analysis therefore rules out the simple model based on threshold effects proposed by the Reviewer. In a revised version of the manuscript, we will more explicitly discuss the quantifications in Fig. S2A and Fig. S3B.

An important point is that in the current setup distinguishing between dosage effects and effects of extended presence of Gata4 cannot be distinguished. Wouldn't titrating the amount of doxycycline used for induction be a more direct way to achieve different initial levels of Gata4 expression?

This concern has also been raised by Reviewer #1, and is addressed in detail in our response to their comment above. Briefly, in our opinion this concern is addressed in the current manuscript by the experiments performed in the four clonal lines with independent integrations (Figure S3). Here, the duration of doxycycline induction and hence time of GATA4-mCherry exposure is held constant, such that the only difference between the conditions is GATA4-mCherry dosage. We will discuss this important function of Fig. S3 in a revised version of a manuscript.

Unfortunately titrating doxycycline does not allow titrating transgene induction levels in a meaningful way, as sub-saturating doses of doxycycline lead to an increased heterogeneity in transgene expression with many non-expressing cells, rather than to reduced expression levels across all cells. See PMID: 17048983 for a possible explanation of this observation.

Another point the authors should appropriately discuss and consider is that a lack of effect of different doses/durations of Gata4 expression could be due to the fact that by the time Gata6 is induced, the levels of Gata4 in cells previously treated for different periods of time are no longer detectably different. Such a regulation would equally result in indistinguishable cell fate proportioning. Can the authors exclude such a regulation? This is an important point at the heart of the authors conclusion.

The Reviewer seems to suggest that by separating the initiation of GATA6 expression from the GATA4-mCherry pulse in time, the decision to initiate PrE-like differentiation could be independent from GATA4-mCherry concentration, thus explaining the robust cell type proportions. The data shown in Figs. S2C, S3D and Fig. 3 A - C clearly exclude such a regulation: In conditions where we supply recombinant FGF4, the proportions of the different cell types scale with GATA4-mCherry expression levels, indicating that GATA4-mCherry dose does indeed affect Gata6 expression. In a revised version of the manuscript we will discuss and consider how these observations argue against a model where the decision to initiate PrE-like differentiation occurs independently from GATA4-mCherry levels.

The authors make some general statements on cell differentiation (e.g. l205). They also claim that the Fgf4-based mechanism of lineage proportioning could act in a range of tissues during development. However, the use of the term differentiation for the induction of PrE-identity (or Gata-factor expression to be exact, see comment below) after Gata4 overexpression is problematic. The system chosen by the authors is entirely artificial. ES cells normally do not differentiate into extraembryonic cell types. It needs to be made clear in the manuscript that they do not study a differentiation process that normally occurs in the embryo or in differentiating ESC cultures. The system the authors are using would, in my opinion, rather qualify as cell programming or transdifferentiation than as differentiation. I suggest presenting the system using clearer unambiguous language and to try to avoid any generalisations based on an artificial transgene-overexpression based system. The results have to be presented with this limitation in mind.

To address the Reviewer’s concerns regarding terminology, we will expand on the relationship of our system to normal ESC differentiation and lineage specification in the embryo, and discuss its possible limitations. We disagree however with the Reviewer’s assertion that using a transgene-based overexpression system precludes drawing any general conclusions. Rather, the system allows mimicking Epi- and PrE-like differentiation in a uniquely accessible context, and thereby to exploit the molecularly simple regulation of this cell fate decision for studying basic principles of cell differentiation. This view is supported by Reviewer #3 in the referees cross-commenting section below, who emphasizes the value of such models and notes that they are very common in developmental biology.

It is unclear how 'PrE-like' (as stated e.g. in the abstract) the cells really are after a short pulse of Gata4 expression. No proper characterisation has been performed but needs to be included, if the authors want to term these cells PrE-like.

A recent study by Amadei et al. (PMID: 33378662) supports the notion that a short pulse of GATA4 expression can trigger bona fide PrE-like differentiation. In this study, the authors induced a similar doxycycline-inducible GATA4 expression system for 6 hours, and observed subsequent differentiation into several PrE derivatives, including the anterior visceral endoderm. In a revised version, we will cite this study to support our claim that the GATA6-positive cells are indeed PrE-like. Additionally, we offer to perform immunostainings with an extended panel of known PrE marker proteins to substantiate the PrE-like character of the GATA6-expressing cells.

How is the statement in l112 that "The clear separation between the two populations suggests that the increase in the proportion of double negative cells at the expense of GATA6+; NANOG- PrE-like cells beyond 40 h is mostly fueled by the downregulation of NANOG expression in the GATA6-negative cell population, combined with a slower proliferation of the GATA6-positive population, rather than by the reversion of PrE-like into double negative cells." supported by the data?

We realize from the comments of all three reviewers that this section was confusing and potentially misleading in the original version of the manuscript. In a revision, we will reword this paragraph to better bring out the major conclusions from the GATA6 and NANOG expression patterns shown in Fig. S1A. These data show that the majority of cells belong to one of two discrete clusters from 16 h onwards. The clear separation of the two clusters furthermore indicates that cells rarely switch their gene expression patterns. Given these observations, the changes of cell type proportions reported in Figure S1B can be explained as a consequence of slower proliferation of cells in the GATA6-positive relative to the GATA6-negative cluster. In addition, NANOG expression in the GATA6-negative cluster declines over time, such that progressively more cells are classified as double negative.

Would the data and modelling performed by the authors be in line with a model in which the decision to express Gata6 is a stochastic choice (with a certain probability based on the levels of Gata4 induction) that is then stabilized and reinforced by Fgf signalling rather than Fgf signalling having an instructive role?

The simulations shown for the Fgf4 mutant case in Fig. 3 D - G, right column, are based on a model in which the decision to express Gata is a stochastic choice with a probability based on the initial levels of GATA expression, and reinforced by FGF signaling. Thus, our data from the Fgf4 mutant, but not the wild type, are perfectly in line with such a model.

We realize from the Reviewer’s comment that we have not made sufficiently clear the conceptual differences between the models for the mutant and the wild type case. We suspect that this lack of clarity stems from the fact that the two models rely on the same circuitry, except for the regulatory link between GATA and FGF. This link however makes a crucial difference: It transforms the simple single cell input-output model of the mutant case, which is common to many previous publications, into a population level model with cell-cell feedback which shows new emergent behavior. And only this population level model, but not the single cell model for the Fgf4 mutant, can recapitulate the experimental data observed in the wild type. In a revised version of the manuscript we will expand on these crucial differences when describing the model and data in Fig. 3.

The statement in line 187 "This indicates that GATA4-mCherry expression negatively regulates FGF4 signaling during cell type specification." is not supported by the data. The authors show only a correlation and actually correctly say so in line 195.

Prompted by the comments of both Reviewer #1 and #3, we will carry out experiments to mechanistically explore the regulation of Fgf4 expression by GATA factors (see our response to Reviewer #1 above for a detailed description). Depending on the outcome of these experiments we will reword this statement.

In Fig 2F statistical analysis between the re-seeded conditions is required for the conclusion that "the proportion of PrE-like cells systematically increased with cell density". Replating itself appears to quite drastically impact lineage distribution. Do the authors have an explanation for this?

The p-value in line 221 of the original manuscript refers to a test for a linear trend between the three conditions following a one-way ANOVA in GraphPad Prism. We apologize that this has not been made clear and will add this information in a revised version.

The observation that replating drastically impacts lineage distribution is perfectly in line with the overall conclusion from this section, namely that FGF signaling is enhanced by cell-cell contacts. Replating strongly reduces the number of direct cell-cell contacts by disrupting the colony structure of the culture. Thus it is expected that the proportion of the PrE-like cells - which require exposure to FGF ligands - is reduced under these conditions compared to the condition that has not been replated. We will discuss this explanation in a revision.

Fig 2G shows a key experiment illustrating the local effect of Fgf4 expression on first and second neighbours. The authors have investigated this effect using a Fgf-signalling reporter. Why did they not assay Gata6 expression in this assay instead of a Spry reporter? This would be the experiment to show that also Gata6 expressing cells (after transient Gata4 induction) are clustered around Fgf4 producing cells and be a strong piece of evidence to show that local Fgf4 signalling and cell-cell communication is indeed involved in cell identity proportioning. The cell lines required for this experiment (including Fgf4 mutant Gata4 inducible ESCs) appear to be available.

We decided to measure the FGF4 signaling range with a Spry4:H2B-Venus reporter because its response time is faster than that of GATA6 expression during differentiation. Furthermore, the Spry4:H2B-Venus reporter provides a quantitative readout for FGF4 signaling, in contrast to a binary read-out that would be expected for GATA6 expression. We will be happy to discuss these considerations in a revised manuscript.

We agree that measuring FGF4 signaling range with Fgf4 mutant Gata4-mCherry inducible cells as suggested by the Reviewer constitutes a complementary approach to further corroborate the role of local FGF4 signaling in cell differentiation. However, we would like to stress that our demonstration of local FGF4 signaling is already supported by two fully orthogonal quantitative experiments, one relying on cell replating and the other one relying on the signalling reporter. The concept of local signaling is further supported by our quantitative analysis of the spatial arrangement of cell types in Fig. 4. The additional experiment suggested by the Reviewer is therefore unlikely to substantially change the paper’s conclusions, as also pointed out by Reviewer #3 in the referees cross-commenting section. Therefore, we offer to perform this experiment for a revision, but would like to seek the editor’s opinion if this is deemed necessary to make the paper acceptable for publication.

The authors conclude from data in Fig 3A that proper cell type proportioning depends on initial Gata4 levels in Fgf4 mutants, in contrast to WT cells where the initial levels appear more irrelevant. Is 10ng/ml too high a dose? Would using a lower concentration (such as ~2ng/ml suggested by Fig 2D to give WT-like distribution) result in a complete rescue of cell lineage proportioning in this assay? Formally a control of adding additional Fgf4 to WT cells will also ne needed to control for a potential effect of exogenous Fgf4 addition.

In our initial characterization of the Fgf4 mutant cell lines, we have performed experiments where we examined cell type proportions upon culture in the presence of different doses of FGF4 following doxycycline induction times between 1 h and 8 h. These experiments confirm the suspicion of the Reviewer that cell type proportions similar to the wild type can be obtained with a lower dose of 2.5 ng/ml FGF4 after 8 h of induction. For shorter induction times followed by differentiation in the presence of 2.5 ng/ml FGF4 however, cell type proportions were strongly skewed towards Epiblast-like cells. These data thus further support the major conclusion from Fig. 3A quoted by the Reviewer: Proper cell type proportioning in Fgf4 mutants depends on GATA4 levels, and this behavior is independent from the FGF4 concentration applied. We offer to add this data to a revised manuscript.

The effects of adding FGF4 to wild type cells are shown in Fig. S2C and S3D in the current version of the manuscript. This control has been performed in all experiments shown in Fig. 3A - C, but we decided to omit it for clarity. We are happy to add this information back in as requested by the Reviewer.

Does the model in Fig 3E consider potentially varying doses of exogenous Fgf4? Can the model also predict what happens if Fgf4 is added to WT cells, as suggested above as control? In general, the value of this model is unclear. Figure 3E is near impossible to understand, no quantitative information is given.

The model in Fig. 3E can of course be simulated with different doses of exogenous FGF4. These simulations recapitulate the experimental results described under point 10 above: Cell type proportions for the Fgf4 mutant case are skewed towards NANOG-positive cells at lower FGF4 doses, and vary with initial conditions irrespective of FGF4 dose. We offer to show the results of these simulations in a revised manuscript alongside the experimental data discussed above.

It is also possible to incorporate into the model addition of exogenous FGF4 to the wild type. Simulations of this condition confirm the experimentally observed increase in PrE-like cells shown in Fig. S2C and S3D of the current manuscript.

To help the reader digest Fig. 3E, we will add separating lines similar to the gates of the flow cytometry data in panel A, and indicate the proportion of cells in the respective quadrants.

The Reviewer’s comment that the value of the model is unclear indicates to us that we have not explained in sufficient detail the conceptual differences between the behavior of the model of the wild type and the mutant case. As detailed in our response to Reviewer’s comment 6. above, we will rewrite the text to bring out more clearly the insight that the model brings.

Fig4A: What were WT and Fgf4 mutant cells treated differently in this assay (8h vs 4h, respectively)?

The spatial arrangement of cell types in Fgf4 mutant cells has been assayed in two conditions that give similar cell type proportions as seen in the wild type, as motivated in lines 366 - 370 of the current manuscript. We decided to show the condition with 4 h induction followed by differentiation in the presence of 10 ng/ml FGF4 in the main Figure 4 because it is most similar to the condition that gives wild-type like cell type proportions in the Fgf4 mutant shown in the immediately preceding main Figure 3, while the condition that uses 8 h induction followed by differentiation in the presence of 2.5 ng/ml FGF4 refers back to the main Figure 2. We show both primary data and the complete analysis for the latter condition in Figures S8D and S10. Fig. S10 provides a direct comparison between the two conditions and clearly demonstrates that they show similar dynamics. We do not think that exchanging the two datasets between main and supplementary Figures will add value to the manuscript.

Does the interpretation that at 24h there is a difference in Fig 4C survive statistical scrutiny? Only few datapoints are shown and any apparent differences seem due to outliers rather than a shift in cluster radii. How often were these experiments independently repeated? This information is missing. In Fig 4B, I cannot appreciate any difference between cell lines.

We will perform statistical testing to assess whether the spatial arrangement of cell types is significantly different between the time points, and mention the results in the text.

To evaluate the spatial arrangement of cell types, we have performed two independent experiments in the wild type, and analyzed two conditions for the mutant case. In each experiment, we have analyzed at least eight positions per condition and control. Spatial clustering of wild type cells at 40 h is also observed in earlier Figures in the manuscript (e.g. Fig. 1D, S2B, S3C).

The similarities between wild type and Fgf4 mutant cells shown in Fig. 4B are not surprising and fully in line with the data shown in panel C, which shows that differences between time points are much more pronounced compared to the differences between genotypes. However, we realize that the micrographs and analysis plots in Fig. 4A and B were perhaps not fully representative for the aggregate behavior shown in panel C. In a revision, we will therefore show data from more representative colonies in panels A and B.

**Minor points:**

a) More information on statistics should be given in the Figures and legends.

To address this concern we will perform statistical tests for differences in proportions of the main cell types in Figures 1D and 3C. In addition, we will perform statistical testing on Fig. 4C as detailed in point 13 above.

b) Percentages should be indicated in the quadrants of the FACS plots of Fig 3A and E.

This is a good suggestion, we will add this information. See also our response to point 11 above.

c) What is the underlying evidence for the statement: "The specification of Epi- and PrE-like cells in ESCs shows both molecular and functional parallels to the patterning of the ICM of the mouse preimplantation embryo."

In the current manuscript, this statement is further substantiated in the subsequent paragraph (lines 483 - 503). We realize that this order is potentially confusing and will change it. We will further modify this section as part of our response to major point 3. above.

d) Fig 5C is difficult to interpret without a comprehensive decoding of colour information.

To facilitate interpretation of this panel, we will add a legend to decode the colour information of the traces (purple: VNPhigh, cyan: VNPlow)

Reviewer #2 (Significance (Required)):

This manuscript provides novel insights into the role of Fgf-mediated cell-cell communication to establish proper ratios of cell identities in a PrE-induction system. The authors provide some interesting data and interpretation. Overall, the significance is slightly impaired by the highly artificial nature of the studied cell fate specification event.

This manuscript will be of interest to readers working on early embryonic cell fate decision as well as researchers working on modelling of cellular processes.

My expertise lies in the field of cell fate decision and pluripotency.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

It is well established that FGF signalling plays a role in the partitioning of the Primitive Endoderm and Epiblast fates during preimplantation mammalian development. Recent work has shown that this fate decisions is associated with a mechanism that is able to maintain the proportions of the two fates stable in the face of perturbations. Here, the authors address this mechanism and show that it is dependent on FGF signalling and associated with the fate decision. In the process they suggest and test a novel mechanism based on short range FGF signalling. A series of carefully designed and executed experiments, refine and provide evidence for the model. This is an original and important piece of work that will influence the field of pattern formation.

Overall the manuscript is well written but, at least from the perspective of this reviewer, there are places in which clarity can be improved.

Lines 104 and ff: the description of the dynamics of the different populations fater the GATA4 pulse, can be clarified. The reference to the double negative population emerging from the PrEnd population is not clear. It is stated that the proportion of these cells increased continuously and it said to be at the expense of the decrease of the PrEnd population whose variation is referred to as 'slightly declined". How can a slight decline fuel a steady increase in the double negative?

Also, what are these double negative? Could they be cells differentiating into embryonic lineages?

We realize from the comments of all three Reviewers on this paragraph that it was confusing and potentially misleading in the original manuscript. In a revised version we will rewrite this section to clarify our interpretation of the data in Fig. S1. First, the clear separation of the two clusters observed in NANOG-GATA6 expression space indicates that cells rarely switch between the two clusters. Then, a likely explanation for the slow decline in the fraction of GATA6-positive cells is a slower proliferation compared to the GATA6-negative cells. Third, the increase in the proportion of double negative cells is caused by a progressive downregulation of NANOG expression in the GATA6-negative cluster. These NANOG expression dynamics are consistent with NANOG expression dynamics in epiblast cells of the embryo, and could indeed indicate differentiation towards embryonic lineages. We will mention this possibility in a revised manuscript.

See also our response to Reviewer #1 and Reviewer #2, point 5..

In Figure 1 and its discussion, it would be good to see a representation of the stability of the final proportions relative to the different initial conditions, a variation on 1E.

This is a good suggestion. In a revised version, we plan to add a panel to Fig. 1 in which we plot the final proportions of the different lineages versus the GATA4-mCherry expression levels for the different induction times. This will illustrate more clearly that the final proportions of cell types are largely independent from the initial conditions.

Paragraph lines 182 and ff: the report that GATA4 expression is able to suppress FGF4 signalling, autonomously is, at least for this reviewer, a novel and important result and one that impinges on the understanding of the process. The authors should emphasize this.

We agree with the Reviewer that the direct regulation of Fgf4 expression through GATA factors is a new regulatory link suggested by our data that has not been described before and that is crucial for the functioning of the system. Prompted by a similar comment of Reviewer #1 above, we offer to further explore the mechanistic basis of this link through an analysis of published ChIPseq data, functional studies of a GATA binding site upstream of the Fgf4 start codon, or a more detailed temporal dissection of NANOG, GATA and Fgf4 expression dynamics following doxycycline induction (see our response to Reviewer #1 above for more details). These new experiments and analyses will allow us to emphasize this novel result, and thereby significantly strengthen our paper.

Paragraph lines 274 and ff (section on the involvement of FGF4 in the robustness of the process) needs some explanations. The derivation of the conclusion that 'recursive communication vis FGF4 underlies a population-level phenotype ...characterized by the differentiation of robust proportions of cell types..." from the experiments requires some unwrapping. It would be helpful if the authors could reason how the conclusion follows from the experiments.

We realize from this Reviewer’s comment and the comments of Reviewer #2 above that we have not explained well enough how the results shown in Fig. 3 A-C (lines 274 - 283) lead to our conclusion of emergent behavior, which are then further substantiated in the modelling in panels D - G. The central conclusion of this paragraph rests on the observation that cell type proportions are dependent on initial conditions in the Fgf4 mutant, but not in wild type cells. As we had supplied FGF4 externally to the Fgf4 mutant cells, the only difference between these two conditions is that FGF4 dose in wild type cells is regulated by the cell population, i.e. cells can communicate via FGF4, whereas mutant cells cannot. We will expand on this line of reasoning, and also explain in more detail the differences in the models for the mutant case and the wild type, which we believe will help to conceptualize the experimental results. See also our response to Reviewer #2, points 6. and 11..

Their model does not seem to include the commonly agreed regulatory interaction between Nanog and FGF4, at least not directly, and it would be helpful if a reasoning could be provided for this decision.

A discussion of the regulatory interaction between NANOG and Fgf4 has also been requested by Reviewer #1. In our response to their point above, we provide a reasoning why we have omitted it in the current manuscript. Briefly, our decision not to include a direct positive link between NANOG and Fgf4 expression rests on our observation that Fgf4 mRNA continues to be expressed 2 days after switching cells from 2i + LIF medium to N2B27, a time at which NANOG already starts to be downregulated as a consequence of differentiation along embryonic lineages. We will add this data to a revised manuscript. In addition, we propose above to dissect in more detail the temporal sequence of GATA4-mCherry, Fgf4 and NANOG expression upon doxycycline induction. This analysis will provide further information about the role of NANOG for Fgf4 mRNA expression in ESCs.

Reviewer #3 (Significance (Required)):

In this manuscript, Raina and colleagues use an Embryonic Stem (ES) cell based experimental system to address a central problem in developmental biology, namely the emergence of stable scaled populations of different cell fates. The experiments are elegant in design, carefully executed and the effort provides a solution to the problem: a novel mechanism based on short range FGF signalling that provides homeostatic control of relative cell populations. This is an important piece of work with sound conclusions that establishes a new paradigm in pattern formation whose implications are likely to lead to a reassessment of the role of FGF in different patterning paradigms. The experiments are quantitative and supported by a modelling effort based on a theoretical piece of work (Stanoev et al. 2021) which underpins the conclusion.

This manuscript will appeal to a wide audience including developmental and stem cell biologists as well as modellers.

My expertise cover the areas addressed in the manuscript.

**Referees cross-commenting**

It looks as if, with some nuances, we all agree on the value of the work. I do not have any issues with the comments of Reviewer 1, though I disagree that the model tested and improved here is similar to existing ones. While it is true that this work is related to a theory paper by some of the authors, the experimental test and resulting conclusions are very important. On the other hand, I am very surprised by the comments of Reviewer 2 who, after conceding the value and potential significance of the work, raises a list of queries, largely small details and opinions rather than points of substantial concerns, hinting at a need for the authors to perform extra work and analysis that will not change the conclusions of the manuscript. Some of this e.g. #9 would be a nice piece of additional evidence, but more an adornment than a necessary piece of additional evidence. The main problem of this reviewer is the lack of appreciation of what they define as 'highly artificial nature' of the study without providing any reason for why such experiments (very common in developmental biology) can lead to misleading conclusions. It seems to me that most, if not all, of their significant concerns can be dealt with in a rebuttal or by altering the text, either to discuss the issues raised, to clarify the points or qualify the conclusions.

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Referee #3

Evidence, reproducibility and clarity

It is well established that FGF signalling plays a role in the partitioning of the Primitive Endoderm and Epiblast fates during preimplantation mammalian development. Recent work has shown that this fate decisions is associated with a mechanism that is able to maintain the proportions of the two fates stable in the face of perturbations. Here, the authors address this mechanism and show that it is dependent on FGF signalling and associated with the fate decision. In the process they suggest and test a novel mechanism based on short range FGF signalling. A series of carefully designed and executed experiments, refine and provide evidence for the model. This is an original and important piece of work that will influence the field of pattern formation.

Overall the manuscript is well written but, at least from the perspective of this reviewer, there are places in which clarity can be improved.

Lines 104 and ff: the description of the dynamics of the different populations fater the GATA4 pulse, can be clarified. The reference to the double negative population emerging from the PrEnd population is not clear. It is stated that the proportion of these cells increased continuously and it said to be at the expense of the decrease of the PrEnd population whose variation is referred to as 'slightly declined". How can a slight decline fuel a steady increase in the double negative?

Also, what are these double negative? Could they be cells differentiating into embryonic lineages?

In Figure 1 and its discussion, it would be good to see a representation of the stability of the final proportions relative to the different initial conditions, a variation on 1E.

Paragraph lines 182 and ff: the report that GATA4 expression is able to suppress FGF4 signalling, autonomously is, at least for this reviewer, a novel and important result and one that impinges on the understanding of the process. The authors should emphasize this.

Paragraph lines 274 and ff (section on the involvement of FGF4 in the robustness of the process) needs some explanations. The derivation of the conclusion that 'recursive communication vis FGF4 underlies a population-level phenotype ...characterized by the differentiation of robust proportions of cell types..." from the experiments requires some unwrapping. It would be helpful if the authors could reason how the conclusion follows from the experiments.

Their model does not seem to include the commonly agreed regulatory interaction between Nanog and FGF4, at least not directly, and it would be helpful if a reasoning could be provided for this decision.

Significance

In this manuscript, Raina and colleagues use an Embryonic Stem (ES) cell based experimental system to address a central problem in developmental biology, namely the emergence of stable scaled populations of different cell fates. The experiments are elegant in design, carefully executed and the effort provides a solution to the problem: a novel mechanism based on short range FGF signalling that provides homeostatic control of relative cell populations. This is an important piece of work with sound conclusions that establishes a new paradigm in pattern formation whose implications are likely to lead to a reassessment of the role of FGF in different patterning paradigms. The experiments are quantitative and supported by a modelling effort based on a theoretical piece of work (Stanoev et al. 2021) which underpins the conclusion.

This manuscript will appeal to a wide audience including developmental and stem cell biologists as well as modellers.

My expertise cover the areas addressed in the manuscript.

Referees cross-commenting

It looks as if, with some nuances, we all agree on the value of the work. I do not have any issues with the comments of Reviewer 1, though I disagree that the model tested and improved here is similar to existing ones. While it is true that this work is related to a theory paper by some of the authors, the experimental test and resulting conclusions are very important. On the other hand, I am very surprised by the comments of Reviewer 2 who, after conceding the value and potential significance of the work, raises a list of queries, largely small details and opinions rather than points of substantial concerns, hinting at a need for the authors to perform extra work and analysis that will not change the conclusions of the manuscript. Some of this e.g. #9 would be a nice piece of additional evidence, but more an adornment than a necessary piece of additional evidence. The main problem of this reviewer is the lack of appreciation of what they define as 'highly artificial nature' of the study without providing any reason for why such experiments (very common in developmental biology) can lead to misleading conclusions. It seems to me that most, if not all, of their significant concerns can be dealt with in a rebuttal or by altering the text, either to discuss the issues raised, to clarify the points or qualify the conclusions.

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Referee #2

Evidence, reproducibility and clarity

In their manuscript entitled "Cell-cell communication through FGF4 generates and maintains robust proportions of differentiated cell types in embryonic stem cells" Raina et al study the effect of Fgf-signalling based local cell-cell communication for the establishment of PrE-like and Epi-like cells. The authors use an elegant, albeit artificial, system to analyse the effect of Fgf signalling on establishing 'normal' lineage proportions after transient induction of Gata4 expression. The main conclusions of the manuscript are: i) Gata6 positive cells emerge through short range Fgf4 based cell-cell cummunication. ii) Fgf4 signalling can compensate a wide range of initial levels of Gata6 expression and produce properly portioned cell identities. The authors also state that this mechanism could operate in a range of developing tissues.

Major points:

1. Fgf4 KOS ESCs are deficient in initiating epiblast lineage differentiation (Kunath 2007). Therefore, the effect studied by the authors might be multifactorial and the general inability of Fgf4 deficient cells to enter differentiation might contribute to the observed differentiation defects and defects of cell fate proportioning. Specifically, it could be expected that Nanog regulation is affected in Fgf4 mutants, although, to my knowledge, the specific phenotype of Fgf4 depletion has not been evaluated in Gata4 induced cell programming towards PrE. What steps have the authors taken to exclude an impact of general cell fate change defects in Fgf4 KO ESCs.
2. Increasing the time of Gata4 expression results in increasing levels of Gata4 levels (Fig 1C). This is shown at the overall mean fluorescence level. However, it is important to also quantify how many cells do actually show some increase in Gata4 levels. Fig1D suggests that the number of Gata4 expressing cells is quite similar between 4h and 8h induction, but this needs to be quantified. An explanation for the apparent dosage independence of Gata4 could then be simple threshold effects, such that there is no additional effect of increased Gata4 levels in WT cells without any further requirement of feedback regulation after a certain threshold level of Gata4 is reached. Have the authors considered such a simple model? An important point is that in the current setup distinguishing between dosage effects and effects of extended presence of Gata4 cannot be distinguished. Wouldn't titrating the amount of doxycycline used for induction be a more direct way to achieve different initial levels of Gata4 expression? Another point the authors should appropriately discuss and consider is that a lack of effect of different doses/durations of Gata4 expression could be due to the fact that by the time Gata6 is induced, the levels of Gata4 in cells previously treated for different periods of time are no longer detectably different. Such a regulation would equally result in indistinguishable cell fate proportioning. Can the authors exclude such a regulation? This is an important point at the heart of the authors conclusion.
3. The authors make some general statements on cell differentiation (e.g. l205). They also claim that the Fgf4-based mechanism of lineage proportioning could act in a range of tissues during development. However, the use of the term differentiation for the induction of PrE-identity (or Gata-factor expression to be exact, see comment below) after Gata4 overexpression is problematic. The system chosen by the authors is entirely artificial. ES cells normally do not differentiate into extraembryonic cell types. It needs to be made clear in the manuscript that they do not study a differentiation process that normally occurs in the embryo or in differentiating ESC cultures. The system the authors are using would, in my opinion, rather qualify as cell programming or transdifferentiation than as differentiation. I suggest presenting the system using clearer unambiguous language and to try to avoid any generalisations based on an artificial transgene-overexpression based system. The results have to be presented with this limitation in mind.
4. It is unclear how 'PrE-like' (as stated e.g. in the abstract) the cells really are after a short pulse of Gata4 expression. No proper characterisation has been performed but needs to be included, if the authors want to term these cells PrE-like.
5. How is the statement in l112 that "The clear separation between the two populations suggests that the increase in the proportion of double negative cells at the expense of GATA6+; NANOG- PrE-like cells beyond 40 h is mostly fueled by the downregulation of NANOG expression in the GATA6-negative cell population, combined with a slower proliferation of the GATA6-positive population, rather than by the reversion of PrE-like into double negative cells." supported by the data?
6. Would the data and modelling performed by the authors be in line with a model in which the decision to express Gata6 is a stochastic choice (with a certain probability based on the levels of Gata4 induction) that is then stabilized and reinforced by Fgf signalling rather than Fgf signalling having an instructive role?
7. The statement in line 187 "This indicates that GATA4-mCherry expression negatively regulates FGF4 signaling during cell type specification." is not supported by the data. The authors show only a correlation and actually correctly say so in line 195.
8. In Fig 2F statistical analysis between the re-seeded conditions is required for the conclusion that "the proportion of PrE-like cells systematically increased with cell density". Replating itself appears to quite drastically impact lineage distribution. Do the authors have an explanation for this?
9. Fig 2G shows a key experiment illustrating the local effect of Fgf4 expression on first and second neighbours. The authors have investigated this effect using a Fgf-signalling reporter. Why did they not assay Gata6 expression in this assay instead of a Spry reporter? This would be the experiment to show that also Gata6 expressing cells (after transient Gata4 induction) are clustered around Fgf4 producing cells and be a strong piece of evidence to show that local Fgf4 signalling and cell-cell communication is indeed involved in cell identity proportioning. The cell lines required for this experiment (including Fgf4 mutant Gata4 inducible ESCs) appear to be available.
10. The authors conclude from data in Fig 3A that proper cell type proportioning depends on initial Gata4 levels in Fgf4 mutants, in contrast to WT cells where the initial levels appear more irrelevant. Is 10ng/ml too high a dose? Would using a lower concentration (such as ~2ng/ml suggested by Fig 2D to give WT-like distribution) result in a complete rescue of cell lineage proportioning in this assay? Formally a control of adding additional Fgf4 to WT cells will also ne needed to control for a potential effect of exogenous Fgf4 addition.
11. Does the model in Fig 3E consider potentially varying doses of exogenous Fgf4? Can the model also predict what happens if Fgf4 is added to WT cells, as suggested above as control? In general, the value of this model is unclear. Figure 3E is near impossible to understand, no quantitative information is given.
12. Fig4A: What were WT and Fgf4 mutant cells treated differently in this assay (8h vs 4h, respectively)?
13. Does the interpretation that at 24h there is a difference in Fig 4C survive statistical scrutiny? Only few datapoints are shown and any apparent differences seem due to outliers rather than a shift in cluster radii. How often were these experiments independently repeated? This information is missing. In Fig 4B, I cannot appreciate any difference between cell lines.

Minor points:

a) More information on statistics should be given in the Figures and legends.

b) Percentages should be indicated in the quadrants of the FACS plots of Fig 3A and E.

c) What is the underlying evidence for the statement: "The specification of Epi- and PrE-like cells in ESCs shows both molecular and functional parallels to the patterning of the ICM of the mouse preimplantation embryo."

d) Fig 5C is difficult to interpret without a comprehensive decoding of colour information.

Significance

This manuscript provides novel insights into the role of Fgf-mediated cell-cell communication to establish proper ratios of cell identities in a PrE-induction system. The authors provide some interesting data and interpretation. Overall, the significance is slightly impaired by the highly artificial nature of the studied cell fate specification event.

This manuscript will be of interest to readers working on early embryonic cell fate decision as well as researchers working on modelling of cellular processes.

My expertise lies in the field of cell fate decision and pluripotency.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript Raina et al. use an in vitro model of PE specification based on the transient overexpression of GATA4 in ESCs to show that the acquisition of primitive endoderm (PE) identity is governed at the population levels by cell-cell interactions mediated by FGF signaling. The authors further argue that the specification of a defined proportion of "PE" and "Epiblast" cells in a differentiating population of ESC is an emergent property of a system where paracrine signaling shifts the balance between two alternative stable states. Overall, the work does not reach radically new conclusions: broadly similar models are outlined in several other publications, including from the authors. Yet this study makes use of elegant genetic models and is particularly well executed. In addition, it includes a very accurate characterisation of the spatial range of FGF signaling activity that is original and adds on the existing knowledge. Moreover, the authors show novel evidence suggesting that GATA factors inhibits Fgf4 transcription and the activity of the FGF signaling pathway in ESCs.

Two major points deserve further clarification:

In this manuscript the authors claim that the proportions of cells acquiring PE fate is, at least in the experimental setup adopted, largely independent from the levels of GATA4 induction, and therefore of the initial state of the gene regulatory network regulating this cell fate transition. However, the authors should discuss how the current findings relate to their previous results, showing that the duration/levels of Gata4 induction, in a similar experimental setting, play an important role in determining the final proportion of cells cell acquiring "PE" fate. Absolute expression levels may be crucial for this distinction, but the authors seem to exclude this possibility (see figure S3).

Most importantly, the authors incorporate in their model the notion that GATA6 inhibits FGF signaling. It would be interesting to understand how such inhibition is mechanistically mediated. For instance GATA6 has been shown to bind in proximity of the Fgfr2 gene (Wamaitha et al., Genes and Dev., 2015). Alternatively, the authors show a direct effect on Fgf4 expression. The short time window of the reported repressive transcriptional effects (8h, Fig 2 middle), might suggest a direct regulation. The authors should test this possibility, and discuss what alternative modes of regulation could be envisaged (for instance, indirect effects mediated by Nanog). This is a key result that deserves a more detailed mechanistic characterisation.

Minor points:

Fig S1: The authors should show quantifications of Nanog and GATA6 levels before the beginning of the differentiation protocol.

Line 106: The authors write "the initially large proportion of GATA6+; NANOG+ double positive cells". It appears that at 16h of differentiation ESCs have already partitioned between Gata6 or Nanog expressing cells. The authors should rephrase the sentence to reflect what seems to be an almost total absence of truly double positive cells. Possibly, an analysis conducted at earlier time points could clarify these dynamics.

Line 124: The authors write "... concentration dependent downregulation of NANOG expression". The effects may rather depend on the time of doxycycline stimulation.

Line 192: The authors write "...and confined to cells with low GATA4-mCherry expression levels". It would be helpful to have an indication of the cell boundaries, possibly showing localisation of a membrane bound protein.

It would be interesting for the authors to discuss how the spatial range of FGF activity measured in culture could affect PE specification in the embryo.

Significance

See above.

Transparent Peer Review

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Review of "Co-chaperone involvement in knob biogenesis implicates host-derived chaperones in malaria virulence." by Diehl et al for Review Commons.

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**Major Comments.** __

1. In this paper the function of Plasmodium falciparum exported protein PFA66, is investigated by replacing its functionally important dnaJ region with GFP. These modified parasites grew fine but produced elongated knob-like structures, called mentulae, at the surface of the parasites infected RBCs. Knobs are elevated platforms formed by exported parasite proteins at the surface of the infected RBC that are used to display PfEMP1 cytoadherance proteins which help the parasites avoid host immunity. The mentulae still display some PfEMP1 and contain exported proteins such as KAHRP but can no longer facilitate cytoadherence. Complementation of the truncated PFA66 with full length protein restored normal knob morphology however complementation with a non-functional HPD to QPD mutant did not restore normal morphology implying interaction of the PFA66 with a HSP70 possibly of host origin is important for function. While a circumstantial case is made for PFA66 interacting with human HSP70 rather than parasite HSP70-x, is there any direct evidence for this eg, protein binding evidence? I feel that without some additional evidence for a direct interaction between PFA66 and human HSP70 then the paper's title is a little misleading.

   We thank the reviewer for their kind words. They are correct that we do not show direct evidence of such an interaction, but would like to note that we, and others, despite concerted efforts to produce direct evidence, have always been hindered by the nature of the experimental system. As noted also in our reply to Reviewer 3, the inability to genetically modify the host cell leads us to suggest that indirect evidence is the best that can conceivably be provided at this time. Our evidence, although indirect, is the first experimental evidence for the importance of such an interaction, all other suggestions having been based on “guilt by association” i.e. protein localisation or co-IP analyses.

Was CSA binding restored upon complementation of ∆PFA with the full-size copy of PFA66?

As this project grew organically and was driven by the results already obtained, we decided to use knob morphology via SEM as a “proof-of-principle” to show that we could reverse the phenotype. Thus, while we cannot comment on whether ALL functions of PFA66 are complemented, we suspect that if the knobs revert to their WT morphology, this is likely to be true for the other tested phenotypes. We do not feel that revisiting all of our assays (which would basically entail repeating almost every experiment so far carried out) would really be much more informative. We have added a note in the discussion stating “We wish to note that we cannot unequivocally state that our complementation construct allows reversion of all the aberrant phenotypes herein investigated, however we feel it likely that all abnormal phenotypes are linked and thus our “proof-of-principle” investigation of knob/eKnob phenotypes is likely to be reflected in other facets of host cell modification and can thus be seen as a proxy for such.”.

**Minor Comments**

Line 36, NPP should be NPPs if referring to the plural.

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Changed

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Line 37, MC should be MCs if referring to the plural. By the way this acronym is never used in the text, it's always written 'Maurer's clefts'.

Changed

Abstract, Line 52-53, could be changed to "uncover a new KAHRP-independent..." as it currently implies (albeit weakly) that that this is the first observation of a KAHRP-independent mechanism for correct knob biogenesis. Maier et al 2008, have previously shown that knock out of PF3D7_1039100 (J-domain exported protein), greatly reduced knob size and knock out of PHISTb protein PF3D7_0424600, resulted in knobless parasites.

Correct. In line with the suggestions of another reviewer, this section has been changed.

In the Abstract it is mentioned that "Our observations open up exciting new avenues for the development of new anti-malarials." This is never really expanded upon in the rest of the paper and so seems like a bit of a throwaway line and could be left out.

Good point, changed

Line 59, WHO world malaria report should be cited here since these numbers are from the report not a paper from 2002.

Done

Line 67, Marti et al 2004 should be cited here as its published at the same time as Hiller et al 2004.

Our mistake. Done

Line 76, I suggest using either 'erythrocyte' or 'red blood cell' throughout the text not both.

We now use erythrocyte throughout

Line 80, Maier et al 2008 should be referenced here.

Done

Line 87, the authors should cite Birnbaum et al 2017 for the technique used. This is cited immediately after (line 98) in the results section but could be addressed at both points in the text.

Done

Line 123, IFAs and live cell imaging failed to detect the PFA-GFP protein and the author proposes this is due to low expression levels. However, PFA66 is expressed at ~350 FPKM in the ring stage and previous studies from your own group have visualised it using GFP before. Is there another explanation for this such as disruption of the locus here has served to greatly reduce the expression level of the fusion protein?

The truncated protein is now distributed throughout the whole erythrocyte cytosol, not concentrated into J-dots, likely making detection difficult. We wish to note that our original GFP tagged PFA66 lines (Külzer et al, 2010) did not really show a strong signal in comparison to other lines we are used to analysing. We further believe that the sub-cellular fractionation (Figure S1) demonstrates the erythrocyte cytosolic localization of the truncated PFA66. We have no evidence that truncation causes lower expression, but any future revision will include a comparison of expression levels of endogenously GFP tagged dPFA and PFA66.

Line 147, for consistency it would be best to introduce infected red blood cell (iRBC) at the beginning of the main text and use throughout the text instead of switching between 'infected human erythrocyte' and iRBC.

We agree, and have changed accordingly

Line 153, Fig S2A does not exist.

We apologise, this has been changed

Lines 156-158: Different knob morphologies are described with repeated reference to Fig2 and FigS2. Since multiple whole-cell SEM images are displayed in these figures it would be worth adding lettering and/or zoomed-in regions of interest highlighting examples of each aberrant knob type.

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This has now been added to Figure S2.

Line 178-179, "Although not highly abundant in either sample, the morphology of Maurer's clefts appeared comparable in both samples (data not shown)." Why is the data not shown? Representative images of Maurer's clefts from each line should be included in the supplementary figures or this in-text statement should more clearly justified.

Figure S3 has been adjusted to also show Maurer´s clefts in more detail. An Excel table of Data can be provided if necessary.

Line 196, indirect immunofluorescence assay (IFA).

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Changed

Line 201, how was the 'non-significant difference' measured? PHISTc looks quite different by eye. Rephrase the term "significant difference" as localisation of these exported proteins was compared visually rather than quantified. Otherwise, a measure of mean fluorescence intensity could be taken for each protein as a basic comparison between the two lines. In the Figure legend of S4, the term "no drastic difference", is used suggesting this was not quantified. By the way, PHISTc appears different by the represented figure.

We apologise for our use of a specific term for non-statistically verified observations. The PHISTc image the reviewer comments on, was presented incorrectly (too much brightness introduced during processing) and is now correct. We mean to say that we could not (in a blinded check), tell the difference between WT and KO IFA images. Only KAHRP (in our opinion) demonstrated a different fluorescence pattern. As KAHRP has previously been implicated in knob formation, we then analysed this phenotype in more detail. A detailed analysis of the fluorescence pattern in the other IFAs does, in our eyes, not add to the story or add any real value to our observations.

Line 213, you now have 3 versions for the word wild type, 'wild type', 'wild-type' and 'WT', best to choose one for consistency.

Changed

Line 232, 'tubelike' to 'tube-like'.

Changed

Line 279, just use 'IFA', the acronym has already been explained earlier in the text.

Changed

Line 319, 'permeation' should be 'permeability'.

Changed

Line 353, 'The action of host actin is known' to 'Host actin is known'.

Changed

Line 373, 'through their role as regulators'.

Changed

Line 402, either use 'HSP70-x' or 'HSP70-X' throughout the text.

Changed

Line 540, the speed used to pellet the samples for sorbitol lysis assay, 1600g is quite high and could reflect RBC fragility rather than direct sorbitol induced lysis. The parasitemia is also very low, and previous published methods have used ~90% parasitemia rather than the 2% used here. We are not saying the method is wrong but please check it is accurate.

We used the method of our former colleague Stefan Baumeister (University of Marburg), who is an expert in analysis of NPP, thus we are sure the method is correct. We are in fact tempted to remove the NPP data as they deflect from the main narrative of the manuscript, this being the reason we include them only as supplementary data

Line 479, 10µm should be 10 µM.

Changed

In Fig 1A, the primers A, B, C etc are not explained anywhere that I can see.

This information has now been included in the 1A Figure legend and table 2A.

Figure 1B, I do not see any clear band for the 3' integration indicated with the *. Can a better image be shown?

We apologise. Integration PCRs are notoriously challenging. Any revised manuscript will include better quality images

It seems from Fig 3G,H,I that the KAHRP puncta are bigger in ∆PFA but are as abundant as CS2. Given that KAHRP is associated with knobs how do you reconcile this with there being fewer knobs per unit area in ∆PFA compared to CS2 as in Fig 2B? The numbers of knobs/KAHRP spots/Objects per um2 seems to vary between Fig 2 and 3. Please provide some commentary about this.

We are not sure if all KAHRP spots actually label eKnobs, and it is possible that there are KAHRP “foci” that are not associated with eKnobs. We also wish to note that the data in figure 2 and 3 were produced using very different techniques. Sample preparation may lead to membrane shrinkage or stretching, and the different microscopy techniques have very different levels of resolution. For this reason we do not believe that the data from these very different independent experiments can be compared, however a comparison within a data set is possible and good practice.

In the bottom panels of Fig 4, KAHRP::mCherry appears to extend beyond the glycocalyx beyond the cell. Is this an artifact?

We checked assembly of the figure and are sure that this was not introduced during production of the figure. Our only explanation is that WGA does not directly stain the erythrocyte membrane, but the glycocalyx. A closer examination of the WGA signal reveals that it is weaker at this point (and also in the eKnobs i, ii) so potentially the KAHRP signal is beneath the erythrocyte plasma membrane, but the membrane cannot be visualised at this point.

Line 837, does this refer to 10 technical replicates or was the experiment repeated on 10 independent occasions? This should at least be done in 2 biological replicates given the range in technical replicates on the graph. Was CS2 considered as '100% lysis' or the water control described in the method? Please provide more detail.

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This figure is the result of 10 biological and 4 technical replicates. A number of data points were removed as lying outside normal distribution (Gubbs test). The highest value within a biological replicate was set to 100% to allow comparison of results. This has now been corrected in the text.

Reviewer #1 (Significance (Required)):

This is a reasonably significant publication as it describes knob defects that to my knowledge have never been observed before. Importantly, the deletion of the J domain from PFA66 is genetically complemented to restore function really confirming a role for this protein in knob development. Amino acids critical for the function of the J-domain are also resolved. Apart from some minor technical and wording issues the paper is really nice work apart from one area which is the proposed partnership of PFA66 with human HSP70 for which there is not much direct evidence. If this evidence can be provided, we think this work could be published in a high impact journal. Without the evidence, it could find a home in a mid-level journal with some tempering of the claims of PFA66's interaction with human HSP70.

**Referee Cross-commenting**

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There seems to be a high degree of similarity in the reviewers' comments and I think as many issues as possible should be addressed. I definitely agree that the term mentula should be not be used.

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We have now adopted the suggestion of Reviewer 3, and use the term eKnobs.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Plasmodium falciparum exports several proteins that contain J-domains and are hypothesized to act as co-chaperones to support partner HSP70s chaperones in the host erythrocyte, but the function of these co-chaperones is largely unknown. Here the authors provide a functional analysis of one of these exported HSP40 proteins known as PFA66 by using the selection-linked integration approach to generate a truncation mutant lacking the C-terminal substrate binding domain. While there is no fitness cost during in vitro culture, light and electron microscopy analysis of this mutant reveals defects in knob formation that produces a novel, extended knob morphology and ablates Var2CSA-mediated cytoadherence. These knob formation defects are distinct from previous mutants and this unique phenotype is exploited by the authors to show that the HSP70-stimulating "HPD" motif of PFA66 impacts rescue of the altered knob phenotype. In other HSP40 co-chaperones, this motif is critical to stimulate partner HSP70 activity, suggesting that PFA66 acts as a bona fide co-chaperone. Importantly, previous work by the Przyborski lab and others has shown that deletion PfHSP70x, the only HSP70 exported by the parasite, does not phenocopy the PFA66 mutant, implying that the partner HSP70 is of host origin. The results are exciting but I have some concerns about controls needed to properly interpret the functional complementation experiments. My specific comments are below.

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We agree that some control experiments are missing, and these will be included in any future revision.

**Major comments**

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• The failure of the HPD mutant PFA66 to rescue the knob-defect is very interesting. However, the authors need to determine that the HPA mutant is expressed at the same level as the WT (by quantification against the loading controls in the western blots in Fig 1D and Fig S6H) and is properly exported (by IFA and/or WB on fractionated iRBCs, as done for the GFP-fused truncation in Fig S1A). Otherwise, the failure to rescue is hard to interpret. If these controls were in place, the conclusion that a host HSP70 is likely being hijacked by PFA66 is appropriate. This genetic data would be greatly strengthened by in vitro experiments with recombinant protein showing activation of a host HSP70 by PFA66, but I realize this may be out of the scope of the present study. Along these lines, it might be worth discussing the finding by Daniyan et al 2016 that recombinant PFA66 was found to bind human HSPA1A with similar affinity to PfHSP70x but did not substantially stimulate its ATPase activity, suggesting this is not the relevant host HSP70. This study is cited but the details are not discussed. __

As in our answer to Reviewer 1, we will examine the expression and localisation of both WT and mutant PFA66.

We are currently expressing and purifying a number of HSP40/70 combinations for exactly the kind of analysis suggested and hope to include such data in future revisions, but as the reviewer fairly notes, this is really beyond the scope of the current study.

Regarding Daniyan et al (and other) papers: The fact that PFA66 can stimulate PfHSP70x does not preclude that it also interacts with human HSP/HSC70, and indeed there is some stimulation of human HSP70. Daniyan and colleagues did steady-state assays in the absence of nucleotide exchange factors. Therefore, the stimulation of human HSP/HSC70 is not very prominent. One should either do single-turnover experiments or add a nucleotide exchange factor to make sure that nucleotide exchange does not become rate-limiting for ATP hydrolysis. This is completely independent of the results for PfHSP70-X the intrinsic nucleotide exchange rates of the studied HSP70s could be very different. Also, it is important to understand that J-domain proteins generally do not stimulate ATPase activity much by themselves but in synergism with substrates, allowing the possibility that such an in vitro assay may not reflect the situation in cellula. dditionally the resonance units in the SPR analysis for PFA66-HsHSP70 are lower than those for PFA66-PfHSP70-X. This could mean that PFA66 is a good substrate for PfHSP70-X but not for HsHSP70, but this does not mean that PFA66 does not cooperate with HsHSP70.

- The authors claim that truncation of PFA66 alters the localization of KAHRP but not the other exported proteins they evaluated by IFA (Fig S4). This seems baseless as they don't apply the same imageJ evaluation to these other proteins. Similarly, the statement that KAHRP structures "appear by eye to have a lower circularity, although we were not able to substantiate this with image analysis" is subjective/qualitative and should probably be removed.

We mean to say that we could not (in a blinded check), tell the difference between WT and KO IFA images. Only KAHRP (in our opinion) demonstrated a different fluorescence pattern. As KAHRP has previously been implicated in knob formation, we then analysed this phenotype in more detail. A detailed analysis of the fluorescence pattern in the other IFAs does, in our eyes, not add to the story or add any real value to our observations.

The statement on the circularity has been removed according to the reviewers wishes.

-The section title "Chelation of membrane cholesterol...causes reversion of the mutant phenotype in ∆PFA" seems an overstatement given the MBCD effect on the knob morphology is fairly weak and remains significantly abnormal.

The title of this section was misleading, we agree. We have retitled it “Chelation of membrane cholesterol but not actin depolymerisation or glycocalyx degradation causes partial reversion of the mutant phenotype in ∆PFA” to clarify that the reversion was only partial (as explained by the following text in the manuscript).

**Minor comments**

- The DNA agarose gel image in Fig 1B is not very convincing. Most of the bands are faint and there is a lot of background/smear signal in the lanes. Also, it would help for clarity if the primer pairs used for each reaction were stated as shown in the diagram (rather than simply "WT", "5' Int" and "3' Int").

We apologise. Integration PCRs are notoriously challenging. Any revised manuscript will feature clearer images.

- Given the vulgar connotation of "mentula", the authors might consider an alternative term.

We have now adopted the term “eKnobs” suggested by Reviewer 3.

- lines 67-69: The authors may wish to cite a more recent review that takes into account updated Plasmepsin 5 substrate predication from Boddey et al 2013 (PMID: 23387285). For example, Boddey and Cowman 2013 (PMID: 23808341) or de Koning-Ward et al 2016 (PMID: 27374802).

A fair point, we have now added Koning-Ward.

- lines 77-79: "deleted" is repetitive in this sentence.

Changed

- line 115: It might be clearer to state "endogenous PFA66 promoter"

Changed

- lines 131-132: "...these data suggests that deletion of the SBD of PFA66 leads to a non-functional protein." Behl et al 2019 (PMID: 30804381) showed the recombinant C-terminal region of PFA66 (residues 219-386, including the SBD truncated in the present study) binds cholesterol. The authors may wish to mention this along with their reference to Kulzer et al 2010 showing PFA66 segregates with the membrane fraction, suggesting cholesterol is involved in J-dot targeting.

We should have noted this connection and thank the reviewer for bringing it to our attention. This section has been revised to include this important information.

- line 198: It's not clear what is meant by "+ve" here and afterward. Please define.

We have now changed this to “structures labelled by anti-KAHRP antibodies”, or merely “KAHRP”.

- lines 749-750: "Production of PFA and NEO as separate proteins is ensured with a SKIP peptide". Translation of the 2A peptide does not always cause a skip (see PMID: 24160265) and often yields only about 50% skipped product (for example, PMID: 31164473). Because of the close cropping in the western blots in Fig 1C or S1A this is difficult to assess. Is a larger unskipped product also visible? Beyond this one point, it is general preferable that the blots not be cropped so close.

A very valid point, and in other parasite lines we have indeed detected non-skipped protein. In our case, we visualise a band at the predicted molecular mass for the skipped dPFAGFP and the commonly observed circa. 26kDa GFP degradation product. The full-length blots have now been included as supplementary data (Figure S7).

- lines 867-868: Explain more clearly what "Cy3-caused fluorescence" is measuring.

The Cy3 channel refers to anti-var2CSA staining, and we have now included this information.

- Several figure legends would benefit from a title sentence describing what the figure is about (ie, Fig legends 1, 3, 5, S1, S5 & S6)

This has been added.

Reviewer #2 (Significance (Required)):

This manuscript by Diehl et al reports on the function of the exported P. falciparum J-domain protein PFA66 in remodeling the infected RBC. Obligate intracellular malaria parasites export effector proteins to subvert the host erythrocyte for their survival. This process results in major renovations to the erythrocyte, including alteration of the host cell cytoskeleton and formation of raised protuberances on the host membrane known as knobs. Knobs serve as platforms for presentation of the variant surface antigen PfEMP1, enabling cytoadherence of the infected RBC to the host vascular endothelium. This process is of great interest as it is critical for parasite survival and severe disease during in vivo infection. The basis for trafficking of exported effectors within the erythrocyte after they are translocated across the vacuolar membrane is not well understood but is known to involve chaperones. This is a particularly interesting study in that it provides evidence in support of the hypothesis, initially proposed nearly 20 years ago, that the parasite hijacks host chaperones to remodel the erythrocyte. This is biologically intriguing and also suggests new therapeutic strategies targeting host factors that would not be subjected to escape mutations in the parasite genome. The work will be of interest to the those studying exported protein trafficking and/or virulence in Plasmodium (such as this reviewer) as well as the broader chaperone and host-pathogen interaction fields.

**Referee Cross-commenting**

I also agree with similarity in comments. Some additional discussion on the failure to localize the PFA66 truncation by live FL is warranted, as noted by reviewer #1. Seems likely that either the level of PFA66 protein is reduced by the truncation or the truncated PFA66 is dispersed from J-dots and harder to visual when diffuse instead of punctate. In either case, the complementing copy (WT or QPD) should be visualized by IFA.

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As noted above, we believe our inability to visualize the truncated protein is likely due to its dispersal throughout the whole erythrocyte cytosol as opposed to lower expression levels, but we will be checking this, and also the localisation of WT and mutant PFA66 complementation chimera and expect to have this result for the next revision.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

The data are for the most part well controlled and reveal a potential function for PFA66 in knob formation. The assays are state of the art and the data provides insight into knob formation.

However, some conclusions are not fully supported by the data. For example, 'uncover a KAHRP-independent mechanism for correct knob biogenesis' (line 52-53) is not supported by the data because PFA66 truncation could result in misfolding of KAHRP and thus lead to knob biogenesis defects.

We meant to imply that not only perturbations/absence of KAHRP lead to aberrant knobs. This is now changed to “…uncover a new KAHRP-independent molecular factor required for correct knob biogenesis.”.

The other major issue is that despite having a complemented parasite line in hand, the parental parasite line is used as a control for almost all assays. This is a critical issue because an alternative explanation for their data would be that expression of truncated PFA66 leads to expression of a misfolded protein that aggregates in the host RBC OR it clogs up the export pathway and indirectly leads to knob biogenesis defects. It is surprising that the authors do not test the localization of dPFA using microscopy especially since it is tagged with GFP. While the complemented parasite line does revert back, this could also be due to the fact that the complement overexpresses the chaperone helping mitigate issues caused by the truncated protein.

As all virulence characteristics we monitor in this study have been verified many times in the parental CS2 parasites in the literature, we think that the best comparative control is indeed the truncated cell line. The large part of our study aimed to characterize differences in various characteristics upon inactivation of PFA66 function, and for this reason we used the parental WT line as a control. Using the complementation line would not truly reflect the effect of PFA66 truncation, as PFA66::HA was not expressed from an endogenous locus, but rather from an episomal plasmid. This itself may result in expression levels which differ from WT, and thus this parasite line cannot be seen as the gold-standard control for assaying PFA66 function.

We did indeed try to localize dPFA (lines 122-123 in the original manuscript), but were unsuccessful, likely due to diffusion of dPFA throughout the entire erythrocyte cytosol (as opposed to concentration into J-dots as the WT). For this reason we carried out fractionation instead, and could show that dPFA is soluble within the erythrocyte cytosol. This experiment additionally excludes any blockage of the export pathway as no dPFA was associated with the pellet/PV fraction. Other proteins were still exported as normal (Figure S4), further supporting a functional export pathway. Indeed, as reported by ourselves and our colleagues (particularly from the Spielmann laboratory, Mesen-Ramirez et al 2016, Grüring et al 2012), blockage of the export pathway is likely to lead to non-viable parasites as the PTEX translocon seems to be the bottleneck for export of a number of proteins, many of which are essential for parasite survival.

Reviewer #3 (Significance (Required)):

The malaria-causing parasite extensively modifies the host red blood cell to convert the host into a suitable habitat for growth as well as to evade the immune response. It does so by exporting several hundred proteins into the host cell. The functions of these proteins remain mostly unknown. One parasite-driven modification, essential for immune evasion, is the assembly of 'knob' like structures on the RBC surface that display the variant antigen PfEMP1. How these knobs are assembled and regulated is unknown.

In the current manuscript, Diehl et al target an exported parasite chaperone from the Hsp40 family, termed PFA66. The phenotypic observations described in the manuscript are quite spectacular and well characterized. The truncation of PFA66 results in some abnormal knob formation where the knobs are no longer well-spaced and uniform but instead sometimes form tubular structures termed mentulae. The mechanistic underpinnings driving the formation of mentulae remain to be understood but that will probably several more manuscripts to be deciphered.

We thank the reviewer for their kind comments, and also for the recognition that this current manuscript is merely the exciting beginning of a story!

**Major Comments:**

General comment on the use of controls: The large part of our study aimed to characterize differences in various characteristics upon inactivation of PFA66 function, and for this reason we used the parental WT line as a control. Using the complementation line as a control in this context would not truly reflect the effect of PFA66 truncation, as PFA66::HA was not expressed from an endogenous locus, but rather from an episomal plasmid. This itself may result in expression levels which differ from WT, and thus this parasite line cannot be seen as the gold-standard control for assaying PFA66 function. Our complementation experiments were initially designed to verify that phenotypic changes ONLY related to inactivation of PFA66 function and were (as unlikely as this is) not due to second site changes during the genetic manipulation process. To avoid lengthy and not really very informative analysis of the complementation line, we used knob morphology via SEM as a “proof-of-principle”. However, as the reviewer is formally correct, we have added a passage to the discussion stating that “We wish to note that we cannot unequivocally state that our complementation construct caused reversion of all the aberrant phenotypes herein investigated, however we feel it likely that all abnormal phenotypes are linked and thus our “proof of principle” investigation of knob/eKnob phenotypes is likely to be reflected in other facets of host cell modification and can thus be seen as a proxy for such.“.

Fig 3: The control used here is the parental line. Was there a reason why the complemented parasite line was not used as the control? Showing that the KAHRP localization and distribution is restored upon complementation would greatly increase the confidence in the phenotype.

Please see our general comments above.

Fig 5: The data showing a defect in CSA binding are convincing but again only the parental control is used and not the complemented parasite line. The complemented parasite line should be used as a control for the PFA binding mutant.

Please see our general comments above, and also our reponse to reviewer 1.

In 5D, the defect in dPFA seems to be occur to a lesser degree than Fig. 2C. How many biological replicates are shown in each of these figures? The figure legend says 20 cells were quantified via IFA but were these cells from one experiment? The expression of mentulae seems quite variable, while the authors mention '22%' (line 164), it seems in most other experiments, its more ~10% (5D and S6B, D-E). Were these experiments blinded?

As the reviewer is likely aware, subtle differences in parasite culture conditions, stage, fixation, SEM conditions and length of time in culture between time experimental time points can lead to variations in results. Due to the time required to generate the data for figure 5, these experiments took place months after the original (i.e. Figure 2C) analysis. It is not possible to directly compare the results of these two independent experiments, however it is possible to compare the results of the parasite lines included within each set of experimental data. Due to the time and cost involved, each of these experiments represents only one biological replicate. If required, we can include more replicates, although this is more likely to further complicate the situation due to the reasons mentioned above.

Fig S6G: The staining suggests that most PfEMP1 in is not exported, in any parasite line. Staining for PfEMP1 is technically challenging and these data are not enough to show that expression level is 'similar' (Line 279-280). It may be more feasible to use the anti-ATS antibody and stain for the non-variant part of PfEMP1 (Maier et al 2008, Cell).

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It is well known that a large portion of PfEMP1 remains intracellular. This figure does not aim to differentiate between surface exposed and internal PfEMP1, but merely to show that similar TOTAL PfEMP1 is expressed in the deletion line, and also that the parasites have not undergone a switching event which would lead to loss of CSA binding ability. We will endeavour to address this in future revisions by Western Blot but wish to note that WB analysis of PfEMP1 is notoriously difficult.

Lines 320-322: The logic of why increased robustness of the RBC membrane would lead to faster parasite growth is confusing. It is likely that the loss of PfEMP1 expression leads to faster growth. The loss of NPP is minimal and may not cause growth defects in rich media.

As far as we can detect, there is no loss of total PfEMP1 expression (as verified by figure S6G), but rather a drop in surface exposure and functionality, which is unlikely to affect parasite growth rates. What we intended to say was that the NPP assay is influenced by fragility of the erythrocyte, and therefore a stiffer erythrocyte may be more resistant to sorbitol-induced lysis. As the NPP result does not really add much to the main narrative of this manuscript, we would prefer not to invest unnecessary effort for a minimal potential readout. Indeed, we are tempted to remove the NPP data as they deflect from the main findings of the manuscript, this being the reason we include them only as supplementary data

Lines 433-434: These data do support a function for HsHsp70 but these data are among many others that have previously provided circumstantial evidence for its role in host RBC modification. May be a co-IP would help support these conclusions better.

Despite all our best efforts and publications, we have been unable to detect this interaction in co-IP or crosslink experiments, although we were successful in detecting interactions between another HSP40 (PFE55) and HsHSP70 (Zhang et al, 2017). Although this is disappointing, it may be explained due to the transient nature of HSP40/HSP70 interactions. We agree that our suggestion (that parasite HSP40s functionally interact with human HSP70) is not novel (we and others have noted this possibility for over 10 years), however the challenging nature of the experimental system makes it very difficult to show direct evidence of the importance of this interaction in cellula. Over the past decade we have use numerous experimental approaches to try to address this but have always been confounded by technical challenges. In 2017 the corresponding author took a sabbatical to attempt manipulation of hemopoietic stem cells to reduce HSP70 levels in erythrocytes, however it appears (unsurprisingly) that HsHSP70 is required for stem cell differentiation, and thus this tactic was not followed further. The authors believe that, due to the lack of the necessary technology, indirect evidence for this important interaction is all that can realistically be achieved at this time, and this current study is the first to provide such evidence.

We would further like to note that a successful co-IP would not directly verify a functional interaction between PFA66 and HsHSP70, but could also reflect a chaperone:substrate interaction between these proteins, and is therefore not necessarily informative.

**Minor Comments:**

Fig1: The bands are hard to see in WT and 3’Int. May be a better resolution figure would help? Also, the schematic shows primers A-D but the figure legend does not refer to them. It would be useful to the reader to have the primers indicated above the PCR gel along with the expected sizes.

We apologise. Integration PCRs are notoriously challenging. Any revised manuscript will contain clearer images.

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Fig S1: The NPP data could be improved if tested in minimal media. It has been shown that NPP defects do not show up in rich media (Pillai et al 2012, Mol. Pharm. PMID: 22949525). Does complementation restore NPP and growth rate?

As the NPP result does not really add much to the main narrative of this manuscript, we would prefer not to invest unnecessary effort for a minimal potential readout. Indeed, we are tempted to remove the NPP data as they deflect from the main findings of the manuscript, this being the reason we include them only as supplementary data. Likewise the complementation experiments are, we feel, unnecessary.

Fig 4: It is not clear what the line scan analysis are supposed to show. What does ‘value’ on the y-axis mean?

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These are line scans of fluorescence intensity (arbitrary units) along the yellow arrows shown on the fluorescent panels. This is now indicated in the figure legend.

Fig S5D: Maybe it was a problem with the file but no actin staining is visible.

The actin stain was visible on the screen, but unfortunately not in the PDF. We have applied (suitable) enhancement to produce the images in the new version.

Fig 6: A model for mentulae formation is not really proposed. Only what the authors expect the mentulae to look like.

We have changed the legend to reflect this “Figure 6. Proposed model for eKnob formation and structure.”. We do propose that runaway extension of an underlying spiral protein may lead to eKnobs, thus would like to keep the word “formation”.

Lines 312-313: It is not clear what 'highly viable' means, parasites are either viable or not.

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This has been changed.

Lines 400-405: The authors forgot to cite a complementary paper that showed no virulence defect upon 70x knockout or knockdown (Cobb et al mSphere 2017). Those data also support a role for HsHsp70.

We apologise for the omission. This is now included.

**Referee Cross-commenting**

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I agree, the comments are pretty similar. The authors could tone down their conclusions or add more data to support their conclusions. May be call them elongated knobs or eKnobs, instead of mentula? __

We have now removed the offending term and use eKnobs.

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Referee #3

Evidence, reproducibility and clarity

The data are for the most part well controlled and reveal a potential function for PFA66 in knob formation. The assays are state of the art and the data provides insight into knob formation.

However, some conclusions are not fully supported by the data. For example, 'uncover a KAHRP-independent mechanism for correct knob biogenesis' (line 52-53) is not supported by the data because PFA66 truncation could result in misfolding of KAHRP and thus lead to knob biogenesis defects.

The other major issue is that despite having a complemented parasite line in hand, the parental parasite line is used as a control for almost all assays. This is a critical issue because an alternative explanation for their data would be that expression of truncated PFA66 leads to expression of a misfolded protein that aggregates in the host RBC OR it clogs up the export pathway and indirectly leads to knob biogenesis defects. It is surprising that the authors do not test the localization of dPFA using microscopy especially since it is tagged with GFP. While the complemented parasite line does revert back, this could also be due to the fact that the complement overexpresses the chaperone helping mitigate issues caused by the truncated protein.

Significance

The malaria-causing parasite extensively modifies the host red blood cell to convert the host into a suitable habitat for growth as well as to evade the immune response. It does so by exporting several hundred proteins into the host cell. The functions of these proteins remain mostly unknown. One parasite-driven modification, essential for immune evasion, is the assembly of 'knob' like structures on the RBC surface that display the variant antigen PfEMP1. How these knobs are assembled and regulated is unknown.

In the current manuscript, Diehl et al target an exported parasite chaperone from the Hsp40 family, termed PFA66. The phenotypic observations described in the manuscript are quite spectacular and well characterized. The truncation of PFA66 results in some abnormal knob formation where the knobs are no longer well-spaced and uniform but instead sometimes form tubular structures termed mentulae. The mechanistic underpinnings driving the formation of mentulae remain to be understood but that will probably several more manuscripts to be deciphered.

Major Comments:

Fig 3: The control used here is the parental line. Was there a reason why the complemented parasite line was not used as the control? Showing that the KAHRP localization and distribution is restored upon complementation would greatly increase the confidence in the phenotype.

Fig 5: The data showing a defect in CSA binding are convincing but again only the parental control is used and not the complemented parasite line. The complemented parasite line should be used as a control for the PFA binding mutant. In 5D, the defect in dPFA seems to be occur to a lesser degree than Fig. 2C. How many biological replicates are shown in each of these figures? The figure legend says 20 cells were quantified via IFA but were these cells from one experiement? The expression of mentulae seems quite variable, while the authors mention '22%' (line 164), it seems in most other experiments, its more ~10% (5D and S6B, D-E). Were these experiments blinded?

Fig S6G: The staining suggests that most PfEMP1 in is not exported, in any parasite line. Staining for PfEMP1 is technically challenging and these data are not enough to show that expression level is 'similar' (Line 279-280). It may be more feasible to use the anti-ATS antibody and stain for the non-variant part of PfEMP1 (Maier et al 2008, Cell).

Lines 320-322: The logic of why increased robustness of the RBC membrane would lead to faster parasite growth is confusing. It is likely that the loss of PfEMP1 expression leads to faster growth. The loss of NPP is minimal and may not cause growth defects in rich media.

Lines 433-434: These data do support a function for HsHsp70 but these data are among many others that have previously provided circumstantial evidence for its role in host RBC modification. May be a co-IP would help support these conclusions better.

Minor Comments:

Fig1: The bands are hard to see in WT and 3'Int. May be a better resolution figure would help? Also, the schematic shows primers A-D but the figure legend does not refer to them. It would be useful to the reader to have the primers indicated above the PCR gel along with the expected sizes.

Fig S1: The NPP data could be improved if tested in minimal media. It has been shown that NPP defects do not show up in rich media (Pillai et al 2012, Mol. Pharm. PMID: 22949525). Does complementation restore NPP and growth rate?

Fig 4: It is not clear what the line scan analysis are supposed to show. What does 'value' on the y-axis mean?

Fig S5D: Maybe it was a problem with the file but no actin staining is visible.

Fig 6: A model for mentulae formation is not really proposed. Only what the authors expect the mentulae to look like.

Lines 312-313: It is not clear what 'highly viable' means, parasites are either viable or not.

Lines 400-405: The authors forgot to cite a complementary paper that showed no virulence defect upon 70x knockout or knockdown (Cobb et al mSphere 2017). Those data also support a role for HsHsp70.

Referee Cross-commenting

I agree, the comments are pretty similar. The authors could tone down their conclusions or add more data to support their conclusions. May be call them elongated knobs or eKnobs, instead of mentula?

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Referee #2

Evidence, reproducibility and clarity

Plasmodium falciparum exports several proteins that contain J-domains and are hypothesized to act as co-chaperones to support partner HSP70s chaperones in the host erythrocyte, but the function of these co-chaperones is largely unknown. Here the authors provide a functional analysis of one of these exported HSP40 proteins known as PFA66 by using the selection-linked integration approach to generate a truncation mutant lacking the C-terminal substrate binding domain. While there is no fitness cost during in vitro culture, light and electron microscopy analysis of this mutant reveals defects in knob formation that produces a novel, extended knob morphology and ablates Var2CSA-mediated cytoadherence. These knob formation defects are distinct from previous mutants and this unique phenotype is exploited by the authors to show that the HSP70-stimulating "HPD" motif of PFA66 impacts rescue of the altered knob phenotype. In other HSP40 co-chaperones, this motif is critical to stimulate partner HSP70 activity, suggesting that PFA66 acts as a bona fide co-chaperone. Importantly, previous work by the Przyborski lab and others has shown that deletion PfHSP70x, the only HSP70 exported by the parasite, does not phenocopy the PFA66 mutant, implying that the partner HSP70 is of host origin. The results are exciting but I have some concerns about controls needed to properly interpret the functional complementation experiments. My specific comments are below.

Major comments

• The failure of the HPD mutant PFA66 to rescue the knob-defect is very interesting. However, the authors need to determine that the HPA mutant is expressed at the same level as the WT (by quantification against the loading controls in the western blots in Fig 1D and Fig S6H) and is properly exported (by IFA and/or WB on fractionated iRBCs, as done for the GFP-fused truncation in Fig S1A). Otherwise, the failure to rescue is hard to interpret. If these controls were in place, the conclusion that a host HSP70 is likely being hijacked by PFA66 is appropriate. This genetic data would be greatly strengthened by in vitro experiments with recombinant protein showing activation of a host HSP70 by PFA66, but I realize this may be out of the scope of the present study. Along these lines, it might be worth discussing the finding by Daniyan et al 2016 that recombinant PFA66 was found to bind human HSPA1A with similar affinity to PfHSP70x but did not substantially stimulate its ATPase activity, suggesting this is not the relevant host HSP70. This study is cited but the details are not discussed.
• The authors claim that truncation of PFA66 alters the localization of KAHRP but not the other exported proteins they evaluated by IFA (Fig S4). This seems baseless as they don't apply the same imageJ evaluation to these other proteins. Similarly, the statement that KAHRP structures "appear by eye to have a lower circularity, although we were not able to substantiate this with image analysis" is subjective/qualitative and should probably be removed.
• The section title "Chelation of membrane cholesterol...causes reversion of the mutant phenotype in ∆PFA" seems an overstatement given the MBCD effect on the knob morphology is fairly weak and remains significantly abnormal.

Minor comments

• The DNA agarose gel image in Fig 1B is not very convincing. Most of the bands are faint and there is a lot of background/smear signal in the lanes. Also, it would help for clarity if the primer pairs used for each reaction were stated as shown in the diagram (rather than simply "WT", "5' Int" and "3' Int").
• Given the vulgar connotation of "mentula", the authors might consider an alternative term.
• lines 67-69: The authors may wish to cite a more recent review that takes into account updated Plasmepsin 5 substrate predication from Boddey et al 2013 (PMID: 23387285). For example, Boddey and Cowman 2013 (PMID: 23808341) or de Koning-Ward et al 2016 (PMID: 27374802).
• lines 77-79: "deleted" is repetitive in this sentence.
• line 115: It might be clearer to state "endogenous PFA66 promoter"
• lines 131-132: "...these data suggests that deletion of the SBD of PFA66 leads to a non-functional protein." Behl et al 2019 (PMID: 30804381) showed the recombinant C-terminal region of PFA66 (residues 219-386, including the SBD truncated in the present study) binds cholesterol. The authors may wish to mention this along with their reference to Kulzer et al 2010 showing PFA66 segregates with the membrane fraction, suggesting cholesterol is involved in J-dot targeting.
• line 198: It's not clear what is meant by "+ve" here and afterward. Please define.
• lines 749-750: "Production of PFA and NEO as separate proteins is ensured with a SKIP peptide". Translation of the 2A peptide does not always cause a skip (see PMID: 24160265) and often yields only about 50% skipped product (for example, PMID: 31164473). Because of the close cropping in the western blots in Fig 1C or S1A this is difficult to assess. Is a larger unskipped product also visible? Beyond this one point, it is general preferable that the blots not be cropped so close.
• lines 867-868: Explain more clearly what "Cy3-caused fluorescence" is measuring.
• Several figure legends would benefit from a title sentence describing what the figure is about (ie, Fig legends 1, 3, 5, S1, S5 & S6)

Significance

This manuscript by Diehl et al reports on the function of the exported P. falciparum J-domain protein PFA66 in remodeling the infected RBC. Obligate intracellular malaria parasites export effector proteins to subvert the host erythrocyte for their survival. This process results in major renovations to the erythrocyte, including alteration of the host cell cytoskeleton and formation of raised protuberances on the host membrane known as knobs. Knobs serve as platforms for presentation of the variant surface antigen PfEMP1, enabling cytoadherence of the infected RBC to the host vascular endothelium. This process is of great interest as it is critical for parasite survival and severe disease during in vivo infection. The basis for trafficking of exported effectors within the erythrocyte after they are translocated across the vacuolar membrane is not well understood but is known to involve chaperones. This is a particularly interesting study in that it provides evidence in support of the hypothesis, initially proposed nearly 20 years ago, that the parasite hijacks host chaperones to remodel the erythrocyte. This is biologically intriguing and also suggests new therapeutic strategies targeting host factors that would not be subjected to escape mutations in the parasite genome. The work will be of interest to the those studying exported protein trafficking and/or virulence in Plasmodium (such as this reviewer) as well as the broader chaperone and host-pathogen interaction fields.

Referee Cross-commenting

I also agree with similarity in comments. Some additional discussion on the failure to localize the PFA66 truncation by live FL is warranted, as noted by reviewer #1. Seems likely that either the level of PFA66 protein is reduced by the truncation or the truncated PFA66 is dispersed from J-dots and harder to visual when diffuse instead of punctate. In either case, the complementing copy (WT or QPD) should be visualized by IFA.

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Referee #1

Evidence, reproducibility and clarity

Review of "Co-chaperone involvement in knob biogenesis implicates host-derived chaperones in malaria virulence." by Diehl et al for Review Commons.

Major Comments.

1. In this paper the function of Plasmodium falciparum exported protein PFA66, is investigated by replacing its functionally important dnaJ region with GFP. These modified parasites grew fine but produced elongated knob-like structures, called mentulae, at the surface of the parasites infected RBCs. Knobs are elevated platforms formed by exported parasite proteins at the surface of the infected RBC that are used to display PfEMP1 cytoadherance proteins which help the parasites avoid host immunity. The mentulae still display some PfEMP1 and contain exported proteins such as KAHRP but can no longer facilitate cytoadherence. Complementation of the truncated PFA66 with full length protein restored normal knob morphology however complementation with a non-functional HPD to QPD mutant did not restore normal morphology implying interaction of the PFA66 with a HSP70 possibly of host origin is important for function. While a circumstantial case is made for PFA66 interacting with human HSP70 rather than parasite HSP70-x, is there any direct evidence for this eg, protein binding evidence? I feel that without some additional evidence for a direct interaction between PFA66 and human HSP70 then the paper's title is a little misleading.
2. Was CSA binding restored upon complementation of ∆PFA with the full-size copy of PFA66?

Minor Comments

1. Line 36, NPP should be NPPs if referring to the plural.
2. Line 37, MC should be MCs if referring to the plural. By the way this acronym is never used in the text, it's always written 'Maurer's clefts'.
3. Abstract, Line 52-53, could be changed to "uncover a new KAHRP-independent..." as it currently implies (albeit weakly) that that this is the first observation of a KAHRP-independent mechanism for correct knob biogenesis. Maier et al 2008, have previously shown that knock out of PF3D7_1039100 (J-domain exported protein), greatly reduced knob size and knock out of PHISTb protein PF3D7_0424600, resulted in knobless parasites.
4. In the Abstract it is mentioned that "Our observations open up exciting new avenues for the development of new anti-malarials." This is never really expanded upon in the rest of the paper and so seems like a bit of a throwaway line and could be left out.
5. Line 59, WHO world malaria report should be cited here since these numbers are from the report not a paper from 2002.
6. Line 67, Marti et al 2004 should be cited here as its published at the same time as Hiller et al 2004.
7. Line 76, I suggest using either 'erythrocyte' or 'red blood cell' throughout the text not both.
8. Line 80, Maier et al 2008 should be referenced here.
9. Line 87, the authors should cite Birnbaum et al 2017 for the technique used. This is cited immediately after (line 98) in the results section but could be addressed at both points in the text.
10. Line 123, IFAs and live cell imaging failed to detect the PFA-GFP protein and the author proposes this is due to low expression levels. However, PFA66 is expressed at ~350 FPKM in the ring stage and previous studies from your own group have visualised it using GFP before. Is there another explanation for this such as disruption of the locus here has served to greatly reduce the expression level of the fusion protein?
11. Line 147, for consistency it would be best to introduce infected red blood cell (iRBC) at the beginning of the main text and use throughout the text instead of switching between 'infected human erythrocyte' and iRBC.
12. Line 153, Fig S2A does not exist.
13. Lines 156-158: Different knob morphologies are described with repeated reference to Fig2 and FigS2. Since multiple whole-cell SEM images are displayed in these figures it would be worth adding lettering and/or zoomed-in regions of interest highlighting examples of each aberrant knob type.
14. Line 178-179, "Although not highly abundant in either sample, the morphology of Maurer's clefts appeared comparable in both samples (data not shown)." Why is the data not shown? Representative images of Maurer's clefts from each line should be included in the supplementary figures or this in-text statement should more clearly justified.
15. Line 196, indirect immunofluorescence assay (IFA).
16. Line 201, how was the 'non-significant difference' measured? PHISTc looks quite different by eye. Rephrase the term "significant difference" as localisation of these exported proteins was compared visually rather than quantified. Otherwise, a measure of mean fluorescence intensity could be taken for each protein as a basic comparison between the two lines. In the Figure legend of S4, the term "no drastic difference", is used suggesting this was not quantified. By the way, PHISTc appears different by the represented figure.
17. Line 213, you now have 3 versions for the word wild type, 'wild type', 'wild-type' and 'WT', best to choose one for consistency.
18. Line 232, 'tubelike' to 'tube-like'.
19. Line 279, just use 'IFA', the acronym has already been explained earlier in the text.
20. Line 319, 'permeation' should be 'permeability'.
21. Line 353, 'The action of host actin is known' to 'Host actin is known'.
22. Line 373, 'through their role as regulators'.
23. Line 402, either use 'HSP70-x' or 'HSP70-X' throughout the text.
24. Line 540, the speed used to pellet the samples for sorbitol lysis assay, 1600g is quite high and could reflect RBC fragility rather than direct sorbitol induced lysis. The parasitemia is also very low, and previous published methods have used ~90% parasitemia rather than the 2% used here. We are not saying the method is wrong but please check it is accurate.
25. Line 479, 10µm should be 10 µM.
26. In Fig 1A, the primers A, B, C etc are not explained anywhere that I can see.
27. Figure 1B, I do not see any clear band for the 3' integration indicated with the *. Can a better image be shown?
28. It seems from Fig 3G,H,I that the KAHRP puncta are bigger in ∆PFA but are as abundant as CS2. Given that KAHRP is associated with knobs how do you reconcile this with there being fewer knobs per unit area in ∆PFA compared to CS2 as in Fig 2B? The numbers of knobs/KAHRP spots/Objects per um2 seems to vary between Fig 2 and 3. Please provide some commentary about this.
29. In the bottom panels of Fig 4, KAHRP::mCherry appears to extend beyond the glycocalyx beyond the cell. Is this an artifact?
30. Line 837, does this refer to 10 technical replicates or was the experiment repeated on 10 independent occasions? This should at least be done in 2 biological replicates given the range in technical replicates on the graph. Was CS2 considered as '100% lysis' or the water control described in the method? Please provide more detail.

Significance

This is a reasonably significant publication as it describes knob defects that to my knowledge have never been observed before. Importantly, the deletion of the J domain from PFA66 is genetically complemented to restore function really confirming a role for this protein in knob development. Amino acids critical for the function of the J-domain are also resolved. Apart from some minor technical and wording issues the paper is really nice work apart from one area which is the proposed partnership of PFA66 with human HSP70 for which there is not much direct evidence. If this evidence can be provided, we think this work could be published in a high impact journal. Without the evidence, it could find a home in a mid-level journal with some tempering of the claims of PFA66's interaction with human HSP70.

Referee Cross-commenting

There seems to be a high degree of similarity in the reviewers' comments and I think as many issues as possible should be addressed. I definitely agree that the term mentula should be not be used.

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Referee #1

Evidence, reproducibility and clarity

Bhide and colleagues present an insightful study of how cellular mechanics influences differential cell behaviour during morphogenesis despite apparent genetic homogeneity of the cellular ensembles. They dissect the extensively studied system of mesoderm invagination in Drosophila, focussing on the differences in cell behaviours between the cells in the middle of the infolding tissue and on the periphery that, as far as we know, share a common gene expression profile. They describe sub-cellular dynamics of major effector of apical constriction morphogenesis, the myosin motor distribution, in the invaginating cells and conclude that differences in myosin levels alone cannot account for the observed differences in cell behaviours. In order to understand the cell behaviour inhomogeneity, they turn to biophysical simulation and in an impressively exhaustive manner substantiate the idea that non-linear effects are required for explaining the phenomenon. This theoretical treatment fits well with the notion that the genetic identity of the cells but rather cell-cell mechanical coupling determine the differences in invaginating cell's behaviours. Additionally, the modelling is consistent with the myosin asymmetry and dynamics in the cells whose behaviours is being contrasted. Complementary, and beautifully executed filament-based modelling of microscopic actomyosin contractility further corroborates this view. Finally, the proposed model of non-linear actomyosin contractility dynamics governing the differential cell behaviour across genetically homogenous cellular field, is challenged by two complementary laser ablation and optogenetic experimental approaches. Overall, the results represent convincing evidence that points the tissue mechanics field of Drosophila mesoderm into an interesting new direction and has general implications for the understanding of the interplay between genetic regulation and emergent behaviours of cells operating in mechanically complex multicellular embryonic context.

The study is meticulously executed, highly quantitative and combines effectively experiment and theory. I have only minor comments that concern in particular the presentation of the results.

The paper is very dense and the text does not complement well the results presented in the main figures. Many panels in the Figures are not referred to explicitly. Figure elements are referenced out of order both within and across Figures. Sometimes, particularly, in the last two Figures (3 and 4) the reader is left alone to figure out what the data show (with the appropriately terse legends and without the clear narrative in the text, it is an uphill battle for non-specialists). Some key results are hidden in the sea of elements within the Figure 2 that contains the most important, relevant and impressive data. As an example, on line 168 the authors point to panel 2F to demonstrate the asymmetry of myosin distribution in some cells. To the best of my understanding, this phenomenon is actually shown in Fig 2E which is curiously not referenced at all.

Similarly, Figure 2K and L provide crucial data substantiating much of the conclusions of the paper. It requires a major effort to understand what the graphs mean.

The following simulation results are quite impressive and would deserve a separate Figure which could provide more space for explaining what the parameter maps actually show. What is for instance plotted on the Y axis as steepness?

Secondly, I find the overall narrative of the manuscript needing some reorganisation. The main question is set-up extremely well, however in the middle of the manuscript the focus on the connection between cell behaviours and genetic programs is lost. New conclusions on force transmission between cells emerge, however they are not obviously connected with the question posed from the onset and addressed in the discussion section. My impression is that the authors are conservative in their reasoning, however it does compromise the overall message of the story that should ideally focus on one subject. I find the combined evidence presented sufficiently supportive of the model that is beautifully and eloquently presented in the concluding sentence of the paper:

"This mechanism, which we propose corresponds to the non-linear behaviour predicted by the models, would apply both to central and to lateral cells, with a catastrophic 'flip' being stochastic and rare in central cells, but reproducible in lateral cells because of the temporal and spatial gradient in which contractions occur."

This may not turn out to be the entire story or even entirely correct, but it is certainly and exciting way of thinking about the problem. I wish that the manuscript would stay more on this subject throughout and provide intermediate conclusions supporting this model as the story develops.

Few more minor comments:

Line 36 - typo Line 97 - starting bracket missing Line 126 - data on intensity are presented here. There is also a panel on concentration (Fig 1H). Where is this discussed? Line 132 - panel 2G - disruptive out of sequence reference to a future figure Line 135 - with this regard - please spell out this important conclusion Line 183 - typo Line 210 - insects do not have intermediate filaments Line 238 - please provide a hint of how such global ablations are performed Line 240 - walk us through the Figure, it is too complex to figure it out alone Line 245 - why is the clear hypothesis mentioned above (point 2) rephrased? Line 273 - vague statement

Significance

The results represent convincing evidence that points the tissue mechanics field of Drosophila mesoderm into an interesting new direction and has general implications for the understanding of the interplay between genetic regulation and emergent behaviours of cells operating in mechanically complex multicellular embryonic context.

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Referee #2

Evidence, reproducibility and clarity

Bhide and colleagues explore the mechanisms of cell expansion in epithelial morphogenesis. During the invagination of the Drosophila mesoderm, cells in the center of the prospective mesoderm constrict under the action of actomyosin pulses, while lateral cells elongate towards the center of the mesodermal placode to accommodate the reduction in apical surface of the central cells. Central and lateral cells display strong similarities in terms of gene expression. How are thus this different behaviors (contraction and expansion) accomplished? The authors found that both central and lateral cells assemble actomyosin networks, although lateral cells do it with a certain delay. Mathematical models of cell constriction across the mesoderm using different strain-stress responses showed that strain-induced cell softening was necessary recapitulate the patterns of constriction and expansion observed in vivo. Furthermore, modelling predicts that cells can stretch until the actin networks yield and break. Laser ablation and optogenetic reduction of contractility in central cells results in a reduction in the apical surface area of lateral cells. An optogenetic increase in contractility in lateral cells caused an increase in apical area in central cells. Together, these data suggest that mechanical cues can override and contribute to sculpting genetically defined morphogenetic domains.

I propose to address the following points before further considering the manuscript:

MAJOR

1. Figure 3: following laser ablation of central cells, lateral cells reduce their apical surface. How do the authors know that this reduction in lateral cell apical surface area is an active process, driven by actomyosin-based contraction, rather than a passive response to the expansion of the wound induced by laser ablation? A similar argument could explain the constriction of lateral cells after optogenetic inhibition of actomyosin networks: the central cells relax, expand and compress the lateral cells. To demonstrate active responses of the lateral cells upon laser ablation and optogenetic manipulations of central cells, at the very least the authors should show the distribution of myosin in the lateral cells that constrict and demonstrate the assembly of contractile networks.
2. Modelling suggests that actin networks yield and break in lateral cells. Does this occur in vivo?
3. Lines 166-175: The authors propose that constriction of a cell affects the localization of myosin in its neighbors. However, this is not directly measured. The authors should quantify the relative myosin offset in the cells around constricting cells, and show that that offset is greater (and oriented towards the constricting cell) than in cells around expanding cells. There should be a correlation between the relative size change of a cell and the myosin offset (not just concentration) in their neighbours. In addition, does optogenetic activation of constriction in lateral cells affect the offset of myosin networks in central cells?
4. Fig. 2E-F: the authors argue that the mean myosin concentration in lateral cells at certain times is equivalent to that of central cells earlier in the invagination process. However, the fraction of apical surface area covered by myosin network is consistently lower for lateral cells (and also for central cells that remain unconstricted!). Have the authors considered this fact, and if not, why? Wouldn't this explain, at least in part, why some cells constrict and others do not, if medial myosin networks drive the disassembly of the apical surface? If myosin activity were increased in laterals cells once central cells begin constricting, would that lead to an increased fraction of lateral cell surfaces covered by actomyosin networks and to reduced lateral cell elongation?

MINOR

1. Image panels are missing scale bars in many figures.
2. Fig. 1C'-D': The authors should include a color bar to provide some indication of the scale of the apical areas measured. Same comment for other figures in which apical area is color-coded.
3. Supp. Fig. 2E-F, G-H and Supp. Fig. 6: what is the difference between myosin intensity and myosin concentration? Junctional vs medial localization? Or summed vs mean pixel value? Please be specific, the difference between intensity and concentration is not clear.
4. Line 118: Supp. Fig. 2 does not have panels I and K.
5. Line 223: the authors reference data at 175 sec, but Supp. Fig. 6 does not show any images at that time point. They should be added or a different time point indicated.

TYPOS

1. Abstract: "[in a supracellular context" should be "in a supracellular context".
2. Line 145: should this be a reference to Supp. Fig. 5 instead of Supp. Fig. 4?
3. Line 166: I am not sure how Supp. Fig. 5 supports this statement. Is this the right figure reference? Should it be Supp. Fig. 4 instead?
4. Line 881: "representing on line" should be "representing one line".

OPTIONAL

Tony Harris' lab showed that the Arf-GEF Steppke antagonizes myosin and facilitates cell deformation at the leading edge of the embryonic epidermis during Drosophila dorsal closure (West et al., Curr Biol, 2017). Does Steppke localize to junctions in lateral but not central mesoderm cells? Does the pattern of Steppke localization in the mesoderm change with manipulations to the contractility of central cells?

Significance

This is an interesting study, and one that makes uses of beautiful tools, including quantitative microscopy and image analysis, mathematical modeling and optogenetic manipulations. The prediction that embryonic cells display non-linear stress-strain responses is exciting, as linearity has been the predominant assumption so far. However, I find that model predictions are not well supported by the data, and that alternative interpretations of some results are possible. Additionally, the paper lacks insight into the molecular mechanisms that facilitate stretching (although that could be the subject of a follow-up study).

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this study, the authors explore potential mechanisms for why some cell constrict while other cells expand, despite similar intrinsic genetic programs, during Drosophila ventral furrow formation at the onset of gastrulation. The authors combine quantitative analyses of cell shapes and myosin levels from multiphoton confocal and Multi-View SPIM imaging, optogenetic and laser perturbation experiments, and mechanical models to argue that nonlinear mechanical interactions between cells are required to explain the cell behaviors. Based on microscopic models of the actomyosin cytoskeleton in the tissue the authors argue that the required nonlinear mechanical behavior is consistent with actomyosin network reorganization.

Major comments:

• Although the area of investigation is exciting and the results are interesting, unfortunately the quality of the results and comparison between experiment and modeling in the current version of the manuscript are not convincing. Although it is not clearly explained in the manuscript, the experimental results on cell shapes, myosin intensity, laser manipulation, optogenetic perturbations appear to be from a single embryo or small number of embryos for each experiment (Figures 1, 3, 4). The authors state that the cell stretching pattern "was best recapitulated by a superelastic response", but did not provide direct quantitative comparisons of the different mechanical models to the experimental data to clearly demonstrate this. Moreover, the local optogenetic myosin recruitment experiments in Figure 4 do not provide sufficient information on optogenetic tool recruitment, myosin localization, or cell behaviors to justify the claim that the central cells are not activated by the optogenetic perturbation and are only responding to the forces from neighboring cells.
• The authors should provide direct quantitative comparisons of the models and experiments to clearly demonstrate their claims that the superelastic model is better than the linear model or other nonlinear models.
• The authors should do additional experiments and/or provide more details for the existing experiments (to include several embryos per condition) on myosin quantification, photo-manipulation, and optogenetics experiments. Additional controls would like be necessary for claims resulting from the optogenetics experiments in Figure 4.
• The additional time and resources required to address these concerns would depend on the experimental details, N values, and statistics in the current studies, which unfortunately were not described in the current manuscript.
• Methods descriptions for reproducibility are generally adequate, with the exception of N values and statistics - see above.
• Are the experiments adequately replicated and statistical analysis adequate? No, see above.

Minor comments:

1) Scale bars for images are missing throughout.

2) Number of embryos and cells analyzed missing throughout text and figure legends.

3) Units are missing for many quantities in figures and tables throughout.

4) Many figure references in the main text are incorrect, pointing either to the wrong figure or wrong figure panel.

5) Line 728. What time point was used for myosin concentrations used in the model? How might myosin dynamics influence these findings?

6) The authors show a few examples of myosin pulsing in lateral cells and then conclude that myosin pulsing is not qualitatively different from central cells (lines 135-136). The author should quantify the number of pulsing lateral cells as well as period and amplitude of pulsing, or discuss relevant results from prior studies in more detail to justify this conclusion.

7) Lines 145-150. The authors very briefly describe the results of the linear-stress strain response and conclude this did not yield outputs corresponding to in vivo data and leave this largely to the supplementary figures. This is a key point in the paper and deserves much more discussion and space in the main text. As mentioned in main comments above, a quantitative comparison of the different mechanical models to show that the superelastic model better describes the observations should be included (potentially as an inset to Fig 2D showing a quantitative measure of the quality of model fit to the data).

8) Lines 162-163. Provide more rationale for why strain-softening would most likely manifest as permanent or reversible cytoskeletal reorganization.

9) Lines 187-188. "This shows that forces acting on each cell from its neighbors have an important role in determining the cell's behavior." This seems somewhat obvious; perhaps a bit more explanation would help the reader to understand the importance of these results.

10) Lines 196-198. How were the concentrations and lengths of F-actin chosen? How were the concentration and properties of linkers chosen? How sensitive are the results to these details of the cytoskeletal composition?

11) Lines 238-244. It would be helpful to include some additional quantification that clearly shows the reader the differences in cell behaviors in control and perturbed tissue. For the optogenetics experiment, it would be important to show quantification that the lateral cells are not being directly perturbed during photoactivation of neighboring cells (e.g. due to light leakage). In both perturbations, it would be helpful to quantify how many cells in rows 7 and 8 constricted and by how much did they constrict? How reproducible were these effects?

12) Lines 245-252. A key assumption in interpreting this experiment seems to be that the central cells are not directly perturbed by the optogenetic activation. Additional quantifications of RhoGEF2-CRY2 and/or myosin should be shown to support this. It would be helpful to include some additional quantification that clearly shows the reader the differences in cell behaviors in control and experimental regions. How reproducible were these effects?

13) A section on statistics is missing from the methods section.

14) Line 615. Ensure that Eq. 1 is dimensionally consistent; crucially, what units are used for 'M'? If the model is non-dimensionalized, provide the reference scales.

15) Line 675: The investigated stress-strain relationships are presented in Table S1. What are the definitions of xpl and xsh?

16) Line 678: Parameter values for the stress-strain relationships are given in Table S2. Can you provide more information on how these values were selected and their units? How sensitive are the results to changes in these values? Provide references when possible.

17) Line 697. Please comment on why the embryo appears skewed to the right.

18) Line 712. A color-bar corresponding to this color-code is missing in the figure.

19) Lines 715-717. It seems panels E and E' are swapped in the legend.

20) Line 724 (Fig 2). It is difficult to read anything in panel K inset or Panel L inset.

21) Line 728. What does "embryo 1" refer to?

22) Line 732. A quantitative measure of the quality of the fits of the models to the experimental data should be included.

23) Line 739. What exactly does "Embryo 2" refer to?

24) Line 779. Why is a z-plane of 15 microns below surface chosen?

25) Line 797. Why is a z-plane of 25 microns below the surface chosen?

26) Line 900. Panel G in Supp Fig 5 is not described in figure description.

• Are prior studies referenced appropriately? Yes.
• Are the text and figures clear and accurate? No (see details listed above).
• It would be very helpful to the reader to show direct quantitative comparison of the different mechanical models with the experimental observations to show how much better the nonlinear model is compared to the linear model. An extended explanation of experiments and experimental results within the main text would improve the manuscript.

Significance

The key advance in this work is in identifying a potential role of nonlinear mechanical properties in contributing to distinct cell behaviors within a tissue during development in vivo. This contributes to a growing body of work highlighting the importance of cell and tissue mechanical properties in regulating cell behaviors during the formation of tissue structure.

This work adds to a growing body of work connecting actomyosin contractility in cells to tissue-scale behavior during development. This work provides a unique mechanical modeling perspective to the study of apical constriction during Drosophila ventral furrow invagination, highlighting a potential role for superelastic cell mechanical behaviors during morphogenesis in vivo.

The finding would be of interest to researchers working in the areas of morphogenesis, mechanobiology, the cytoskeleton, and active matter.

This reviewer's expertise is in experimental studies of the cytoskeleton and cell mechanics during morphogenesis.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Bhide and colleagues present an insightful study of how cellular mechanics influences differential cell behaviour during morphogenesis despite apparent genetic homogeneity of the cellular ensembles. They dissect the extensively studied system of mesoderm invagination in Drosophila, focussing on the differences in cell behaviours between the cells in the middle of the infolding tissue and on the periphery that, as far as we know, share a common gene expression profile. They describe sub-cellular dynamics of major effector of apical constriction morphogenesis, the myosin motor distribution, in the invaginating cells and conclude that differences in myosin levels alone cannot account for the observed differences in cell behaviours. In order to understand the cell behaviour inhomogeneity, they turn to biophysical simulation and in an impressively exhaustive manner substantiate the idea that non-linear effects are required for explaining the phenomenon. This theoretical treatment fits well with the notion that the genetic identity of the cells but rather cell-cell mechanical coupling determine the differences in invaginating cell's behaviours. Additionally, the modelling is consistent with the myosin asymmetry and dynamics in the cells whose behaviours is being contrasted. Complementary, and beautifully executed filament-based modelling of microscopic actomyosin contractility further corroborates this view. Finally, the proposed model of non-linear actomyosin contractility dynamics governing the differential cell behaviour across genetically homogenous cellular field, is challenged by two complementary laser ablation and optogenetic experimental approaches. Overall, the results represent convincing evidence that points the tissue mechanics field of Drosophila mesoderm into an interesting new direction and has general implications for the understanding of the interplay between genetic regulation and emergent behaviours of cells operating in mechanically complex multicellular embryonic context. The study is meticulously executed, highly quantitative and combines effectively experiment and theory. I have only minor comments that concern in particular the presentation of the results.

The paper is very dense and the text does not complement well the results presented in the main figures. Many panels in the Figures are not referred to explicitly. Figure elements are referenced out of order both within and across Figures. Sometimes, particularly, in the last two Figures (3 and 4) the reader is left alone to figure out what the data show (with the appropriately terse legends and without the clear narrative in the text, it is an uphill battle for non-specialists). Some key results are hidden in the sea of elements within the Figure 2 that contains the most important, relevant and impressive data.

We have split this figure in two, moved some of the results from Suppl. Fig. 5 into one of its parts and included new calculations and data. We have also extended the description of these results in the main text and in the figure legends.

As an example, on line the authors point to panel 2F to demonstrate the asymmetry of myosin distribution in some cells. To the best of my understanding, this phenomenon is actually shown in Fig 2E which is curiously not referenced at all.

We have corrected the references to the panels

Similarly, Figure 2K and L provide crucial data substantiating much of the conclusions of the paper. It requires a major effort to understand what the graphs mean. The following simulation results are quite impressive and would deserve a separate Figure which could provide more space for explaining what the parameter maps actually show. What is for instance plotted on the Y axis as steepness?

We have added the following explanation: “The ‘width’ of the profile is the number of cells with maximum value; the ‘steepness’ is the slope between minimal and maximal values (equation 2 in materials and methods).”

Secondly, I find the overall narrative of the manuscript needing some reorganisation. The main question is set-up extremely well, however in the middle of the manuscript the focus on the connection between cell behaviours and genetic programs is lost. New conclusions on force transmission between cells emerge, however they are not obviously connected with the question posed from the onset and addressed in the discussion section.

To us, the section on force transmission seemed like an important component of the issue of intrinsic versus extrinsically determined cell behaviours. We had seen that the intrinsic programme of the cells, as reflected in their myosin levels, might not be sufficient to explain the difference between stretching and constricting. If their behaviour is not intrinsically determined, then there must be something acting from the outside, and we are looking here at what that might be, i.e. we need to find out how the potential constriction is influenced. The first model tests under which conditions differential contractility leads to different ‘cell’ behaviours. This in turn leads directly to the question of the forces the cells in the epithelium exert on each other.

My impression is that the authors are conservative in their reasoning, however it does compromise the overall message of the story that should ideally focus on one subject. I find the combined evidence presented sufficiently supportive of the model that is beautifully and eloquently presented in the concluding sentence of the paper:

"This mechanism, which we propose corresponds to the non-linear behaviour predicted by the models, would apply both to central and to lateral cells, with a catastrophic 'flip' being stochastic and rare in central cells, but reproducible in lateral cells because of the temporal and spatial gradient in which contractions occur."

This may not turn out to be the entire story or even entirely correct, but it is certainly and exciting way of thinking about the problem. I wish that the manuscript would stay more on this subject throughout and provide intermediate conclusions supporting this model as the story develops.

Few more minor comments:

We have corrected all of the typos, mistakes and omissions and adapted the text, as mentioned below.

Line 36 - typo > Line 97 - starting bracket missing > Line 126 - data on intensity are presented here. There is also a panel on concentration (Fig 1H). Where is this discussed?

An explanation (definition) has been added to the main text.

Line 132 - panel 2G - disruptive out of sequence reference to a future figure > Line 135 - with this regard - please spell out this important conclusion

We have expanded this part, basically introducing the conclusion more clearly (we hope).

Line 183 - typo > Line 210 - insects do not have intermediate filaments

We have added ‘mammalian‘ to the reported experiment in the text, to make it clear that this does not refer to Drosophila cells

Line 238 - please provide a hint of how such global ablations are performed > We have added this – both explicitly, and the relevant references.

Line 240 - walk us through the Figure, it is too complex to figure it out alone > We have added a more extensive explanation both in the text and in the new figure legend.

Line 245 - why is the clear hypothesis mentioned above (point 2) rephrased? > Line 273 - vague statement

We have changed the text in response to these useful pointers.

**Significance:

The results represent convincing evidence that points the tissue mechanics field of Drosophila mesoderm into an interesting new direction and has general implications for the understanding of the interplay between genetic regulation and emergent behaviours of cells operating in mechanically complex multicellular embryonic context.

Reviewer #2

Bhide and colleagues explore the mechanisms of cell expansion in epithelial morphogenesis. During the invagination of the Drosophila mesoderm, cells in the center of the prospective mesoderm constrict under the action of actomyosin pulses, while lateral cells elongate towards the center of the mesodermal placode to accommodate the reduction in apical surface of the central cells. Central and lateral cells display strong similarities in terms of gene expression. How are thus this different behaviors (contraction and expansion) accomplished? The authors found that both central and lateral cells assemble actomyosin networks, although lateral cells do it with a certain delay. Mathematical models of cell constriction across the mesoderm using different strain-stress responses showed that strain-induced cell softening was necessary recapitulate the patterns of constriction and expansion observed in vivo. Furthermore, modelling predicts that cells can stretch until the actin networks yield and break. Laser ablation and optogenetic reduction of contractility in central cells results in a reduction in the apical surface area of lateral cells. An optogenetic increase in contractility in lateral cells caused an increase in apical area in central cells. Together, these data suggest that mechanical cues can override and contribute to sculpting genetically defined morphogenetic domains.

I propose to address the following points before further considering the manuscript:

Major

1. Figure 3: following laser ablation of central cells, lateral cells reduce their apical surface. How do the authors know that this reduction in lateral cell apical surface area is an active process, driven by actomyosin-based contraction, rather than a passive response to the expansion of the wound induced by laser ablation?

   A similar argument could explain the constriction of lateral cells after optogenetic inhibition of actomyosin networks: the central cells relax, expand and compress the lateral cells.

With regard to the comparison to wounds, it is important to note that the epithelium is not actually wounded by either ablation method. Thus, while the treatments ablate the actyomyosin meshwork, they do not ablate or kill the cells. Perhaps the term is an unfortunate choice, since it is more commonly used in developmental biology for killing cells. However, here the cells remain intact and when the optogenetic or laser treatment is released the cells resume their physiological activities.

We have added a note in the text and now refer to ‘laser microdissection’, a term of art in the field, for more clarity.

Regarding the more important question of what is the active process, expansion of the central cells or constriction of the lateral cells, a contribution from expanding central cells is of course in theory not impossible.

However, for this scenario to work, in the absence of pulling from the lateral cells, there would have to be a force that is generated in the central cells, in this case a pushing force that would expand the cells and act on the lateral cells. We have shown in our previous work that if the actomyosin is dissected in dorsal cells, which are not surrounded by potentially contractile cells, the cells do not expand (Rauzi et al, 2017). This shows that ‘relaxing’ by itself does not have ‘expansion’ as a consequence. One would therefore have to consider how such a pushing force could arise in these cells. We can think of only two possibilities: hydrostatic pressure or an active force from the subcellular molecular machinery.

Considering hydrostatic pressure, if the apical actomyosin that is ablated was responsible for maintaining such a pressure inside the cell (a reasonable assumption), then releasing the actomyosin would allow the cell volume to push against the neighbouring cell. However, such a recoil would occur on a very short time scale (seconds), whereas we see the contraction of the lateral cells continuing over extended periods (minutes).

Alternatively, expansive forces could be generated by the cytoskeleton. Cytoskeletal pushing forces can come from microtubules (classical example: mitotic spindle; epithelial morphogenesis: work from T. Harris and B. Baum labs: PMID 18508861 and 20647372), or from continuous creation of new cross-linked or branching actin networks pushing against plasma membranes, as in the leading edge of crawling cells. But the microtubules in the blastoderm cells are not oriented in such a way they could provide a force in the correct dimension in these cells (the majority is oriented along the apical-basal axis). In addition, the connection between MT and the plasma membrane depends on the cortical actin meshwork (involving, for example, the actin-binding proteins P120-Catenin or patronin/Shot; Roeper lab, PMID 24914560, StJohnston Lab, PMID: 27404359) but the connection of actin with the plasma membrane has been severed in the optogenetically manipulated cells.

By contrast, we show that normal lateral mesodermal cells possess a contractile actin network. So the only sustained force generated in the system at this point is the contractile force in lateral cells (which is normally counteracted by the stronger contractile force from central cells).

Thus, we conclude that the expansion of central cells is a passive response to a contractile force from lateral cells, not an active process and conversely, the constriction of lateral cells is an active autonomous process.

To demonstrate active responses of the lateral cells upon laser ablation and optogenetic manipulations of central cells, at the very least the authors should show the distribution of myosin in the lateral cells that constrict and demonstrate the assembly of contractile networks.

We have now included the requested data for the experiments with laser ablations. Suppl. Fig. 8 and Suppl. video 3 show the myosin that accumulates in lateral cells. It would be nice also to be able to show this for the optogenetic experiments. However, despite trying hard, we have not succeeded in generating healthy embryos that carry the entire set of transgenes that are necessary to carry out the optogenetic experiments and at the same time visualize myosin (see also response to referee 2, point 3).

1. Modelling suggests that actin networks yield and break in lateral cells. Does this occur in vivo?

We postulate that the skewed and inhomogeneous distribution of myosin and the large myosin-free areas in stretched cells (lines 170 – 172 in the original text) are indications of a yielding meshwork, or at least of uneven force distribution in the network that leads to ineffective contraction or even release – i.e. functionally correspond to yielding. We have made this more explicit now.

We have also added an additional panel quantifying more clearly the proportion of low- myosin areas in lateral cells (now Fig. 3H).

Work from the Lecuit lab has recently shown beautifully that it is the connectivity of the myosin mesh rather than the underlying actin meshwork that affects apical forces in epithelial cells (PMID: 32483386), and our own findings are entirely consistent with that.

1. Lines 166-175: The authors propose that constriction of a cell affects the localization of myosin in its neighbors. However, this is not directly measured. The authors should quantify the relative myosin offset in the cells around constricting cells, and show that that offset is greater (and oriented towards the constricting cell) than in cells around expanding cells. There should be a correlation between the relative size change of a cell and the myosin offset (not just concentration) in their neighbours. We now provide measurements of the rate of cell area change against the offset of surrounding myosin (the distance of myosin from a cellular border). We see that surrounding myosin is closer to the border of constricting cells and tends to be further away from the borders of expanding cells.

We have added these data to the new Fig. 3I.

In addition, does optogenetic activation of constriction in lateral cells affect the offset of myosin networks in central cells?

This is technically challenging. For such an experiment we would need an embryo to express membrane and myosin markers in addition to the two optogenetic constructs and the GAL4 driver. We tried multiple times to generate such a cross, but obtained either no embryos or, at best, deformed embryos. We also tried to use the MCP-MS2 system in parallel to CRY2-RhoGEF2 but the crosses had the same problem. This sensitivity to additional genetic load was also observed in the DeRenzis lab, who generated these strains and tested and used them extensively.

1. Fig. 2E-F: the authors argue that the mean myosin concentration in lateral cells at certain times is equivalent to that of central cells earlier in the invagination process. However, the fraction of apical surface area covered by myosin network is consistently lower for lateral cells (and also for central cells that remain unconstricted!). Have the authors considered this fact, and if not, why? Wouldn't this explain, at least in part, why some cells constrict and others do not, if medial myosin networks drive the disassembly of the apical surface?

We believe in fact that this is precisely part of the picture and it was what we had meant to propose, but the text was perhaps indeed just to condensed. Thus, we had stated in line of the original document:

“While the asymmetry is visible in all cell rows, there are larger areas without myosin and the distance of displacement is greater in lateral cells (Fig. 2G-J)”,

and in the discussion (line 277 – 285):

“Despite the homogeneous actin meshwork in stretching cells, the areas that are free of active myosin occupy a large proportion of the apical surface – similar to ectodermal or amnioserosa cells in which the connection of pulsatile foci to the underlying actin meshwork is lost. ... Dilution of cortical myosin may compromise a cell’s ability to make sufficient physical connections, in particular along the dorso-ventral axis, so that even if sufficient force is generated, it cannot shorten the cell in the long dimension. In other words, even though the cells have enough myosin to create force, the system is not properly engaged and its force is not transmitted to the cell boundary.”

However, we didn’t state this with sufficient clarity in the results section and have added an extra sentence to this effect.

If myosin activity were increased in laterals cells once central cells begin constricting, would that lead to an increased fraction of lateral cell surfaces covered by actomyosin networks and to reduced lateral cell elongation?

This is a really nice experiment, and we have indeed tried to induce activation at later time points, but unfortunately this did not yield unambiguous results. If we did the manipulation after the central cells had clearly constricted, then activating lateral cells did not lead to their contraction. However, since this is a negative result and we have no independent criterion for knowing how 'strong' the induced contraction was (as explained above, we are unfortunately not able to visualize the myosin in these experiments), and why it might not have been sufficient to overcome the pull from central cells.

In this context it is worth remembering that in mutants in which myosin is overactivated as a result of defective upstream signalling, lateral cells stretch less or not at all. See PMID: 24026125 for gprk2 mutants and our own results for active Rho1:

{{images cannot be displayed}}

Figure: Confocal Z-section of embryos expressing sqh::GFP (myosin; green) and GAP43::mCherry (membrane; magenta) imaged ventrally. A constitutively active form of Rho1 is ectopically expressed using a maternal Gal4 driver, inducing activation of myosin in more lateral cells. White dots mark the mesectoderm determined by backtracing after ventral furrow invagination. Yellow arrows in B are constricted cells in row 7/8.

Minor

1. Image panels are missing scale bars in many figures. > 2. Fig. 1C'-D': The authors should include a color bar to provide some indication of the scale of the apical areas measured. Same comment for other figures in which apical area is color-coded.

We have added the missing elements

1. Supp. Fig. 2E-F, G-H and Supp. Fig. 6: what is the difference between myosin intensity and myosin concentration? Junctional vs medial localization? Or summed vs mean pixel value? Please be specific, the difference between intensity and concentration is not clear.

In the cases where we talk about myosin ‘amount’ we have now exchanged the term ‘intensity’, i.e the physical term for the amount of light, for ‘amount’ (i.e. that for which we use the light intensity as a proxy) and have explained in the main text how we define total apical myosin amount and apical myosin concentration (amount over area). However, in the cases where we are describing the actual image analysis, as in Suppl. Fig. 3, we use ‘intensity’ as the term of art that is used for the methods employed here. Similarly, the terms ‘sum intensity’ and ‘mean intensity’ are terms used for image in analysis in Fiji.

The definitions of “junctional” and “medial” actin were introduced by the Lecuit lab (PMID: 21068726), and we have included the appropriate reference.

1. Line 118: Supp. Fig. 2 does not have panels I and K. > 5. Line 223: the authors reference data at sec, but Supp. Fig. 6 does not show any images at that time point. They should be added or a different time point indicated.

These errors have been corrected.

Typos

1. Abstract: "[in a supracellular context" should be "in a supracellular context". > 2. Line 145: should this be a reference to Supp. Fig. 5 instead of Supp. Fig. 4? > 3. Line 166: I am not sure how Supp. Fig. 5 supports this statement. Is this the right figure reference? Should it be Supp. Fig. 4 instead? > 4. Line 881: "representing on line" should be "representing one line".

These errors have been corrected.

Optional

Tony Harris' lab showed that the Arf-GEF Steppke antagonizes myosin and facilitates cell deformation at the leading edge of the embryonic epidermis during Drosophila dorsal closure (West et al., Curr Biol, 2017). Does Steppke localize to junctions in lateral but not central mesoderm cells? Does the pattern of Steppke localization in the mesoderm change with manipulations to the contractility of central cells?

This is certainly interesting, and we have ordered the protein trap, UAS constructs and RNAi lines. However, these will be long-term and time-consuming experiments.

Significance:

This is an interesting study, and one that makes uses of beautiful tools, including quantitative microscopy and image analysis, mathematical modeling and optogenetic manipulations. The prediction that embryonic cells display non-linear stress-strain responses is exciting, as linearity has been the predominant assumption so far. However, I find that model predictions are not well supported by the data, and that alternative interpretations of some results are possible. Additionally, the paper lacks insight into the molecular mechanisms that facilitate stretching (although that could be the subject of a follow-up study).

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary:

In this study, the authors explore potential mechanisms for why some cell constrict while other cells expand, despite similar intrinsic genetic programs, during Drosophila ventral furrow formation at the onset of gastrulation. The authors combine quantitative analyses of cell shapes and myosin levels from multiphoton confocal and Multi-View SPIM imaging, optogenetic and laser perturbation experiments, and mechanical models to argue that nonlinear mechanical interactions between cells are required to explain the cell behaviors. Based on microscopic models of the actomyosin cytoskeleton in the tissue the authors argue that the required nonlinear mechanical behavior is consistent with actomyosin network reorganization.

Major comments:

• Although the area of investigation is exciting and the results are interesting, unfortunately the quality of the results and comparison between experiment and modeling in the current version of the manuscript are not convincing. Although it is not clearly explained in the manuscript, the experimental results on cell shapes, myosin intensity, laser manipulation, optogenetic perturbations appear to be from a single embryo or small number of embryos for each experiment (Figures 1, 3, 4).

We had analysed a much larger number of embryos, but only included those for presentation that provided the most extensive data. It is extremely difficult to obtain absolutely ‘perfect’ embryos at high resolution for full quantification over long periods. ‘Perfect’ means that the embryos are mounted in such a way that they are imaged from an angle of 45 degrees off the dorso-ventral axis, so that initially mesodermal rows 3 to 7 are seen, and then, as furrow formation progresses, the more lateral rows move through the field of vision. It is difficult to mount in this perfect manner for two reasons: the shape of the embryo means that the embryo does not ‘like’ to be balanced in this position, but instead prefers to fall back on its side. Secondly, the embryo has to be mounted at a time point before visible differentiation along the D-V axis, so no visual cues exist to get the positioning right. This means that many of our recordings lack either the more ventral or the lateral cell rows. While the findings for these more restricted observations are fully consistent with our reports, they cannot be quantified with a full comparison across all cell rows over the entire imaging period. Nevertheless, we have processed and analysed further examples which we have now included in Suppl. Fig. 2 and Suppl. Fig. 8.

The authors state that the cell stretching pattern "was best recapitulated by a superelastic response", but did not provide direct quantitative comparisons of the different mechanical models to the experimental data to clearly demonstrate this.

Data that illustrate this were shown in Suppl. Fig 5 – but, admittedly, were not well explained, or rather, not at all. We have now added better explanations, expanded the figure, included new analyses, and now present some of these data in the new Fig. 2. Briefly, the figure shows that superelastic and elastoplastic responses are the only curves that successfully reproduce the pattern of stretching lateral cells (last 3 cells stretching with the inner cell stretching most and the last cell stretching least) while at the same time matching the ratio between the cell sizes of the most stretching cells to the least stretching cell.

The top row of the parameter scans in Suppl. Fig. 5 (now Fig. 2) shows how many cells stretch for each combination of myosin curve steepness (y-axis) and width (x-axis) with shades of blue indicating the number of cells, and the red outline in the field where 3 cells stretch outlining those conditions where the inner cell stretches most. The bottom row shows the resulting size ratios of largest to smallest cell. High ratios in the region outlined in red in the top row are only reached for the superelastic and elastoplastic responses, with the elastomeric tending in the right direction.

We have now also quantified a goodness-of-fit (root mean squared error, RMSE) measurement between our experimental data and the simulated data of all our models. This is shown now in the new Fig. 2.[1]

We also note that only the parameter maps of the superelastic and elastoplastic models (Fig. 2J,K) resemble the equivalent parameter maps of the microscopic model (Fig. 3Q).

Moreover, the local optogenetic myosin recruitment experiments in Figure 4 do not provide sufficient information on optogenetic tool recruitment,

We have included images that illustrate the optogenetic construct in the illuminated cells, but not in the central cells in Suppl. Fig. 8. It is impossible to show the construct in the ‘dark’ cells, because illuminating them would activate the construct.

myosin localization,

As explained above, this is unfortunately technically not feasible. The best we can do is refer to the description of the construct by Izquierdo et al. (PMID: 29915285), which shows the accuracy of the tool and the highly specific membrane recruitment of myosin.

or cell behaviors

We have added quantitative comparisons between the experimental and control areas. to justify the claim that the central cells are not activated by the optogenetic perturbation and are only responding to the forces from neighboring cells.

• The authors should provide direct quantitative comparisons of the models and experiments to clearly demonstrate their claims that the superelastic model is better than the linear model or other nonlinear models.

See response above.

• The authors should do additional experiments and/or provide more details for the existing experiments (to include several embryos per condition) on myosin quantification, photo-manipulation, and optogenetics experiments.

We have provided data for more embryos for all cases.

Additional controls would like be necessary for claims resulting from the optogenetics experiments in Figure 4.

This has been addressed above – we have provided additional data and controls.

• The additional time and resources required to address these concerns would depend on the experimental details, N values, and statistics in the current studies, which unfortunately were not described in the current manuscript.

We have been able to add substantial additional data and have added the requested numbers. For many of the experiments each recording can be very time consuming and for the reasons explained in this response, it is not always easy to obtain precisely the desired recording from the desired imaging angle with the manipulations having been done precisely in the desired position. The numbers of embryos are therefore not high, but multiple shorter recordings provide a body of results that support the findings, but are not easily comparable statistically.

• Methods descriptions for reproducibility are generally adequate, with the exception of N values and statistics

See above.

• Are the experiments adequately replicated and statistical analysis adequate?

No, see above.

Minor comments:

1) Scale bars for images are missing throughout.

We have added these

2) Number of embryos and cells analyzed missing throughout text and figure legends. We have added additional embryos for all conditions and have included the numbers of cells analysed for all quantifications (except in cases where each data point represents a cell).

3) Units are missing for many quantities in figures and tables throughout.

We have added these

4) Many figure references in the main text are incorrect, pointing either to the wrong figure or wrong figure panel.

These have been corrected

5) Line 728. What time point was used for myosin concentrations used in the model?

We have added this information to the figure legend.

How might myosin dynamics influence these findings?

As regards the subcellular dynamics of myosin, these are included in the microscopic model (see ref Belmonte et al.;PMID: 28954810). Preliminary results showed that small changes in myosin stall force and unloaded myosin speed have little effect in our general results. This is now shown in a new supplemental figure (Suppl. Fig. 6). However, if the referee is referring to the dynamics of myosin accumulation over time, this is an interesting question.

We had begun to explore this topic, but then realized for the linear stress-strain model that it is in fact expected that myosin accumulation would ultimately not affect the outcome. This is because in a linear model the final state of the system is determined by the final shape of the governing myosin profile regardless of the time evolution of the profile, and our simulations confirm this. A systematic analysis for all other stress- strain curves with temporal changes in myosin profiles (where a dependency on the profile temporal evolution is expected) is very time-consuming and will be interesting to pursue in future.

The main conclusion here that linear models do not recapitulate the observed data as well as the non-linear ones stands regardless of how the temporal dynamics of myosin accumulation may affect the non-linear systems.

6) The authors show a few examples of myosin pulsing in lateral cells and then conclude that myosin pulsing is not qualitatively different from central cells (lines 135- 136). The author should quantify the number of pulsing lateral cells as well as period and amplitude of pulsing, or discuss relevant results from prior studies in more detail to justify this conclusion.

By ‘not qualitatively different’ we had meant only ‘in the sense that they are capable of generating contractile forces’, and we have made that more explicit in the text now. The quantitative differences have already been analysed and reported by the Martin lab (https://doi.org/10.1101/2020.04.15.043893; the pulses are slower and less persistent), and our point was that in spite of these known differences, the pulses are able to mediate constriction.

7) Lines 145-150. The authors very briefly describe the results of the linear-stress strain response and conclude this did not yield outputs corresponding to in vivo data and leave this largely to the supplementary figures. This is a key point in the paper and deserves much more discussion and space in the main text.

We have included a more extensive description and interpretation of the results in the main text, as detailed in several responses above

As mentioned in main comments above, a quantitative comparison of the different mechanical models to show that the superelastic model better describes the observations should be included (potentially as an inset to Fig 2D showing a quantitative measure of the quality of model fit to the data).

These comparisons have now been expanded and explained more extensively and moved to the main Figures.

8) Lines 162-163. Provide more rationale for why strain-softening would most likely manifest as permanent or reversible cytoskeletal reorganization.

The only component of the cell that can likely mediate this physical property and also respond at the observed time scales is the cytoskeleton. In these cells it is the main mechanical determinant. Other components that could in principle contribute to the nonlinearity of stress-strain response might be the viscosity of the cytosol, or the plasma membrane. However, stress responses of fluids to shear are usually in the direction of increasing stiffness, and rarely, if ever, with shear thinning. The same is mostly true for colloidal solutions. Therefore it is more likely that the stress-strain relationships at the apical surface of the cells are dominated by the dynamics of the actin cytoskeleton given that even the shape of the plasma membrane is in general determined by the cytoskeleton. We have added a note to this effect in the text.

9) Lines 187-188. "This shows that forces acting on each cell from its neighbors have an important role in determining the cell's behavior." This seems somewhat obvious; perhaps a bit more explanation would help the reader to understand the importance of these results.

We have expanded the explanations of these findings and added a sentence to relate them to the main model of the paper

10) Lines 196-198. How were the concentrations and lengths of F-actin chosen? How were the concentration and properties of linkers chosen?

The parameters were chosen on the basis of our earlier studies on simulated contractile meshworks and the theory underlying their behaviour. We had reported the conditions under which such meshes are able to contract, and also shown that the underlying theory correctly predicts behaviour of experimental meshworks (for those few conditions for which they have been reported).

Unfortunately, there are practically no measurements for the length of F-actin filaments in vivo and estimates vary widely. Reliable data on the density of the cortical network are equally sparse.

Based on our own previous work we chose concentrations of cross-linkers, myosin motors and transmembrane connectors that are able to ensure optimal contraction and force. Our in vivo measurements reported here show that the amounts of F-actin do not vary significantly across the mesoderm, so we used the same concentration of actin, crosslinkers and membrane connectors in all cells of the model, varying only myosin concentration. Taking into account the cell diameter of the mesodermal cells (~7um) and to ensure that the meshwork is sufficiently cross-connected (dense) to generate contraction and transmit forces between cells we used a model where each cell contains F-actin filaments of 1.5 um.

We have expanded our supplemental material to make these points clearer.

How sensitive are the results to these details of the cytoskeletal composition?

We varied both the amounts of cytoskeletal components and the parameters controlling their dynamics (such as myosin stall force and viscosity) and found little impact on model predictions. These data are now presented in Suppl Fig. 6.

11) Lines 238-244. It would be helpful to include some additional quantification that clearly shows the reader the differences in cell behaviors in control and perturbed tissue.

We have added quantitative comparisons of the cells in the perturbed region with cells in an equivalent control region, together with evaluations of two additional embryos.

For the optogenetics experiment, it would be important to show quantification that the lateral cells are not being directly perturbed during photoactivation of neighboring cells (e.g. due to light leakage).

We have included this information, as described above.

In both perturbations, it would be helpful to quantify how many cells in rows 7 and 8 constricted and by how much did they constrict? How reproducible were these effects?

The perturbation experiments were those where it was most difficult to obtain a large number of identical-looking embryos that would allow broad statistics to be applied. For this to work, we would have to have embryos that were identically mounted and illuminated in the identical area of precisely rows 1 to 6 on each side of the midline – at a resolution of one cell row of 6.2 um width. And all this blind, because at the start of the manipulation there are no visual cues for orientation. Morphology gives no cues at this stage. The MS2-MCP-GFP works for laser ablations, but cannot be used for the optogenetics, because the embryo must not be exposed to blue light. This means we cannot predetermine precisely which rows we target.

We have however added data and quantifications for the control and two further laser- manipulated embryos, which are now shown in suppl. Fig. 8. It is evident from both that our perturbations were slightly asymmetric and included the outer rows on only one side and on that side several cells that would normally have stretched are now strongly constricted. While by no means true for all lateral cells, this is a case of one black swan disproving the hypothesis that all swans are white: any constricting cell within two cell diameters of the mesectoderm, i.e. ones that would normally stretch proves that lateral cells do have the capacity to constrict.

12) Lines 245-252. A key assumption in interpreting this experiment seems to be that the central cells are not directly perturbed by the optogenetic activation. Additional quantifications of RhoGEF2-CRY2 and/or myosin should be shown to support this.

We have included an image of the optogenetically activated construct in this experiment in Fig. 5, but we cannot show its behaviour in the non-activated part because if we illuminated it, it would be activated. We were unable to create the embryos necessary to document the behaviour of myosin.

It would be helpful to include some additional quantification that clearly shows the reader the differences in cell behaviors in control and experimental regions. How reproducible were these effects?

We now provide the results from two additional embryos in Suppl. Fig. 8, and include quantitative comparisons between the control and experimental regions for these and for the embryos that are currently shown in Fig. 5 E.

13) A section on statistics is missing from the methods section.

We have added descriptions of the quantifications and statistics.

14) Line 615. Ensure that Eq. 1 is dimensionally consistent; crucially, what units are used for 'M'? If the model is non-dimensionalized, provide the reference scales.

Apart from the initial distance between membrane positions (set to 6.2 um) all other units in our visco-elastic model are arbitrary. In order to make this clearer, instead of using the term “viscosity” in equation 1, we now call it a “damping constant”.

15) Line 675: The investigated stress-strain relationships are presented in Table S1. What are the definitions of xpl and xsh?

We have included these definitions in materials and methods:

All stress-strain curves are linear for extensive strains (∆𝑥) lower than the proportionality limit (𝑥!"), with some curves (elastoplastic and superelastic) undergoing a strain-softening to strain-hardening change after a given strain-hardening limit (𝑥#$).

16) Line 678: Parameter values for the stress-strain relationships are given in Table S2. Can you provide more information on how these values were selected and their units? How sensitive are the results to changes in these values? Provide references when possible.

The values for xpl and xsh were chosen to be within the range of the observed lengths of stretching cells, with xpl < xsh. Changing the values of each parameter listed in Table S2 does change the results quantitatively, but over the ranges we tested them, never to the point of making the linear or the other non-linear models reproduce the target pattern of stretching.

We have stated this in the materials and methods section.

17) Line 697. Please comment on why the embryo appears skewed to the right. Embryos are not always ‘perfect’, unfortunately. In addition, they can get slightly squashed during mounting and imaging. In spite of its imperfection, we showed this particular one, because we had imaging data for a long period without drift or other interference, and with good contrast at great depth.

18) Line 712. A color-bar corresponding to this color-code is missing in the figure.

This has been corrected.

19) Lines 715-717. It seems panels E and E' are swapped in the legend.

corrected

20) Line 724 (Fig 2). It is difficult to read anything in panel K inset or Panel L inset.

We have rearranged this figure and replaced some panels for greater clarity, and to remove redundancy.

21) Line 728. What does "embryo 1" refer to?

This was a remainder from an old plan where each embryo was numbered and listed in a table so that it could be cross-referred to. We have now described in the supplementary table the genotypes and imaging technique for each group of embryos. Where we show data or analyses of the same embryo in different figures, we refer directly to the relevant panels. We have made sure the embryos are referred to correctly in the figure legends.

22) Line 732. A quantitative measure of the quality of the fits of the models to the experimental data should be included.

We have done this, and the new data are now included in the new Figure 2.

23) Line 739. What exactly does "Embryo 2" refer to?

See comment 21

24) Line 779. Why is a z-plane of 15 microns below surface chosen? > 25) Line 797. Why is a z-plane of 25 microns below the surface chosen?

The planes were chosen in each case to show the reader in one single plane rows 7 and 8 along with the central cells > 26) Line 900. Panel G in Supp Fig 5 is not described in figure description.

The panel captions were wrongly numbered. This has now been corrected, and more information on this figure has been included in the text. > - Are prior studies referenced appropriately?

Yes.

• Are the text and figures clear and accurate?

No (see details listed above).

• It would be very helpful to the reader to show direct quantitative comparison of the different mechanical models with the experimental observations to show how much better the nonlinear model is compared to the linear model.

We have included this.

An extended explanation of experiments and experimental results within the main text would improve the manuscript.

We have expanded our explanations in many places.

Significance:

The key advance in this work is in identifying a potential role of nonlinear mechanical properties in contributing to distinct cell behaviors within a tissue during development in vivo. This contributes to a growing body of work highlighting the importance of cell and tissue mechanical properties in regulating cell behaviors during the formation of tissue structure.

This work adds to a growing body of work connecting actomyosin contractility in cells to tissue-scale behavior during development. This work provides a unique mechanical modeling perspective to the study of apical constriction during Drosophila ventral furrow invagination, highlighting a potential role for superelastic cell mechanical behaviors during morphogenesis in vivo.

The finding would be of interest to researchers working in the areas of morphogenesis, mechanobiology, the cytoskeleton, and active matter.

This reviewer's expertise is in experimental studies of the cytoskeleton and cell mechanics during morphogenesis.

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Reply to the reviewers

Reviewer 1:

I think the experiments within the manuscript are generally of good quality and well controlled.

We would like to thank the reviewer for the appreciation of our work.

...However, I find that the authors' conclusions are very often not supported by the experiments performed (as detailed below) and I would strongly recommend that the authors stick to the conclusions that can be drawn based on the data they have generated. In my opinion, this manuscript contains findings that are of interest to the field but it needs to be rewritten with more justifiable conclusions.

We have extensively rewritten the manuscript and toned down the role of the HMR/LHR complex in hybrids while emphasizing its role in Drosophila melanogaster.

1) 'Speciation Core Complex' - The only link to speciation is the fact that the 'SCC' includes D.melanogaster HMR, a known hybrid incompatibility gene. On the other hand, all of these proteins have important functions in a pure species context and all of the interactions reported between the members of the SCC occur in a D.melanogaster background. Also, SCC assembly in viable/inviable hybrids is not tested. Essentially, I would come up with a different and more functionally consistent name for the complex. I highly recommend against naming these stable interactors as the 'SCC' unless the authors can show that mutating any of the other 'SCC' proteins (specifically NLP, NPH, BOH1 & BOH2), which should presumably also disrupt SCC formation, leads to the rescue of hybrid male lethality?

We agree with the reviewer that we base the naming of the complex on the presence of the products of the two known hybrid incompatibility genes Hmr and Lhr. As we did not investigate the complex’ composition in hybrids we agree with the three reviewers that the term SCC is probably misleading. We also agree with the reviewer that it would be highly interesting to investigate whether NLP, NPH, BOH1 or BOH2 mutations also rescue hybrid male lethality. However, we would need to generate fly lines carrying mutations in both the D.mel and the D.sim alleles since the respective genes are autosomal and we feel that this would be beyond the scope of the manuscript. Moreover, such assays would only be possible it those genes are non-essential and not like Nlp, of which the available hypomorphic or deletion alleles are homozygous lethal (**Padeken, J. et al. (2013)**).

2) Is it a stable 6-membered complex? - The only line of evidence for the presence of a stable complex between all 6 proteins are the MS data from Figure 1C and Figure S1A-C. Although I don't think it is necessarily required, a biochemical demonstration that these proteins co-sediment at a high MW would be a much stronger indication of complex formation. That being said, I think the authors can use their expertise in AP-LC/MS to more comprehensively characterize complex formation.

Besides the fact that we observe all six components in AP-MS experiment using either one of the subunits, we have also shown in our previous experiments (Thomae et al, 2013) that all subunits can be purified by a tandem purification using first an antibody against FLAG-HMR followed by a Myc-LHR antibody. We also tried to purify the HMR complex via size exclusion chromatography to determine the size of the complex as suggested by the reviewer. Unfortunately, we did not manage to isolate enough of the complex in a soluble form that allowed us to detect a single peak on a size exclusion column. This may be either due to a disassembly of the complex during the unavoidable dilution during SEC or a lack of antibody sensitivity. We also tried to reconstitute the entire complex from recombinantly expressed proteins but failed to express all subunits in a soluble form. It is worth mentioning that a similar observation has been made, for example, for the Dosage Compensation Complex, which, despite being well characterized, has also eluded a characterization using size exclusion chromatography.

a) For example, the authors could test whether loss of BOH1/BOH2 in S2 cells impacts complex formation. A reduction of interactions between other complex members would strengthen the authors' conclusion of a stable and stoichiometric 6-membered complex.

Based on our observation that HMR and LHR form a stable heterodimeric complex in vitro (Figure S4) we assume that the presence or absence of the other components does not affect the complex composition in its entirety. The experiment suggested by the reviewer would allow us to distinguish between direct and indirect interactions between BOH1/2 and HMR. Though this is clearly a very exciting approach, RNAi mediated knock downs are rarely complete in S2 cells, making such experiments difficult to interpret. Therefore, these experiments would need to be supported by reconstitution of the different complexes in vitro and potentially crosslinking MS experiments. Such extensive molecular analysis would very likely require at least 6 month to be completed and would be beyond the scope of the current manuscript.

1. b) Additionally, I would suggest that they use one (or more) of BOH1/BOH2/NLP/LHR as baits in the S2 cells expressing HMR mutations (HMR2 and HMR DC, Figure 3) to test complex formation. Beyond Figs. 1 and S1, the authors only test one-way interactions between HMR (or HMR mutants) and the other 5 binding partners. It is unclear if the other 5 'SCC' members are capable of binding each other when HMR is mutated. As a result, how HMR affects the ability of other proteins to interact with each other and its role in complex formation remains somewhat unclear. This is particularly important since the authors conclude in the discussion that "HMR acts as a molecular bridge between different modules of the SCC" and that "the integrity of the SCC is essential for its function".

Similar to our answer to the reviewer’s suggestion above, we believe that this experiment requires an additional extensive molecular analysis to be meaningful, which is beyond the scope of the current manuscript. It is important to clarify here that the S2 cells we use still express endogenous full length-HMR, which could participate in complex formation even when Hmr mutant alleles are expressed. To unambiguously show that BOH1 and BOH2 still interact with the other complex components when they no longer associate with HMR, we would therefore need to generate a CRISPR based exchange of all HMR genes in SL2 cells with a mutated version of HMR and analyze their interaction partners. As both alleles fail to fully rescue HMR functionality in a deletion background and as we have shown previously that a removal of HMR results in mitotic defects, it may not even be possible to generate such cell lines.

3) Centromeric vs heterochromatic localization of HMR - There appears to be some differences between Hmr localization across different tissues as the authors have noted in their introduction. In this manuscript, the authors assess HMR localization in S2 cells as well as mitotic and endocycling follicle cells from various stages of oogenesis. In these cell types, the authors compare HMR localization to both Cenp-C (centromere) and HP1 (constitutive heterochromatin). In my opinion, it is not easy to get a clear perspective on what the authors consider to be HMR's true localization in these cells and tissues. I would recommend the following straightforward changes/experiments related to this point,

a) Label the image categories in Figure 4A. Please also describe in detail the classification criteria were used to separate these image categories from one another.

In the revised manuscript we will label the image categories in Figure 4A. An extensive description on how the classification criteria were applied can be found in the methods section.

b) I would also move Figure S7A to the main text since it demonstrates centromeric colocalization of HMR in early follicle cells.

In the revised manuscript we will move **figure S7A to a new figure 5C. We have furthermore investigated the localization of endogenous HMR in various cell types in ovaries, which is going to be included in the revised manuscript as a new figure 5A.

c) Use linescans on existing images to better demonstrate colocalization between Hmr and Cenp-C and/or HP1

In the revised manuscript we will prepare linescans/profile plots for all IF pictures when necessary.

d) Show Cenp-A and HMR staining for the images in Figure 5C and stage 10 follicle cells from Figure S7A.

As stainings with the Cenp-C antibody resulted in more stable and reproducible signals, we used Cenp-C as a proxy for Cenp-A and centromere localization. In Figure S7A and B we stained Cenp-C and showed a greatly reduced expression in follicle cells undergoing endoreplication. We therefore did not perform a Cenp-C (or Cenp-A)/HMR co-staining in these cells and do not think it would add to a better understanding of the mechanisms of HMR locaization (Figure 5C).

e) I feel the authors do not spend enough time discussing the fact that HMRDC still appears to localize to centromeres at most follicle cells upto Stage 7.

We now also include the staining of endogenous HMR (figure 5A revised ms) in the various cell types in ovaries. This allows us to expand the discussion of HMR’s localization in dependency of the cell type and stage. These studies not only reveal the high diversity of HMR localization but also suggests that the potential of HMR to localize to the centromere as well as pericentromeric heterochromatin is crucial for its function. In the revised manuscript we have now discussed the fact that HMRdC still localizes to the centromere up to stage 7 more extensively.

In sum, it would also be nice for the authors to take a clear position on whether HMR is centromeric, heterochromatic or both in the cells they analyze by microscopy and why these localizations may change between the cells they have looked at.

The fact that we now include a novel figure where we investigate HMR’s localization in different cell types allows us to discuss the (diverse) localization as well as its potential regulation more extensively. As the localization is highly dependent on the cell type observed as well as the cell cycle stage use, we feel that these aspects need to be taken into account when describing HMRs localization. This is now discussed in the revised manuscript.

4) HMR2 analyses - I think HMR2 is an important mutant to include as a control for HMRDC, especially since the authors should already have the required strains/data. I specifically mean the following,

1. a) Figure 4C - Please add HMR2 ChIP-seq tracks only if the authors already have this data.

Unfortunately, we were unable to acquire convincing HMR2-ChIP data. This may be due to the fact that HMR2localizes quite diffusely or due to a lower percentage of cells expressing this allele in the S2 lines used. Both issues do not influence our interpretations in AP-MS experiments or in single cell based fluorescence microscopy assays, but is problematic in bulk cell population assays like ChIP. Therefore, we cannot provide good HMR2 ChIP-Seq tracks.

b) Figure 5C and Figure S7B - Add HMR2 IF images. Please also discuss HMR2 localization to centromeres and heterochromatin.

In the revised manuscript, we have/will attache(d) IF images of ovarial tissue made from strains heterozygous for the Hmr2 allele. Due to the lower gene dosage the intensity of HMR stainings is reduced making a precise localization more difficult. As the manuscript mainly focusses on the description of the newly discovered HmrdC allele, we have added this as supplemental material.

c) Figure 5E - Increase n's for the HMR2 fertility assay.

The HMR2 allele has been extensively characterized by Aruna and colleagues (Aruna et al., Genetics (2009)) with regards to its effect on fertility. For this particular assay we only use it as a positive control and reference for the newly described HMRdC allele. We therefore feel that an increase in the number of replicates would be redundant to the earlier publications.

5) HMR localization in female germline cells - Given that the authors indicate that female fertility and telomeric transposon suppression are compromised with HMR2 and HMRDC, I think it would strengthen the manuscript to address HMR localization with respect to heterochromatin and centromeres in the nurse cells and/or oocytes.

We now also include the staining of endogenous HMR (figure 5A revised ms) in nurse cells, oocytes and early-stage follicle cells. This allows us to expand the discussion of HMR’s localization in dependency of the cell type and stage.

6) I find the last part of the abstract and discussion i.e. HMR bridges heterochromatin and the centromere, to be very speculative based on the data presented. As far as I can tell, the only experimental basis for this conclusion is the fact that HMR binds known centromeric and heterochromatic proteins. With this logic, you could easily make a similar argument for the numerous proteins that colocalize with centromeric and pericentromeric heterochromatin. Personally, I would not speculate extensively on a HMR bridging activity without more compelling functional readouts.

Our hypothesis of HMR as a bridging factor between centromeric and pericentromeric heterochromatin is not only based on its colocalization and interaction with components of chromatin types but also on our previous findings that an HMR knockdown results in a moderate centromere declustering and studies using super-resolution microscopy, which indicate that HMR is sandwiched between the two components (Kochanova, N. Y. et al. (2020)). As the proteomic analysis of the two HMR alleles presented in this study suggest that interactions with both components are required for full functionality of HMR, we assume that it bridges between the two chromatin components. However, we agree with the reviewer that this could also be explained by a centromeric as well as a heterochromatic function of HMR, which are independent from each other. We therefore removed the hypothesis from the abstract and discussed it together with other potential explanations for our findings.

**Minor comments:**

1) Intersection plot - I would explain the intersection plot on Figure 1C more thoroughly (I found it confusing).

We expanded the paragraph in which we explain the intersection plot in figure 1C.

2) Image colours - The images in Figure S2 and Figure S7 are hard to interpret due to the colours used for the HA and Hmr channel respectively. I would use the white pseudo-colour for DAPI and omit this channel from the merged image and insets (a line demarcating the nucleus would suffice in the merged image). In addition, a linescan would better represent colocalizations or lack thereof.

We will omit the DAPI channel from the merged images and used a line to demarcate the nucleus as suggested by the reviewer in the revised manuscript. To better illustrate co-localisation of distinct factors we will used line profile plots.

3) I'm not convinced that one can determine stoichiometry and sub-stoichiometry of protein complexes based on spectral counts; spectral counts could be affected by other factors. Therefore, I would hesitate to use "However, HP1a is only present in sub-stoichiometric amounts in the AP-MS purifications with antibodies against the SCC...."

The question of whether the stoichiometry of complexes using iBAQ values of purified protein complexes is intensely discussed in the field. Several studies do suggest that this can indeed be done (i.e. Wohlgemuth, Iet al. Proteomics 15, 862–879 (2015); Smits, A. H., Nucleic Acids Research 41, e28–e28 (2012)), which is why we commented on the lower intensity of HP1a relative to the other subunits of the complex. However, we agree with the reviewer that this can only be an approximation rather than a precise measurement (which would need a full in vitro reconstitution, see comments above). We have mentioned this in the revised manuscript.

4) Ambiguity in description of methods - In the methods section 'Crosses for generating Hmr genotypes for hybrid viability assays', the authors state that "In the rescue experiment, Hmr+ served as a positive (lethality rescue) and Hmr2 as a negative control (no lethality rescue)". The authors might consider rewording this as I think it's a bit strange to refer to hybrid male lethality as a rescued state.

We agree with the reviewer that the wording to describe the assay we used to investigate HMR’s function in male hybrids is counterintuitive as a “rescue of functionality” results in male hybrid lethality. To better describe it we now call the assay “hybrid viability suppression”, according to the nomenclature that has been used by Aruna et al, 2009 (Aruna, S. et al. Genetics (2009)).

.

Reviewer #1 (Significance (Required)):

**Nature and Significance of the advance:**

This work adds to the study of reproductive isolation in Drosophila by defining a stable set of molecular interactors of the HMR hybrid incompatibility protein. In my opinion, this study offers a platform for future research into the poorly understood molecular events that trigger hybrid incompatibility in Drosophila. In addition, the authors generate a novel HMR mutation (HMRDC) that also rescues hybrid male lethality and it would be interesting to determine in finer detail how closely this mutation mimics other known HMR mutations. A characterization of BOH1/BOH2 would have also significantly strengthened the manuscript.

We would like to thank the reviewer for the appreciation of our work. We agree with the reviewer that a deeper characterization of BOH1/BOH2 will further unravel their role in the complex. However, our initial experiments using null alleles or knock downs of BOH1 and BOH2 in D.mel showed no effect or only minor effects on transposon activation and hybrid male lethality. This is most probably due to the fact that the D.sim alleles can fully complement for their function. Moreover, the recombinant expression of BOH1 and 2 turned out to be difficult due to problems in protein solubility. We therefore need to postpone our BOH1 and 2 studies to a later timepoint.

**My Expertise:**

Satellite DNA repeats, Chromocenters, Speciation, Hybrid Incompatibility

**Referees cross-commenting"

I also agree that all the reviewer comments are reasonable. The manuscript would be significantly improved by making conclusions that can be supported by the data. I think some additional experiments are also warranted to make the paper more robust.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

In this study, the authors identify a protein complex that contains hybrid incompatibility genes Hmr and Lhr, naming it SCC (Speciation Core Complex). This paper's major conclusions are: 1) overexpression of Hmr (which resembles the situation in hybrid, where hmr/lhr are overexpressed) results in ectopic protein-protein interaction. 2) Hmr's DNA binding domain (mutated in Hmr2) and C-terminal domain (known to interact with Lhr) are important for its function and in causing hybrid lethality.

The identification of SCC complex is quite intriguing, but this paper does not cover much of functional significance of this complex at all. For example, does mutating other components of SCC complex (BOH1 etc) rescue hybrid lethality? Without examining these important issues, they instead drifted to study the domain function of Hmr. It is not so clear why these two lines of studies are glued together in one paper.

It is not that I insist that the authors have to do all these experiments, but the assembly of the paper makes this paper quite inconclusive. After reading it, the readers are left behind wondering what is the function of SCC---and we do not even know whether 'speciation core complex' is a fair naming, without any knowledge whether any of the components being involved in speciation or not.

Overall, this work contains a lot of important information, which promises future breakthrough on the subject matter. However, unfortunately, the study is not carried out to generate any conclusion and is fairly incomplete at this point.

We thank the reviewer for his appreciation of the importance of our work and apologize that we did not clarify the reasoning of the experiments sufficiently. We think that part of the reviewer’s disappointment is due the fact that we named the complex speciation core complex (SCC), which was indeed an unfortunate decision as we are unable to investigate the complex in male hybrids where it exerts it’s function in mediating hybrid incompatibility (see also answer to comments of reviewer 1). We therefore changed the name to HMR complex and tried to better explain the rational of our experiments in the text.

**Specific comments.**

• Quality of Fig4A is too low. I cannot even tell where is the boundary of nucleus. Diffuse signal in category 'yellow' and 'grey'---are they entire cell or nucleus or nucleolus? Please add additional marker(s) for better interpretation of the Hmr signal presented.

We have improved the quality of figure 4A by adding lines to indicate the nuclear boundary and inserting profile plots to better illustrate the different types of co-localisation.

• In Fig4A and 5C, the localization of Hmr (wild type version) looks quite different in these two images. Which image is more 'representative' for Hmr localization? (as they build the logic on Hmr localization, this inconsistency is quite bothering). This might be cell-type-specific issue, but if so, how do we know the relevance of their localization? These issues make the result of localization analysis of wt/mutant Hmr inconclusive.

After reading the reviewers responses we realized that we did not describe our findings well enough, which resulted in a major confusion about the localization of HMR in cells. Indeed, the localization of HMR differs widely depending on the cell type used. We have now included a new figure (new Figure 5A) illustrating the analysis of the endogenous HMR localization in ovaries isolated from D.mel. We hope that the additional figure together with our interpretation helps to alleviate the confusion and adds to the understanding of HMR’s function and potential evolution of HMR.

Reviewer #2 (Significance (Required)):

Hmr and Lhr are known as 'hybrid incompatibility genes', deletion of which rescues male hybrid lethality in Drosophila melanogaster/simulans hybrid crosses. Understanding the molecular function of Hmr and Lhr is expected to provide insights into the fundamental question of how two species become incompatible (i.e. how speciation occurs). This study investigates the protein complex that contains Lhr and Hmr, identifying a previously unidentified 'core' complex. Understanding the function of this complex may significantly advance our understanding of speciation.

**Referees cross-commenting"

I think all review comments are reasonable. However, I'd like to emphasize that the biggest issue with this paper is not about the data, but how the authors frame it. The term such as 'speciation core complex' is beyond 'hype' (not even 'exaggeration'). Simply there is no evidence that this term can be supported. I think the authors need to be more ethical. I would be surprised if authors truly believe they can claim that the term 'speciation core complex' is justifiable in science.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

**Summary:**

The manuscript "The integrity of the speciation core complex is necessary for centromeric binding and reproductive isolation in Drosophila" by Lukacs and colleagues describes a study that show, by mass-spec and ChIP-seq, that two well established hybrid incompatibility proteins form a 6-protein complex that predominantly localizes near HP1a bound chromatin boundaries. With a C-terminal domain of HMR deleted, the 6-protein core complex was not disrupted, but its interaction and subsequent localization to HP1a domain near centromeres was lost. In addition, an HMR double mutant that disrupts the interaction between HMR and other components of the 6-protein core complex was tested and similar distribution patterns as for the dC mutant were observed. Next, the nuclear localization was HMR was tested in fruit fly follicle cells by IF. In endoreplicating cells, HMR-dC did not colocalize with HP1a, as did the double mutant. The expression level of several transposable elements (TEs) was assessed and only the full length wt Hmr transgene was able to rescue the repression of TEs, whereas neither the dC and double mutants did. When the number of offspring was assayed, a similar pattern was observed. Finally, male hybrid lethality was assayed by crossing D melanogaster mothers with different Hmr alleles with wt D simulans and only the wt Hmr allele resulted in male lethality, whereas both cD and double mutants resulted in 10-40% of the offspring to be male. These findings led the authors to conclude that 1) 6-protein speciation core complex containing HMR, LHR, NLP, NPH, and two uncharacterized proteins called BOH1 and BOH2, 2) overexpression of HMR/LHR results in novel interactions with other chromatin factors, 3) both the double mutant (E317K and G527A) and the C-terminal deletion mutant are important for for protein-protein interaction within the 6-protein complex and associated factors such as HP1a, and 4) HMR bridges heterochromatin and centromeres.

**Major comments:**

• Most of the key conclusions are supported by the evidence presented in this manuscript. The link between centromeres and HMR (and presumably the rest of the 6-protein complex) hinges only on colocalization IF and ChIP-seq data. The change in Hmr localization in cycling follicle vs endoreplicating cells of especially the dC mutant is very interesting. The loss of CENP-C signal correlates with a change in Hmr^dC signal. What exactly drives this change is not explored.

We have shown in the past that HMR requires full length Cenp-C to localize to the centromere in S2 cells. We assume that this is also the case in the follicle cells. Therefore, the lack of Cenp-C recruitment in endoreplicating cells is likely the reason why HMR localizes primarily to HP1a containing heterochromatin. Differently from wild type HMR, HMRdC can’t bind LHR/HP1a as our AP-MS data show and therefore is not recruited to heterochromatin and diffuses away in later stages. We have described this point more extensively in the revised manuscript

• The data presented in this manuscript are mostly clear (see minor comments) and appear to be reproducible, especially as the methods sections is detailed and both the ChIP-seq and mass-spec data is deposited in publicly accessible databases.
• The rational why both HMR and LHR are overexpressed in cell lines is not clearly explained.

As outlined in our response to reviewer 1 the overexpression of HMR and LHR was designed to simulate the hybrid situation, which shows an increase in HMR and LHR levels (Thomae, A. W. et al. Developmental Cell 27, 412–424 (2013)). We have indicated this in the revised manuscript.

• The HMR/LHR overexpression experiment is very nice, and as one would expect, resulted in more protein interactions. Some of these might simply be the result from the abundance of HMR and LHR, which have saturated the core 6-protein complex. This leaves the question what is the true minimal size of the HMR/LHR complex? The dC mutant that removes the BESS domain as well as the double point mutations that disrupts the complex altogether, get to the importance of the stability of the complex and its association with especially HP1a. What the minimal interacting partners of HMR and LHR could be explored by knocking-down both factors and do mass-spec.

We agree with the reviewer that the abundance of HMR and LHR results in a saturation of the core complex thereby having a spillover effect on other proteins. In this regard it is worth mentioning that the expression of the Hmr2 allele does not completely disrupt the complex but rather results in a loss of interactions with NLP, NPH, BOH1 and BOH2 while maintaining the interaction with LHR and HP1a. In fact, when the HMR2 protein is expressed, it shows a stronger interaction with known heterochromatic proteins than the wt protein (Figure 3B). As both mutant alleles show functional defects in pure species and in male hybrids we assume that HMR and LHR need to bind both chromatin types simultaneously. We consider the complex to be somewhat modular as we show that HMR and LHR can interact in isolation (Figure S4) while others have shown that LHR and HP1a, as well as NLP and NPH interact (**Greil, F. et al. EMBO J (2007); Anselm, E. et al. Nucleic Acids Research (2018)respectively). This is now pointed out in the revised manuscript

• For the telomeric TE expression as well as offspring count shown in Figure 5D,E, a wild-type control would be informative as a measure how well the Hmr+/+ rescues both phenotypes.

The misregulation of transposable elements (TE) and fertility defects of Hmr loss of function mutants have been previously characterized (Satyaki, P. R. V. et al. PLoS genetics (2014); Aruna et al.,Genetics (2009))**. We therefore rather focused on the relative expression of TEs in the HmrdC and Hmr2 mutants relative to the wild type rescue allele (Hmr+). Hmr2 serves as a known non-rescue allele (Aruna et al., 2009) in the fertility experiment, while in the TE experiment we describe for the first time a defect in TE repression for this allele.

**Minor comments:**

• In the opening paragraph of the introduction, the authors describe a scenario of sympatric speciation, which is subsequently highlighted by the speciation event between D. melanogaster and D. simulans. Yet, these two species have similar but not identical distribution range, leaving open the possibility the speciation event happened in parapatry. It might be worth rephrasing the first paragraph to leave open both modes of speciation, especially as the manuscript focuses on the mechanistic side of hybrid incompatability-associated proteins.

We did not want to imply that our experiments allow a distinction between a sympatric or parapatric speciation. We thank the reviewer for pointing this out and rephrased the first paragraph accordingly.

• Some of the abbreviations are repeated (e.g. SCC) others aren't introduced (e.g. HI). Overall, less abbreviations will make the text more readable, especially for non-experts.

We tried to avoid acronyms wherever possible and got rid of the term SCC altogether. All acronyms are introduced at the first appearance.

• In IF signal in Figure 4A is difficult to see on the black background. I would suggest either increasing the gain to improve the visibility of the signal or show in black-and-white. In addition, the colors should be labeled in the figure for clarity.

We improved the quality of Figure 4A and labeled the different types of localization (see also answer to reviewer 1).

• In Figure 5C the images for the Hmr^KO;Hmr^2 appears to be missing.

See answer to reviewer 1 (4b). We have/will include the corresponding picture as supplementary material as we consider the characterization of the novel Hmr allele to be the main focus of the manuscript.

In addition, for non-experts it might be helpful to mention which set of IF images are controls, rescues, and test, similar to what was done in Figure 5B.

We have/will indicate which IF pictures are controls and rescue experiments

Reviewer #3 (Significance (Required)):

**Significance:**

• This study provides novel insight how two factors involved in male hybrid lethality, with which chromatin factors they are associated, and how two mutants impact the chromatin localization and in vivo phenotypes.
• Understanding the molecular basis of speciation is limited as most factors that drive speciation are not identified. Drosophila species are at the forefront of this research. Post-zygotic factors have predominantly found to have strong speciation potential. This work build very nicely on this work.
• This manuscript will be predominantly interesting for the Drosophila chromatin field and speciation field.
• I am trained in comparative genomic focusing on centromeric repeats and now study chromatin dynamics at the single molecule level, using cell biology, biochemical and biophysical tools.

We thank the reviewer for appreciating our work. We think that our work will also be interesting for researchers focusing on centromere clustering and genome organization in general and independently of the Drosophila system.

**Referees cross-commenting"

Reviewer comments look reasonable to me- 1-3 months revision is not an undue burden, I think they can do at least some of what was requested. In response to Rev2: Agreed, they ought to tone it down

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Referee #3

Evidence, reproducibility and clarity

Summary:

The manuscript "The integrity of the speciation core complex is necessary for centromeric binding and reproductive isolation in Drosophila" by Lukacs and colleagues describes a study that show, by mass-spec and ChIP-seq, that two well established hybrid incompatibility proteins form a 6-protein complex that predominantly localizes near HP1a bound chromatin boundaries. With a C-terminal domain of HMR deleted, the 6-protein core complex was not disrupted, but its interaction and subsequent localization to HP1a domain near centromeres was lost. In addition, an HMR double mutant that disrupts the interaction between HMR and other components of the 6-protein core complex was tested and similar distribution patterns as for the dC mutant were observed. Next, the nuclear localization was HMR was tested in fruit fly follicle cells by IF. In endoreplicating cells, HMR-dC did not colocalize with HP1a, as did the double mutant. The expression level of several transposable elements (TEs) was assessed and only the full length wt Hmr transgene was able to rescue the repression of TEs, whereas neither the dC and double mutants did. When the number of offspring was assayed, a similar pattern was observed. Finally, male hybrid lethality was assayed by crossing D melanogaster mothers with different Hmr alleles with wt D simulans and only the wt Hmr allele resulted in male lethality, whereas both cD and double mutants resulted in 10-40% of the offspring to be male. These findings led the authors to conclude that 1) 6-protein speciation core complex containing HMR, LHR, NLP, NPH, and two uncharacterized proteins called BOH1 and BOH2, 2) overexpression of HMR/LHR results in novel interactions with other chromatin factors, 3) both the double mutant (E317K and G527A) and the C-terminal deletion mutant are important for for protein-protein interaction within the 6-protein complex and associated factors such as HP1a, and 4) HMR bridges heterochromatin and centromeres.

Major comments:

• Most of the key conclusions are supported by the evidence presented in this manuscript. The link between centromeres and HMR (and presumably the rest of the 6-protein complex) hinges only on colocalization IF and ChIP-seq data. The change in Hmr localization in cycling follicle vs endoreplicating cells of especially the dC mutant is very interesting. The loss of CENP-C signal correlates with a change in Hmr^dC signal. What exactly drives this change is not explored.
• The data presented in this manuscript are mostly clear (see minor comments) and appear to be reproducible, especially as the methods sections is detailed and both the ChIP-seq and mass-spec data is deposited in publicly accessible databases.
• The rational why both HMR and LHR are overexpressed in cell lines is not clearly explained.
• The HMR/LHR overexpression experiment is very nice, and as one would expect, resulted in more protein interactions. Some of these might simply be the result from the abundance of HMR and LHR, which have saturated the core 6-protein complex. This leaves the question what is the true minimal size of the HMR/LHR complex? The dC mutant that removes the BESS domain as well as the double point mutations that disrupts the complex altogether, get to the importance of the stability of the complex and its association with especially HP1a. What the minimal interacting partners of HMR and LHR could be explored by knocking-down both factors and do mass-spec.
• For the telomeric TE expression as well as offspring count shown in Figure 5D,E, a wild-type control would be informative as a measure how well the Hmr+/+ rescues both phenotypes.

Minor comments:

• In the opening paragraph of the introduction, the authors describe a scenario of sympatric speciation, which is subsequently highlighted by the speciation event between D. melanogaster and D. simulans. Yet, these two species have similar but not identical distribution range, leaving open the possibility the speciation event happened in parapatry. It might be worth rephrasing the first paragraph to leave open both modes of speciation, especially as the manuscript focuses on the mechanistic side of hybrid incompatability-associated proteins.
• Some of the abbreviations are repeated (e.g. SCC) others aren't introduced (e.g. HI). Overall, less abbreviations will make the text more readable, especially for non-experts.
• In IF signal in Figure 4A is difficult to see on the black background. I would suggest either increasing the gain to improve the visibility of the signal or show in black-and-white. In addition, the colors should be labeled in the figure for clarity.
• In Figure 5C the images for the Hmr^KO;Hmr^2 appears to be missing. In addition, for non-experts it might be helpful to mention which set of IF images are controls, rescues, and test, similar to what was done in Figure 5B.

Significance

Significance:

• This study provides novel insight how two factors involved in male hybrid lethality, with which chromatin factors they are associated, and how two mutants impact the chromatin localization and in vivo phenotypes.
• Understanding the molecular basis of speciation is limited as most factors that drive speciation are not identified. Drosophila species are at the forefront of this research. Post-zygotic factors have predominantly found to have strong speciation potential. This work build very nicely on this work.
• This manuscript will be predominantly interesting for the Drosophila chromatin field and speciation field.
• I am trained in comparative genomic focusing on centromeric repeats and now study chromatin dynamics at the single molecule level, using cell biology, biochemical and biophysical tools.

**Referees cross-commenting"

Reviewer comments look reasonable to me- 1-3 months revision is not an undue burden, I think they can do at least some of what was requested. In response to Rev2: Agreed, they ought to tone it down

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Referee #2

Evidence, reproducibility and clarity

In this study, the authors identify a protein complex that contains hybrid incompatibility genes Hmr and Lhr, naming it SCC (Speciation Core Complex). This paper's major conclusions are: 1) overexpression of Hmr (which resembles the situation in hybrid, where hmr/lhr are overexpressed) results in ectopic protein-protein interaction. 2) Hmr's DNA binding domain (mutated in Hmr2) and C-terminal domain (known to interact with Lhr) are important for its function and in causing hybrid lethality.

The identification of SCC complex is quite intriguing, but this paper does not cover much of functional significance of this complex at all. For example, does mutating other components of SCC complex (BOH1 etc) rescue hybrid lethality? Without examining these important issues, they instead drifted to study the domain function of Hmr. It is not so clear why these two lines of studies are glued together in one paper.

It is not that I insist that the authors have to do all these experiments, but the assembly of the paper makes this paper quite inconclusive. After reading it, the readers are left behind wondering what is the function of SCC---and we do not even know whether 'speciation core complex' is a fair naming, without any knowledge whether any of the components being involved in speciation or not.

Overall, this work contains a lot of important information, which promises future breakthrough on the subject matter. However, unfortunately, the study is not carried out to generate any conclusion and is fairly incomplete at this point.

Specific comments.

• Quality of Fig4A is too low. I cannot even tell where is the boundary of nucleus. Diffuse signal in category 'yellow' and 'grey'---are they entire cell or nucleus or nucleolus? Please add additional marker(s) for better interpretation of the Hmr signal presented.
• In Fig4A and 5C, the localization of Hmr (wild type version) looks quite different in these two images. Which image is more 'representative' for Hmr localization? (as they build the logic on Hmr localization, this inconsistency is quite bothering). This might be cell-type-specific issue, but if so, how do we know the relevance of their localization? These issues make the result of localization analysis of wt/mutant Hmr inconclusive.

Significance

Hmr and Lhr are known as 'hybrid incompatibility genes', deletion of which rescues male hybrid lethality in Drosophila melanogaster/simulans hybrid crosses. Understanding the molecular function of Hmr and Lhr is expected to provide insights into the fundamental question of how two species become incompatible (i.e. how speciation occurs). This study investigates the protein complex that contains Lhr and Hmr, identifying a previously unidentified 'core' complex. Understanding the function of this complex may significantly advance our understanding of speciation.

**Referees cross-commenting"

I think all review comments are reasonable. However, I'd like to emphasize that the biggest issue with this paper is not about the data, but how the authors frame it. The term such as 'speciation core complex' is beyond 'hype' (not even 'exaggeration'). Simply there is no evidence that this term can be supported. I think the authors need to be more ethical. I would be surprised if authors truly believe they can claim that the term 'speciation core complex' is justifiable in science.

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Referee #1

Evidence, reproducibility and clarity

Summary

How genes involved in hybrid incompatibility function within and across species remains incompletely characterized. This manuscript identifies two novel proteins (BOH1, BOH2) as well as three known proteins (LHR, NLP, NPH) as strong and reproducible interactors of the HMR hybrid incompatibility gene using AP-LC-MS in Drosophila S2 cells and labels these proteins as a 'speciation core complex' (SCC). The authors further show that HMR mutations (the previously identified HMR2 and a newly generated C-terminal truncation lacking the HMR BESS motif, HMRC) differentially disrupt these interactions and alter centromeric HMR localization in S2 cells and tissues. Much like previously described HMR mutations (e.g. HMR2), HMRC rescues HMR-mediated hybrid male lethality in D.melanogaster-D.simulans hybrids leading the authors to conclude that the integrity of the SCC is necessary for centromeric binding and reproductive isolation.

Major comments:

I think the experiments within the manuscript are generally of good quality and well controlled. However, I find that the authors' conclusions are very often not supported by the experiments performed (as detailed below) and I would strongly recommend that the authors stick to the conclusions that can be drawn based on the data they have generated. In my opinion, this manuscript contains findings that are of interest to the field but it needs to be rewritten with more justifiable conclusions.

1) 'Speciation Core Complex' - The only link to speciation is the fact that the 'SCC' includes D.melanogaster HMR, a known hybrid incompatibility gene. On the other hand, all of these proteins have important functions in a pure species context and all of the interactions reported between the members of the SCC occur in a D.melanogaster background. Also, SCC assembly in viable/inviable hybrids is not tested. Essentially, I would come up with a different and more functionally consistent name for the complex. I highly recommend against naming these stable interactors as the 'SCC' unless the authors can show that mutating any of the other 'SCC' proteins (specifically NLP, NPH, BOH1 & BOH2), which should presumably also disrupt SCC formation, leads to the rescue of hybrid male lethality?

2) Is it a stable 6-membered complex? - The only line of evidence for the presence of a stable complex between all 6 proteins are the MS data from Figure 1C and Figure S1A-C. Although I don't think it is necessarily required, a biochemical demonstration that these proteins co-sediment at a high MW would be a much stronger indication of complex formation. That being said, I think the authors can use their expertise in AP-LC/MS to more comprehensively characterize complex formation.

a) For example, the authors could test whether loss of BOH1/BOH2 in S2 cells impacts complex formation. A reduction of interactions between other complex members would strengthen the authors' conclusion of a stable and stoichiometric 6-membered complex.

b) Additionally, I would suggest that they use one (or more) of BOH1/BOH2/NLP/LHR as baits in the S2 cells expressing HMR mutations (HMR2 and HMR C, Figure 3) to test complex formation. Beyond Figs. 1 and S1, the authors only test one-way interactions between HMR (or HMR mutants) and the other 5 binding partners. It is unclear if the other 5 'SCC' members are capable of binding each other when HMR is mutated. As a result, how HMR affects the ability of other proteins to interact with each other and its role in complex formation remains somewhat unclear. This is particularly important since the authors conclude in the discussion that "HMR acts as a molecular bridge between different modules of the SCC" and that "the integrity of the SCC is essential for its function".

3) Centromeric vs heterochromatic localization of HMR - There appears to be some differences between Hmr localization across different tissues as the authors have noted in their introduction. In this manuscript, the authors assess HMR localization in S2 cells as well as mitotic and endocycling follicle cells from various stages of oogenesis. In these cell types, the authors compare HMR localization to both Cenp-C (centromere) and HP1 (constitutive heterochromatin). In my opinion, it is not easy to get a clear perspective on what the authors consider to be HMR's true localization in these cells and tissues. I would recommend the following straightforward changes/experiments related to this point,

a) Label the image categories in Figure 4A. Please also describe in detail the classification criteria were used to separate these image categories from one another.

b) I would also move Figure S7A to the main text since it demonstrates centromeric colocalization of HMR in early follicle cells.

c) Use linescans on existing images to better demonstrate colocalization between Hmr and Cenp-C and/or HP1.

d) Show Cenp-A and HMR staining for the images in Figure 5C and stage 10 follicle cells from Figure S7A.

e) I feel the authors do not spend enough time discussing the fact that HMRC still appears to localize to centromeres at most follicle cells upto Stage 7.

In sum, it would also be nice for the authors to take a clear position on whether HMR is centromeric, heterochromatic or both in the cells they analyze by microscopy and why these localizations may change between the cells they have looked at.

4) HMR2 analyses - I think HMR2 is an important mutant to include as a control for HMRC, especially since the authors should already have the required strains/data. I specifically mean the following,

a) Figure 4C - Please add HMR2 ChIP-seq tracks only if the authors already have this data.

b) Figure 5C and Figure S7B - Add HMR2 IF images. Please also discuss HMR2 localization to centromeres and heterochromatin.

c) Figure 5E - Increase n's for the HMR2 fertility assay.

5) HMR localization in female germline cells - Given that the authors indicate that female fertility and telomeric transposon suppression are compromised with HMR2 and HMRC, I think it would strengthen the manuscript to address HMR localization with respect to heterochromatin and centromeres in the nurse cells and/or oocytes.

6) I find the last part of the abstract and discussion i.e. HMR bridges heterochromatin and the centromere, to be very speculative based on the data presented. As far as I can tell, the only experimental basis for this conclusion is the fact that HMR binds known centromeric and heterochromatic proteins. With this logic, you could easily make a similar argument for the numerous proteins that colocalize with centromeric and pericentromeric heterochromatin. Personally, I would not speculate extensively on a HMR bridging activity without more compelling functional readouts.

Minor comments:

1) Intersection plot - I would explain the intersection plot on Figure 1C more thoroughly (I found it confusing).

2) Image colours - The images in Figure S2 and Figure S7 are hard to interpret due to the colours used for the HA and Hmr channel respectively. I would use the white pseudo-colour for DAPI and omit this channel from the merged image and insets (a line demarcating the nucleus would suffice in the merged image). In addition, a linescan would better represent colocalizations or lack thereof.

3) I'm not convinced that one can determine stoichiometry and sub-stoichiometry of protein complexes based on spectral counts; spectral counts could be affected by other factors. Therefore, I would hesitate to use "However, HP1a is only present in sub-stoichiometric amounts in the AP-MS purifications with antibodies against the SCC...."

4) Ambiguity in description of methods - In the methods section 'Crosses for generating Hmr genotypes for hybrid viability assays', the authors state that "In the rescue experiment, Hmr+ served as a positive (lethality rescue) and Hmr2 as a negative control (no lethality rescue)". The authors might consider rewording this as I think it's a bit strange to refer to hybrid male lethality as a rescued state.

Significance

Nature and Significance of the advance:

This work adds to the study of reproductive isolation in Drosophila by defining a stable set of molecular interactors of the HMR hybrid incompatibility protein. In my opinion, this study offers a platform for future research into the poorly understood molecular events that trigger hybrid incompatibility in Drosophila. In addition, the authors generate a novel HMR mutation (HMRC) that also rescues hybrid male lethality and it would be interesting to determine in finer detail how closely this mutation mimics other known HMR mutations. A characterization of BOH1/BOH2 would have also significantly strengthened the manuscript.

My Expertise:

Satellite DNA repeats, Chromocenters, Speciation, Hybrid Incompatibility

**Referees cross-commenting"

I also agree that all the reviewer comments are reasonable. The manuscript would be significantly improved by making conclusions that can be supported by the data. I think some additional experiments are also warranted to make the paper more robust.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This report examines the mechanism by which the KSHV KaposinB (KapB) protein causes disassembly of processing bodies (PBs) in HUVECs. The authors show that the oncogenic transcription factor YAP is an important component in the signaling pathway of KapB of the oncogenic herpesvirus Kaposi's Sarcoma herpesvirus, which involves the host cell GTPase RhoA, leading to disassembly of processing bodies (PBs).

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Reply to the reviewers

We thank the reviewers for their positive comments on our manuscript. To address their criticisms, we propose to do the following experiments:

Reviewer 1 (mi__nor comments)__:

1. In Fig. 1, the authors show that Btz-WT, but not Btz-HD, localizes to the posterior pole of the oocyte. Do the authors see Btz-WT and/or Btz-HD localized to MNs/muscles/glia at the NMJ? We have had difficulty detecting the expression of our Btz-GFP transgenes at the NMJ. In case this was due to competition with endogenous wild-type Btz, we will repeat the staining in a btz mutant background. If the protein is still undetectable, we can include data showing the localization of UAS-Btz-GFP when overexpressed in muscles or motor neurons.

The mitochondrial phenotypes observed in Btz mutants are striking. But it seems possible that there are defects in overall mitochondrial levels in muscle in addition to defects in their localization. Overall, mitochondrial levels seemed reduced in Btz mutants. Is it possible to do a ATP5A immunoblot in Btz mutants to test whether overall mitochondrial levels are altered?

We will do a Western blot to compare ATP5A levels in btz2/+ and btz2/Df(3R)BSC497 larval carcasses.

ECM proteins are known to be critical for regulating TGFB signaling. That, taken with the multi-tissue genetic requirement for Btz, suggests that Btz might directly regulate either Ltl or Frac RNA, given that these ECM proteins are likely deposited by multiple cell types.

We agree that this is a possibility and we will mention it in the Discussion.

Reviewer 2 (major comments):

1. In Figure 1, regarding the validation of rescue constructs: the EJC interaction-defective mutant is based solely on conservation, as all structural/interaction studies cited with Btz bound to EJC have been with human proteins. They use Vasa localization as a readout of EJC-dependent function, but this is indirect and only assesses one aspect of EJC function (localization). Since many of the main conclusions in the paper are predicated on this mutant being EJC-independent, they should validate this with the Drosophila orthologs using immunoprecipitation. They demonstrate the capability of expressing GFP-tagged versions of Casc3 WT and mutant in S2 cells, so this should not be a cumbersome control experiment to include. We will express tagged Btz-WT and Btz-HD proteins in S2 cells and test whether they can be co-immunoprecipitated with Myc-tagged Drosophila eIF4AIII.

Regarding Figure 3, it could be postulated that the number of boutons would be influenced by the length of axons. Is axon outgrowth accounted for in these experiments? This would influence number of synaptic boutons. Panel F looks very different from panel A in terms of axon length (could this be due to axon outgrowth defect and/or impacted muscle size?) Can quantitation be done also by normalizing to axon length (bouton number/axon length)? Or perhaps this is accounted for in muscle size? If so, this should be explained.

• *

The NMJ grows during development by adding both axonal branches and synaptic boutons, so its size can be measured by counting the number of boutons or branches or measuring branch length. These measures are usually well correlated. In this paper we used bouton number normalized to muscle surface area as our measure of NMJ size, but we did observe corresponding changes in the number and length of branches, as the reviewer points out. We will explain this more clearly in the text.

In Figure 3 quantification: n's vary between genotypes significantly, and this should be explained (e.g. was there a recovery issue between genotypes or just fewer needed for WT-like?).

• *

The btz mutant larvae are more difficult to dissect due to muscle fragility, and some crosses in this genetic background may have yielded fewer usable filets than desired. We believe the numbers we obtained are sufficient to show which differences are significant.

In Figure 4 panels B and F (mutants), there appears to be reduced axon outgrowth (see point above). This should be taken into account when expressing bouton number.

• *

As explained in our response to point 2, axon length and bouton number are correlated measures of synapse size and vary together in this figure as expected.

The RNA-seq data (Figure 5) has a potential issue in that they used larvae with a balancer chromosome (Df), which yields a 50% reduction in any genes on that chromosome. They acknowledge this and removed these genes from the analysis, but the concern remains that this still might be a confounding variable (for example, if reduction in any of these genes might disrupt a signaling pathway). We do not think that the RNA-seq needs to be repeated, but we propose that the authors validate these targets using qPCR in their MN-specific btz knockdown system (this way, they can also include magoh and eif4aIII knockdowns for comparison).

• *

Because only one btz allele was available, we used transheterozygotes with a deficiency for the region to avoid homozygosing other mutations that might be present on the btz2 chromosome. As a consequence, we did observe reduced expression of genes located within the deficiency (which covers a small region, not an entire chromosome), and it is possible that this might contribute to the phenotype. However, we have seen a similar reduction in NMJ size in btz2 homozygotes. We do not think that motor neuron-specific btz knockdown is a useful genotype to validate the RNA-Seq results because ltl and frac levels do not change significantly in the CNS, only in muscle, and knockdown only in motor neurons would be unlikely to change daw levels measured in the whole CNS. Knocking down mago or eIF4AIII in muscle is lethal before the third larval instar stage, preventing us from comparing their effects on gene expression to those of btz. However, we will do qRT-PCR to measure daw, ltl and frac mRNA levels in btz2 homozygous mutant muscles.

Reviewer 2 (minor comments):

1. *Some statements made in the introduction that are not entirely accurate: **

   "A fourth core subunit, known as Barentsz (Btz), Cancer susceptibility candidate gene 3 (CASC3), or Metastatic lymph node 51 (MLN51), associates with the complex following the completion of splicing, and is required for the effects of the EJC on translation, NMD and mRNA localization (Chazal et al., 2013; Palacios et al., 2004; Shibuya et al., 2006; van Eeden et al., 2001)."

   A recent study indicates that Casc3 is not required for EJC-dependent NMD targets in human cells, but rather enhances NMD on a subset of targets (Gerbracht et al. 2020 NAR). Perhaps "is required" should be changed to "plays a role in cytoplasmic EJC-mediated processes, such as...". It has also been shown that EJC core can assemble without Casc3 (e.g. Ballut et al 2005 NSMB, Gehring et al 2009 PLoS Biol). Previous work from the authors show that Casc3 (Btz) is not necessary for EJC function in pre-mRNA splicing (Roignant et al, 2010 Cell). Further, there exists a population of Casc3 lacking EJCs in human cells (Mabin et al 2018 Cell Reports). Collectively, all this evidence points to Casc3 not being a core EJC subunit. *

• *

We will change the text so that we do not refer to Btz/Casc3 as a core subunit.

• • "In the mouse brain, haploinsufficiency for Magoh, Rbm8a or Eif4a3 causes severe microcephaly, but complete loss of Casc3 has a much milder effect that can be attributed to developmental delay (Mao et al., 2017; Mao et al., 2016; Mao et al., 2015; Silver et al., 2010)."

  From Mao et al 2017: complete loss and hypomorphic mutants were embryonic and perinatally lethal (contrary to what the authors are stating here), while compound mutants and heterozygotes exhibited neurodevelopmental delay. By "milder effects" the authors could also be referring to brain size being proportional to body size in the complete loss homozygotes; either way, this should be clarified. *

• *

    By “milder effects” we meant the effect on brain size. We will clarify this in the revised text.
  

Fly-specific nomenclature could be made more accessible to a broader audience, as the full readership will likely not have expertise in Drosophila genetics. For example, w118, btz2 labels used in figures are not explained anywhere in the manuscript. While the authors do a good job of describing various mutants in a more accessible fashion in the results section, the genotype labels in figures can be better explained in the legends.

We apologize for this and will clarify the genotype labels in the figure legends.

Fig 2 L-N panels might warrant more explanation. Can the mitochondria be counted here? Is there also a difference in volume/morphology that could be quantitated? In Figure 2N, muscle fibers are more densely packed in mutant vs. control; can this be explained?

• *

We are hesitant to quantify mitochondria or comment on muscle fiber packing based on the EM images, because only one individual of each genotype was examined. We prefer to simply use these images to provide a higher resolution view of the change in mitochondrial distribution that we observed and quantified using light microscopy. However, we do plan to do a Western blot to determine whether there are changes in the number of mitochondria in btz mutants (see Reviewer 1 point 2).

In Fig 2, to draw parallels between panels A-K and L-N, it might also be helpful to use the red/yellow arrow system on panel A for comparison.

This is a good suggestion that we will follow.

In Figure 3, it might be helpful for a general audience to include zoomed-in picture of boutons (as in Fig 5B), as some panels appear to have less defined bouton shape.

• *

We do observe that boutons tend to be less well separated from each other in btz mutants, and will include zoomed-in pictures to document this.

Is the bouton size different in the mutant in Figure 3? Can this be quantified?

We do not think that there is a significant difference in bouton size in btz mutants, but we will measure this and include a quantification.

Fold changes are modest and not very apparent in staining (we acknowledge that this could be due to early developmental time point). Images could better point out differences in WT vs. mutant that are not readily apparent to those outside the fly neurodevelopment audience.

Because of the inherent variability in synapse shape, it can be difficult to appreciate changes in bouton number from a single image. However, our quantifications show that the changes are consistent and significant.

Fig 4 NMJs are shown on different scale (more zoomed in) than in Figure 3, and differences are bit easier to see at this scale. Presenting Fig 3 on this scale might help the reader with visualizing the differences in WT versus mutant.

• *

We will crop the images in Figure 3 so as to show them at the same scale as in Figure 4.

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Referee #2

Evidence, reproducibility and clarity

Summary

Ho et al. describes the developmental functions of the Drosophila Casc3 ortholog, Barentsz (Btz) using in vivo loss-of-function and rescue experiments in Drosophila larvae. In this study, the authors find that loss of Casc3 contributes to neuromuscular defects in the larval fly. Utilizing transgenics of WT and EJC interaction-defective mutants, they demonstrate that Btz has both EJC-dependent and independent functions in the larval neuromuscular junction, wherein muscle defects are EJC dependent and synaptic defects are EJC-independent. Using RNA-seq, they find that upregulated mRNAs include those that belong to the Activin signaling pathway. They go on to find that the neuromuscular defects in Btz mutants can be attributed to dysregulation of Activin signaling, and are rescued with loss of the Activin ligand, Dawdle (Daw).

Major Comments

Overall, the paper presents well-controlled experiments that support the main conclusions. We propose achievable validation experiments that we believe will strengthen the conclusions of the paper. There is some concern that the magnitude of the effects are overstated, or could be made more apparent to a broader audience (i.e. those in the mRNA regulation field beyond Drosophila geneticists).

• In Figure 1, regarding the validation of rescue constructs: the EJC interaction-defective mutant is based solely on conservation, as all structural/interaction studies cited with Btz bound to EJC have been with human proteins. They use Vasa localization as a readout of EJC-dependent function, but this is indirect and only assesses one aspect of EJC function (localization). Since many of the main conclusions in the paper are predicated on this mutant being EJC-independent, they should validate this with the Drosophila orthologs using immunoprecipitation. They demonstrate the capability of expressing GFP-tagged versions of Casc3 WT and mutant in S2 cells, so this should not be a cumbersome control experiment to include.

• Regarding Figure 3, it could be postulated that the number of boutons would be influenced by the length of axons. Is axon outgrowth accounted for in these experiments? This would influence number of synaptic boutons. Panel F looks very different from panel A in terms of axon length (could this be due to axon outgrowth defect and/or impacted muscle size?) Can quantitation be done also by normalizing to axon length (bouton number/axon length)? Or perhaps this is accounted for in muscle size? If so, this should be explained.

• In Figure 3 quantification: n's vary between genotypes significantly, and this should be explained (e.g. was there a recovery issue between genotypes or just fewer needed for WT-like?).

• In Figure 4 panels B and F (mutants), there appears to be reduced axon outgrowth (see point above). This should be taken into account when expressing bouton number.

• The RNA-seq data (Figure 5) has a potential issue in that they used larvae with a balancer chromosome (Df), which yields a 50% reduction in any genes on that chromosome. They acknowledge this and removed these genes from the analysis, but the concern remains that this still might be a confounding variable (for example, if reduction in any of these genes might disrupt a signaling pathway). We do not think that the RNA-seq needs to be repeated, but we propose that the authors validate these targets using qPCR in their MN-specific btz knockdown system (this way, they can also include magoh and eif4aIII knockdowns for comparison).

Minor comments

Some statements made in the introduction that are not entirely accurate:

• "A fourth core subunit, known as Barentsz (Btz), Cancer susceptibility candidate gene 3 (CASC3), or Metastatic lymph node 51 (MLN51), associates with the complex following the completion of splicing, and is required for the effects of the EJC on translation, NMD and mRNA localization (Chazal et al., 2013; Palacios et al., 2004; Shibuya et al., 2006; van Eeden et al., 2001)."

A recent study indicates that Casc3 is not required for EJC-dependent NMD targets in human cells, but rather enhances NMD on a subset of targets (Gerbracht et al. 2020 NAR). Perhaps "is required" should be changed to "plays a role in cytoplasmic EJC-mediated processes, such as...". It has also been shown that EJC core can assemble without Casc3 (e.g. Ballut et al 2005 NSMB, Gehring et al 2009 PLoS Biol). Previous work from the authors show that Casc3 (Btz) is not necessary for EJC function in pre-mRNA splicing (Roignant et al, 2010 Cell). Further, there exists a population of Casc3 lacking EJCs in human cells (Mabin et al 2018 Cell Reports). Collectively, all this evidence points to Casc3 not being a core EJC subunit.

• "In the mouse brain, haploinsufficiency for Magoh, Rbm8a or Eif4a3 causes severe microcephaly, but complete loss of Casc3 has a much milder effect that can be attributed to developmental delay (Mao et al., 2017; Mao et al., 2016; Mao et al., 2015; Silver et al., 2010)."

From Mao et al 2017: complete loss and hypomorphic mutants were embryonic and perinatally lethal (contrary to what the authors are stating here), while compound mutants and heterozygotes exhibited neurodevelopmental delay. By "milder effects" the authors could also be referring to brain size being proportional to body size in the complete loss homozygotes; either way, this should be clarified.

General minor comments:

• Fly-specific nomenclature could be made more accessible to a broader audience, as the full readership will likely not have expertise in Drosophila genetics. For example, w118, btz2 labels used in figures are not explained anywhere in the manuscript. While the authors do a good job of describing various mutants in a more accessible fashion in the results section, the genotype labels in figures can be better explained in the legends.

• Fig 2 L-N panels might warrant more explanation. Can the mitochondria be counted here? Is there also a difference in volume/morphology that could be quantitated? In Figure 2N, muscle fibers are more densely packed in mutant vs. control; can this be explained?

• In Fig 2, to draw parallels between panels A-K and L-N, it might also be helpful to use the red/yellow arrow system on panel A for comparison.

• In Figure 3, it might be helpful for a general audience to include zoomed-in picture of boutons (as in Fig 5B), as some panels appear to have less defined bouton shape.

• Is the bouton size different in the mutant in Figure 3? Can this be quantified?

• Fold changes are modest and not very apparent in staining (we acknowledge that this could be due to early developmental time point). Images could better point out differences in WT vs. mutant that are not readily apparent to those outside the fly neurodevelopment audience.

• Fig 4 NMJs are shown on different scale (more zoomed in) than in Figure 3, and differences are bit easier to see at this scale. Presenting Fig 3 on this scale might help the reader with visualizing the differences in WT versus mutant.

Significance

Overall, this paper contributes conceptually to understanding EJC-mediated mRNA regulation during development. The contribution here is incremental, but meaningful in terms of defining the scope of regulation by the EJC and its peripheral factors in various contexts. These findings will likely be of interest to the fields of RNA metabolism and neurodevelopment. It also adds to the existing work suggesting Casc3 may have additional functions outside of the EJC (e.g. Mao et al. 2017 RNA, Baguet et al 2007 J Cell Sci, Cougot et al. 2014 J Cell Sci); while these previous studies have suggested Casc3 roles in development and mRNA localization/granule formation that are different from the EJC core proteins, this study more directly tests an EJC-independent role in mRNA regulation of specific targets. Further addressing the molecular basis of this regulation will be outside the scope of this article but will be of interest to the field.

We are molecular biologists who study NMD and are thus equipped to address the EJC-related molecular functions and impact on the transcriptome. We do not have expertise in Drosophila genetics or neurobiology, and thus cannot critically evaluate the specific genetic approaches used or anatomy presented to the full extent. We have, however, pointed out areas that need elaboration regarding the genetic approaches and/or presentation of data that may be unfamiliar to a broader audience (i.e. the RNA metabolism field).

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Referee #1

Evidence, reproducibility and clarity

The Ho et al. manuscript defines developmental functions for Barentsz (Btz), a core subunit of the EJC. While other EJC components, such as eIF4AIII, have been shown to have EJC-independent functions, it has not been clear whether Btz also acted independently of this multi-protein complex. The authors make use of two Btz genomic constructs, a wild-type transgene (Btz-WT) and a transgene carrying mutations in the two eIF4AIII-interacting residues (Btz-HD) to rigorously whether or not Btz has any functions independent of the EJC. Interestingly, they show that while Btz-HD does not rescue Btz functions in the ovary or the muscle, it does rescue Btz functions at the larval NMJ. They back up the conclusion that Btz activity at the NMJ is independent of the EJC by showing that the growth phenotype observed in Btz mutants is not shared by mutants in other EJC components. How does Btz regulate NMJ development? The authors performed an RNAseq experiment and found that several components of an Activin/TGFB pathway. Strikingly, they find that Activin overexpression rescues the NM phenotype in Btz mutants, consistent with its identification in the RNAseq analysis.

This is a very logical and well-constructed paper. The results are well-controlled and convincing. Overall, the manuscript was a delight to read and makes an important contribution to dissecting the function of RNA-binding/associated proteins in neuronal development. I have only a few comments that could be considered prior to publication.

Minor comments:

1. In Fig. 1, the authors show that Btz-WT, but not Btz-HD, localizes to the posterior pole of the oocyte. Do the authors see Btz-WT and/or Btz-HD localized to MNs/muscles/glia at the NMJ?
2. The mitochondrial phenotypes observed in Btz mutants are striking. But it seems possible that there are defects in overall mitochondrial levels in muscle in addition to defects in their localization. Overall, mitochondrial levels seemed reduced in Btz mutants. Is it possible to do a ATP5A immunoblot in Btz mutants to test whether overall mitochondrial levels are altered?
3. ECM proteins are known to be critical for regulating TGFB signaling. That, taken with the multi-tissue genetic requirement for Btz, suggests that Btz might directly regulate either Ltl or Frac RNA, given that these ECM proteins are likely deposited by multiple cell types.

Significance

This paper establishes novel functions for the EJC complex protein Btz, and also delineates which functions depend on the EJC and which are independent. This is significant because there is intense interest in how post transcriptional regulation contributes to neuronal development. The paper fits with a body of literature dissecting neuronal functions for EJC proteins. It represents an important addition to this body of work.

The audience will be molecular neuroscientists, especially those with interests in novel genetic regulatory mechanisms.

My expertise is in developmental genetics and molecular neurobiology.

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Reviewer #1

1. One key citation missing from the current manuscript is from Hwang et al. 2014 (PMID 25288734). This study has already described that the isp-1 mutant strain survives longer during P. aeruginosa infection. This citation also describes that the gene expression profile of isp-1 mutants animals includes a considerable number of pathogen-responsive genes that are similarly induced during infection. While the current manuscript does go into the mechanism of this resistance with more detail, they should amend the language to more appropriately reflect previous work, notably the above reference.

We apologize for the oversight and have added the suggested citation. Hwang et al. show that isp-1 worms have increased resistance to bacterial pathogens that is dependent on HIF-1/HIF1 and AAK- 2/AMPK. In future work, it will be interesting to examine whether HIF-1 and AAK-2 act in concert with, or independently of, ATFS-1 and the p38-mediated innate immune signaling pathway to mediate pathogen resistance and longevity in isp-1 worms. We will add these points to our discussion.

1. The authors suggest that ROS activation of the p38 MAPK pathway is likely not the mechanism that explains the resistance of long-lived mitochondrial mutant animals due to their reduced food intake. However, is ROS production nonetheless involved? Does antioxidant treatment suppress the increased resistance during infection of isp-1 and/or nuo-6 mutant animals?

To address this question, we will treat wild-type, isp-1 and nuo-6 worms with antioxidant and then measure resistance to bacterial pathogens using the P. aeruginosa strain PA14 slow kill assay. For the antioxidant treatment, we will use 10 mM Vitamin C as we have previously shown that this concentration is effective at reducing ROS in isp-1 worms to decrease isp-1 lifespan (Van Raamsdonk and Hekimi 2012, PNAS). Although antioxidant treatment can have pleiotropic effects, if this decreases survival of bacterial pathogen exposure, it will suggest that the elevated ROS production in isp-1 and

nuo-6 worms may contribute to their enhanced bacterial pathogen resistance.

1. (line 278-282): the authors should elaborate on how the p38 MAPK pathway plays a permissive role. It is intriguing that ATFS-1 and ATF-7 are both bZIP transcription factors that could theoretically heterodimerize and that they share common immune gene targets. The authors do indicate that the binding sites for ATFS-1 and ATF-7 are very different and are likely acting distinctly but some speculation would nonetheless strengthen this statement.

While ATFS-1 and ATF-7 were shown to bind to the promoter regions of the same innate immunity genes, the apparent consensus binding sites are different suggesting that they bind to different regions of the promoter. One way in which the p38 MAPK pathway may be playing a permissive role is that ATF- 7 binding and relief from its repressor activity is required for any transcription of p38-mediated innate immunity target genes to occur. This is consistent with our data showing that disruption of nsy-1, sek-1, pmk-1 or atf-7 decreases the expression of innate immunity genes in wild-type worms. In contrast, it may be that the role of ATFS-1 is for enhanced expression of innate immunity genes such that when ATFS-1 is bound to the promoter region, or perhaps enhancer elements, the baseline expression of innate immunity genes that results from the binding of ATF-7 is increased. This idea is supported by our data showing that disruption of atfs-1 does not affect the expression of innate immunity genes in wild- type worms but prevents nuo-6 mutants from having increased expression. We will update our manuscript to include these points.

1. The authors suggest that reduced food consumption of nuo-6 and isp-1 animals may suppress ROS- induced activation of the p38 innate immune pathway. It is intriguing that dietary restriction was previously shown to increase resistance to infection, presumably through p38-independent mechanisms (PMID 30905669). It would be interesting to measure host survival of nuo-6 and isp-1 mutant animals that are dietary-restricted to see if the enhanced survival rates conferred by mitochondrial stress and DR are additive or not.

According to this suggestion, we will compare the bacterial pathogen resistance of wild-type, isp-1 and nuo-6 worms that have undergone dietary restriction to the same strains under ad libitum conditions. This will determine the extent to which their enhancement of pathogen resistance might be additive.

1. Figure 2: It is intriguing that loss of p38 signaling appears to have different effects in nuo-6 versus isp-1 animals. Specifically, loss of p38 signaling in isp-1 mutants renders them more sensitive to infection than wild-type, whereas it generally suppresses survival rates back to wild-type levels in the nuo-6 mutant background. Even within the nuo-6 mutant group, loss of SEK-1 has more dramatic effects on nuo-6 mutant animals than does loss of NSY-1, PMK-1 or ATF-7(gf). This is despite the fact that the nsy-1, sek-1, and pmk-1 alleles that are used in this study are all reported to be null. Can the authors speculate on these differences?

While the isp-1 and nuo-6 mutations both alter mitochondrial function, they affect different components of the electron transport chain. isp-1 mutations affect Complex III (Feng et al. 2001, Dev. Cell), while nuo-6 mutations affect Complex I (Yang and Hekimi 2010, Aging Cell). Although these mutants both have increased lifespan and a similar slowing of physiologic rates, it is not uncommon to observe differences between these mutants. For example, while treatment with the antioxidant NAC completely reverts nuo-6 lifespan to wild-type, it only partially reduces isp-1 lifespan (Yang and Hekimi 2010, PLoS Biology), suggesting that nuo-6 lifespan may be more dependent on ROS than isp-1. We have recently shown that deletion of atfs-1 reduces nuo-6 lifespan, but completely prevents isp-1 worms from developing to adulthood (Wu et al. 2018, BMC Biology), suggesting that isp-1 worms are more dependent on ATFS-1 than nuo-6 worms. Disruption of sek-1 has a greater impact on pathogen resistance than nsy-1 and pmk-1 because SEK-1 is absolutely required for innate immune signaling, while some partial redundancy exists for NSY-1 and PMK-1. We will add these points to our manuscript.

1. One of the main conclusions from this study is that ATFS-1 likely binds directly to innate immune genes that are in common with ATF-7. Since this is such a pivotal finding, the authors should validate some candidate genes from the referenced ChIP seq datasets using ChIP qPCR. Also, are there predicted ATFS-1 binding sites (PMID 25773600) in these promoters?

Our data shows that activation of ATFS-1 increases the expression of innate immunity genes without increasing activation of p38. The simplest explanation for this observation is that ATFS-1 can upregulate the same innate immunity genes as ATF-7. Accordingly, we hypothesized that ATFS-1 and ATF-7 can bind to the same promoter. Fortunately, two previous ChIP-Seq studies, from well-established laboratories who have extensive experience studying ATFS-1 and ATF-7, had already determined which genes are bound by these two transcription factors (Nargund et al. 2015, Molecular Cell; Fletcher et al. 2019, PLoS Genetics). Comparing the results of these two published studies confirmed our hypothesis by demonstrating that the same innate immunity genes are bound by both ATF-7 and ATFS-1 in vivo. In order to provide additional support for the conclusion that ATFS-1 and ATF-7 can bind to the same genes, we will examine the genetic sequence of innate immunity genes that were shown to be bound by both ATFS-1 and ATF-7 in the published ChIP-seq studies to identify predicted binding sites for ATFS-1 and ATF-7, while noting that the ATFS-1-associated sequence is an enriched motif and not an established binding site. If we are able to identify the predicted binding sites for these two transcription factors in the same gene, it will provide further support for the conclusion that these transcription factors can both bind to the same innate immunity genes.

Reviewer #2

1. The authors state that the p38 MAPK PMK-1 is not activated in the long-lived mitochondrial mutants. However, it might be better to state that there is "no enhanced activation" of PMK-1, since they clearly show in nuo-6 and isp-1 mutants the presence of phosphorylated PMK-1 (Fig. 4A), which would indicate an activated form of PMK-1 in these mutants.**

According to this suggestion, we will change the text to indicate that there is no enhanced activation of PMK-1 in nuo-6 and isp-1 worms.

1. Are the food-intake behaviors of all mutants in liquid culture (Fig. 4B-F) the same as their food- intake behaviors on solid agar media, the environment where pathogen resistance was measured?

We previously compared assays measuring food intake on solid agar media versus the liquid culture approach used in the current study to determine which method is the most robust (Wu et al. 2019, Cell Metabolism). While both assays produced similar results, performing the food intake assay on solid agar plates was much more variable as it is challenging to scrape off all of the uneaten bacteria from solid plates in order to measure it. Since the approach of measuring food intake in liquid media produces more consistent and reliable results, we chose to use this assay for the current study. We will update our manuscript to include this justification.

1. Does the p38 pathway single mutant nsy-1 or sek-1 live shorter than wild type on dead E. coli OP50 (Fig. S9) than they do on live OP50 (Fig. 3)? If so, what might that mean? These mutants are also living shorter than wild type on PA14 (Fig. 2), but live as long as wild type on OP50 (Fig. 3). What is in the live OP50 that allows these mutants to live like wild type?

In a previous publication, we found that sek-1 mutants live shorter than wild-type worms, and nsy-1 live slightly shorter than wild-type worms in a lifespan assay performed in liquid medium with dead OP50 bacteria (Wu et al. 2019, Cell Metabolism). In the current study, we performed lifespan assays on solid NGM plates with live OP50 bacteria and observed a wild-type lifespan in sek-1 and nsy-1 worms. Since there are multiple experimental variables that are different between the previous and current study, most notably liquid versus solid media, the lifespan results cannot be directly compared. In the case of measuring survival of these strains on PA14, the simplest explanation is that they are dying sooner because their innate immune signaling pathway is disrupted, and so they are less able to mount an immune response against the pathogenic bacteria. We will update our manuscript to include these points.

At the same time, wouldn't it be simpler to call the multiple antibiotic-treated OP50 as "dead bacteria", instead of "non-proliferating bacteria"? Some of the antibiotics used to treat OP50 are bactericidal and not bacteriostatic.

We previously monitored the OD600 of the antibiotic-treated, cold-treated OP50 that we used in our experiment, and found that there is only a very small decrease in OD600 after 10 days (Moroz et al. 2014, Aging Cell). Since dead bacteria are rapidly broken down leading to a decrease in OD600, this result is consistent with the bacteria being alive but not proliferating. We will include this point in our manuscript.

1. Since nuo-6 and isp-1 do not always behave exactly the same in their dependence on certain genes (e.g., Fig. 2C vs Fig 2D), what happens in isp-1; atfs-1 double mutants? Do these mutants behave in the same manner as nuo-6; atfs-1?

This is an interesting question. Unfortunately, isp-1;atfs-1 mutants arrest during development (Wu et al. 2018, BMC Biology), which is why we only examined the effect of atfs-1 deletion in nuo-6 mutants. We will update the manuscript to note this point.

Regarding nuo-6; atfs-1, why does the double mutant live shorter on PA14 than either single mutant (Fig. 6A)? Is this because atfs-1 is needed to activate the p38 MAPK-dependent and -independent pathways?

It is possible that the nuo-6 mutation makes worms more sensitive to bacterial pathogens, perhaps due to decreased energy production, and that activation of ATFS-1 is required not only to enhance their resistance to pathogens but also to increase their resistance back to wild-type levels. In a previous study, we showed that loss of ATFS-1 slows down the rate of nuclear localization of DAF-16. Thus, loss of atfs-1 may also be decreasing resistance to bacterial pathogens by diminishing the general stress resistance imparted by the DAF-16-mediated stress response pathway. We will update the manuscript to include these points.

In Fig. 7B, the atfs-1(gof) appears to have slightly more phosphorylated p38 compared to wild type, although it is not statistically significant?

While there is a trend towards a very modest increase in phosphorylated p38 in the constitutively-active atfs-1 mutant compared to wild-type, quantification of four biological replicates indicated that the difference is not significant. This result is consistent with the fact that the levels of phosphorylated p38 are not significantly increased in nuo-6 or isp-1 mutants, both of which show activation of ATSF-1. We have provided raw images of all of these Western blots in our supplementals. In addition, we will repeat these Western blots to determine if this difference becomes significant with additional replicates.

In Fig. 6B, the atfs-1 loss-of-function single mutant also increases the expression of Y9C9A.8, but suppresses it in a nuo-6 mutant background? What might that mean?

It is possible that in wild-type animals disruption of atfs-1 causes a compensatory upregulation of specific stress response genes. We have previously shown that deletion of atfs-1 results in upregulation of chaperone genes involved in the cytoplasmic unfolded protein response (hsp-16.11, hsp-16.2; Wu et al. 2018; BMC Biology). Perhaps Y9C9A.8 is acting in a similar way. In nuo-6, the upregulation of Y9C9A.8 is driven by activation of ATFS-1, and thus is prevented by atfs-1 deletion. We will add these points to the manuscript.

Reviewer #3

1. Some studies propose that OP50 offers some toxicity to worms which is not observed in other bacterial strains like HT115. The authors should test the role of the p38-innate immune signaling pathway in nuo-6 and isp-1 lifespan using other non-pathogenic E. coli strains.**

To determine if the effect of disrupting the p38-mediated innate immune signaling pathway on the lifespan of isp-1 and nuo-6 mutants was simply the result of losing protection against OP50 bacteria, we examined the effect of nsy-1, sek-1 and atf-7(gof) mutations on isp-1 and nuo-6 lifespan using non- proliferating bacteria. We found that even when no proliferating bacteria are present, disruption of the p38-mediated innate immune signaling pathway markedly decreases isp-1 and nuo-6 lifespan. This suggests that the p38-mediated innate immune signaling pathway is required for their long lifespan independently of its ability to protect against bacterial infection. Similarly, we have previously shown that lifespan extension resulting from dietary restriction is dependent on the p38-mediated innate immune signaling pathway even when non-proliferating bacteria are used (Wu et al. 2019, Cell Metabolism). We will clarify this important point in the manuscript.

1. The authors should measure food intake in worms exposed to pathogenic bacteria, given that reduced bacterial intake may be related to reduced mortality.

Unfortunately, it is not feasible to perform the food intake assay using the pathogenic bacteria because the bacteria cause death thereby complicating the calculation of food consumed per worm (which requires at least 3 days to assess). As an alternative to measuring food intake, we will attempt to measure intestinal accumulation of P. aeruginosa, which is a balance between food intake and other factors. To do this we will use a P. aeruginosa strain that expresses GFP and quantify the amount of intestinal fluorescence in wild-type, isp-1 and nuo-6 worms that have been grown on the GFP-labelled P. aeruginosa.

1. The authors should check if ROS is required for the activation of the p38-mediated innate immune signaling pathway and reduction in food intake.

To determine if the elevated ROS that is present in isp-1 and nuo-6 worms affects activation of the p38- mediated innate immune signaling pathway, we will treat wild-type, isp-1 and nuo-6 worms with Vitamin C and measure the ratio of phosphorylated p38 to total p38 by Western blotting. Similarly, to examine the effect of ROS on food intake, we will treat wild-type, isp-1 and nuo-6 worms with Vitamin C and then quantify its effect on food intake. For these experiments, we will use 10 mM Vitamin C as we have previously shown that this concentration is effective at reducing ROS in isp-1 worms to decrease isp-1 lifespan (Van Raamsdonk and Hekimi 2012, PNAS).

1. Since ATFS-1 and the p38 pathway control food intake, how related to dietary restriction the phenotypes the authors are studying are?

While the lifespan extension that results from mild impairment of mitochondrial function and the lifespan extension resulting from dietary restriction are both dependent on the p38-mediated innate immune signaling pathway, these interventions modulate innate immunity gene expression in opposite directions. We previously reported that dietary restriction primarily downregulates innate immunity genes (Wu et al. 2019 Cell Metabolism). Here, we show that mutations in isp-1 or nuo-6 primarily result in upregulation of innate immunity genes. To more globally examine gene expression changes between dietary restriction and mild impairment of mitochondrial function, we compared differentially expressed genes. We found that there was very little overlap of either upregulated or downregulated genes between dietary restriction and isp-1/nuo-6 mutants. We will add a supplementary figure to demonstrate this, and add these points to our manuscript.

1. Somewhat related to the previous points, I am not so sure whether the changes in food intake are cause or consequence of the alterations in the innate immunity-related genes. Reduced food intake is depicted in Fig. 8 as the cause of the activation of the p38 pathway, but there is not enough evidence to unequivocally prove that. In fact, food intake might be controlled by the p38 or ATFS-1 pathway or by a common regulator such as ROS.

We apologize that we didn’t make this clearer. In our previous work, we showed that dietary restriction results in decreased activation of the p38 pathway (Wu et al. 2019, Cell Metabolism). Here, we show that activation of ATFS-1 results in decreased food intake. Based on our previous study, this decrease in food intake should similarly decrease p38 pathway activation. In Figure 8, we have depicted ATFS-1 inhibiting food intake, and food intake activating the p38-mediated innate immune signaling pathway. Combined, our model suggests that activation of ATFS-1 should act to decrease p38-mediated innate immune signaling. We will clarify this in the figure legend.

1. I am not so convinced of the role of DAF-16. In fact, in Fig. 5A daf-16 mutation reduces pathogen resistance and that could represent a toxic effect of the mutation. Furthermore, the results in Fig. 4D do not exclude the possibility that daf-16 and isp-1 act in parallel.

We agree that the role of DAF-16 could be non-specific. While we show that disruption of daf-16 leads to decreased bacterial pathogen survival in isp-1 worms, it also decreases bacterial pathogen survival in wild-type worms. Since DAF-16 is known to be required for general resistance to stress, the decreased survival when daf-16 is disrupted could be due to a general toxic effect of reducing general stress resistance. This conclusion is consistent with our observation that DAF-16 is not involved in the upregulation of innate immunity genes in isp-1 worms. We will emphasize these points in our manuscript.

1. Loss of innate immunity related genes may result in toxicity and sensitize worms to pathogenic bacteria. This is further supported by an even lower resistance to pathogens in the double mutants mainly in Fig. 2D.

We agree. Our data confirms that disruption of the p38-mediated innate immune signaling pathway makes worms more susceptible to bacterial pathogens. We will emphasize this point.

1. The blots are saturated, particularly in Fig. 4A, and this can be masking the differences in p38 phosphorylation. In fact, the fact that p38 phosphorylation is not changed is contradictory to the other results. How is p38 regulated by mitochondrial mutations then? I am concerned that p38 is actually not altered and the changes in gene expression are exclusively due to ATFS-1. The interaction with the p38 pathway demonstrated genetically could be due to the toxicity elicited by the loss of function mutations in this pathway.

To address this concern, we will repeat the Western blotting experiment to compare the ratio of phosphorylated p38 to total p38 between wild-type, isp-1 and nuo-6 worms. We will take multiple exposures to ensure that the blots are not over-saturated. Having already completed four replicates, we believe that there is not a major change in p38 activation. Our data suggests that the p38-mediated innate immunity pathway is playing a permissive role such that it is required for baseline expression of innate immunity genes, but that activation of ATFS-1 is driving the enhanced expression of innate immunity genes that we observe in the long-lived mitochondrial mutants and constitutively active atfs-1 mutants. We will update our manuscript to clarify this.

Minor concerns

1. Lines 167 and 174: What are these p values referred to?**

The p-values indicate the significance of the overlap between the two gene sets. Given the size of the two gene sets, this is the probability that the observed number of overlapping genes would result by picking genes at random. We will clarify this in the manuscript.

1. Line 258: I partially agree with the conclusions, since the functions may not necessarily be associated with innate immune signaling but rather other functions of p38.

Since isp-1 and nuo-6 worms have extended longevity even when grown on non-proliferating bacteria this indicates that their long life is not dependent on their enhanced resistance to bacterial pathogens. Similarly, since disruption of genes in the p38-mediated innate immune signaling pathway decrease isp- 1 and nuo-6 lifespan even when the worms are grown on non-proliferating bacteria, this suggests that this pathway enhances longevity independently of its ability to increase innate immunity.

1. Why in figures 4D and E different mutants were used?

We only used isp-1 mutants to examine the effect of daf-16 because we were unable to generate nuo- 6;daf-16 mutants due to close proximity of the two genes on the same chromosome. We only used nuo- 6 mutants to examine the effect of atfs-1 because isp-1;atfs-1 worms arrest during development. We will include this explanation in our manuscript.

1. Line 498: revise writing.

We will rewrite this sentence to improve clarity.

1. Show blots in Fig. 7B.

We will provide an image of a representative Western blot in Figure 7, and will provide the raw images for all of Western blots in our supplementals.

1. It would be interesting to know where the activation of the immune-related genes by the mitochondrial mutations is happening, whether this is a cell autonomous or cell non-autonomous mechanism.

While it would be interesting to explore whether specific tissues are important in sensing mitochondrial impairment in order to upregulate genes involved in innate immunity, it is beyond the scope of this manuscript. Previous work has shown that knocking down the expression of the cytochrome c oxidase gene cco-1 in neurons can activate the ATFS-1 target gene hsp-6 in the intestine (Durieux et al., 2011). Based on this, one could hypothesize that a similar cell non-autonomous mechanism might be involved. We will note this possible future direction in our discussion.

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Referee #3

Evidence, reproducibility and clarity

Campos et al provide evidence that mild mitochondrial dysfunction in C. elegans induces genes involved in innate immunity and promotes bacterial pathogen resistance and longevity, while inhibits food intake through an ATFS-1-mediated mechanism. The manuscript is well-written and the experiments are well-performed and reported. However, there are several points that need to be addressed before the manuscript can be published.

Major concerns

1. Some studies propose that OP50 offers some toxicity to worms which is not observed in other bacterial strains like HT115. The authors should test the role of the p38-innate immune signaling pathway in nuo-6 and isp-1 lifespan using other non-pathogenic E. coli strains.
2. The authors should measure food intake in worms exposed to pathogenic bacteria, given that reduced bacterial intake may be related to reduced mortality.
3. The authors should check if ROS is required for the activation of the p38-mediated innate immune signaling pathway and reduction in food intake.
4. Since ATFS-1 and the p38 pathway control food intake, how related to dietary restriction the phenotypes the authors are studying are?
5. Somewhat related to the previous points, I am not so sure whether the changes in food intake are cause or consequence of the alterations in the innate immunity-related genes. Reduced food intake is depicted in Fig. 8 as the cause of the activation of the p38 pathway, but there is not enough evidence to unequivocally prove that. In fact, food intake might be controlled by the p38 or ATFS-1 pathway or by a common regulator such as ROS.
6. I am not so convinced of the role of DAF-16. In fact, in Fig. 5A daf-16 mutation reduces pathogen resistance and that could represent a toxic effect of the mutation. Furthermore, the results in Fig. 4D do not exclude the possibility that daf-16 and isp-1 act in parallel.
7. Loss of innate immunity related genes may result in toxicity and sensitize worms to pathogenic bacteria. This is further supported by an even lower resistance to pathogens in the double mutants mainly in Fig. 2D.
8. The blots are saturated, particularly in Fig. 4A, and this can be masking the differences in p38 phosphorylation. In fact, the fact that p38 phosphorylation is not changed is contradictory to the other results. How is p38 regulated by mitochondrial mutations then? I am concerned that p38 is actually not altered and the changes in gene expression are exclusively due to ATFS-1. The interaction with the p38 pathway demonstrated genetically could be due to the toxicity elicited by the loss of function mutations in this pathway.

Minor concerns

1. Lines 167 and 174: What are these p values referred to?
2. Line 258: I partially agree with the conclusions, since the functions may not necessarily be associated with innate immune signaling but rather other functions of p38.
3. Why in figures 4D and E different mutants were used?
4. Line 498: revise writing.
5. Show blots in Fig. 7B.
6. It would be interesting to know where the activation of the immune-related genes by the mitochondrial mutations is happening, whether this is a cell autonomous or cell non-autonomous mechanism.

Significance

This study provides significant advance in mechanistic aspects of lifespan regulation in worms, linking mitochondrial metabolism, food intake, innate immunity, resistance to pathogen infections and longevity. The work presents novel mechanistic insights that could be applied to understand how mild mitochondrial dysfunction leads to increased lifespan. Overall, the audience interested in this study are expected to be aging biologists and possibly immunologists with particular interest in mechanistic aspects of longevity and innate immunity, as well as C. elegans as a model organism. I am part of this group of scientists with particular interest in studying the interplay between metabolism and aging.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Campos et al. show that mild mitochondrial impairment promotes C. elegans resistance against the bacterial pathogen Pseudomonas aeruginosa PA14, which is associated with increased expression of a subset of innate immunity genes in the animal. Interestingly, upregulation of the innate immunity genes in the mitochondrial electron transport chain mutants, nuo-6 (complex I) and isp-1 (complex III), does not appear to involve enhanced activation of the p38 MAPK PMK-1, which has been previously implicated in anti-bacterial immunity (Jeong et al, EMBO J 2017, 36, 1046). Because the authors also show that this increased pathogen resistance and expression of innate immunity genes in at least one of the mitochondrial mutants (nuo-6) only partly depend on the p38 PMK-1 pathway, this would argue for the involvement of another pathway. The authors show that this other pathway involves the mitochondrial unfolded protein response (mitoUPR) through activation of the transcription factor atfs-1, which not only upregulates a subset of innate immunity genes, but also presumably decreases pathogen intake. Together their data suggest that the p38 PMK-1 pathway and mitoUPR act in parallel to promote the enhanced pathogen resistance of mitochondrial mutants.

Moreover, while they show that the FOXO transcription factor daf-16 is also required for the enhanced pathogen resistance of mitochondrial mutants (i.e,, isp-1), they rule out daf-16 involvement in the activation of innate immunity genes. Instead, daf-16 decreases pathogen intake and upregulates other stress-response genes. Thus, this study highlights the requirement for multiple pathways to promote pathogen resistance through multiple mechanisms.

Major comments:

(1) The authors state that the p38 MAPK PMK-1 is not activated in the long-lived mitochondrial mutants. However, it might be better to state that there is "no enhanced activation" of PMK-1, since they clearly show in nuo-6 and isp-1 mutants the presence of phosphorylated PMK-1 (Fig. 4A), which would indicate an activated form of PMK-1 in these mutants.

(2) Are the food-intake behaviors of all mutants in liquid culture (Fig. 4B-F) the same as their food-intake behaviors on solid agar media, the environment where pathogen resistance was measured?

(3) Does the p38 pathway single mutant nsy-1 or sek-1 live shorter than wild type on dead E. coli OP50 (Fig. S9) than they do on live OP50 (Fig. 3)? If so, what might that mean? These mutants are also living shorter than wild type on PA14 (Fig. 2), but live as long as wild type on OP50 (Fig. 3). What is in the live OP50 that allows these mutants to live like wild type?

At the same time, wouldn't it be simpler to call the multiple antibiotic-treated OP50 as "dead bacteria", instead of "non-proliferating bacteria"? Some of the antibiotics used to treat OP50 are bactericidal and not bacteriostatic.

(4) Since nuo-6 and isp-1 do not always behave exactly the same in their dependence on certain genes (e.g., Fig. 2C vs Fig 2D), what happens in isp-1; atfs-1 double mutants? Do these mutants behave in the same manner as nuo-6; atfs-1?

Regarding nuo-6; atfs-1, why does the double mutant live shorter on PA14 than either single mutant (Fig. 6A)? Is this because atfs-1 is needed to activate the p38 MAPK-dependent and -independent pathways? In Fig. 7B, the atfs-1(gof) appears to have slightly more phosphorylated p38 compared to wild type, although it is not statistically significant?

In Fig. 6B, the atfs-1 loss-of-function single mutant also increases the expression of Y9C9A.8, but suppresses it in a nuo-6 mutant background? What might that mean?

Some of my comments can be easily addressed with written comments. Others might require generation of a strain, like the isp-1; atfs-1 double mutant, prior to any assays.

Significance

Please see the above summary for the significance of this manuscript to the field. Importantly, this study highlights the requirement for multiple pathways to promote pathogen resistance through multiple mechanisms. Readers interested in aging, mitochondrial function, innate immunity and stress responses should find this study thought-provoking. I include myself in this group of readers, since I study the genetics of C. elegans aging and stress responses.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Campos et al. describe the association between long-lived mitochondrial mutants and increased resistance to pathogen infection. The authors discover that mitochondrial electron transport chain mutants (nuo-6 and isp-1) display increased expression of many genes involved in innate immunity that are regulated by the p38 signaling pathway. Consistent with this finding, mito mutants displayed increased survival during infection. p38 signaling was found to be required for these innate immune gene inductions during mitochondrial stress and for their increased survival during infection. P38 signaling was also found to be required for the increased lifespan of isp-1 and nuo-6 mutant animals. Intriguingly, p38 signaling does not appear to be affected in these mitochondrial mutants, despite being required for the increase in immunity/host resistance. The authors discover that mitochondrial stress animals exhibit reduced feeding which they argue may suppress any activation of the p38 pathway caused by ROS. The mitochondrial UPR was also found to be required for the increase in innate immune gene expression in isp-1 and nuo-6 mutant animals, as well as their extended survival. The authors conclude that ATFS-1 can act in parallel to p38 signaling by directly binding to common innate immune target genes. In support of this, ATFS-1 and ATF-7 appear to bind to shared target genes but likely at independent sites due to their different consensus sequences.

1. One general consideration is that some of the key concepts outlined in this manuscript have already been described previously and are therefore not entirely novel conceptually. For example, one key citation missing from the current manuscript is from Hwang et al. 2014 (PMID 25288734). This study has already described that the isp-1 mutant strain survives longer during P. aeruginosa infection. This citation also describes that the gene expression profile of isp-1 mutants animals includes a considerable number of pathogen-responsive genes that are similarly induced during infection. While the current manuscript does go into the mechanism of this resistance with more detail, they should amend the language to more appropriately reflect previous work, notably the above reference.
2. The authors suggest that ROS activation of the p38 MAPK pathway is likely not the mechanism that explains the resistance of long-lived mitochondrial mutant animals due to their reduced food intake. However, is ROS production nonetheless involved? Does antioxidant treatment suppress the increased resistance during infection of isp-1 and/or nuo-6 mutant animals?
3. (line 278-282): the authors should elaborate on how the p38 MAPK pathway plays a permissive role. It is intriguing that ATFS-1 and ATF-7 are both bZIP transcription factors that could theoretically heterodimerize and that they share common immune gene targets. The authors do indicate that the binding sites for ATFS-1 and ATF-7 are very different and are likely acting distinctly but some speculation would nonetheless strengthen this statement.
4. The authors suggest that reduced food consumption of nuo-6 and isp-1 animals may suppress ROS-induced activation of the p38 innate immune pathway. It is intriguing that dietary restriction was previously shown to increase resistance to infection, presumably through p38-independent mechanisms (PMID 30905669). It would be interesting to measure host survival of nuo-6 and isp-1 mutant animals that are dietary-restricted to see if the enhanced survival rates conferred by mitochondrial stress and DR are additive or not.
5. Figure 2: It is intriguing that loss of p38 signaling appears to have different effects in nuo-6 versus isp-1 animals. Specifically, loss of p38 signaling in isp-1 mutants renders them more sensitive to infection than wild-type, whereas it generally suppresses survival rates back to wild-type levels in the nuo-6 mutant background. Even within the nuo-6 mutant group, loss of SEK-1 has more dramatic effects on nuo-6 mutant animals than does loss of NSY-1, PMK-1 or ATF-7(gf). This is despite the fact that the nsy-1, sek-1, and pmk-1 alleles that are used in this study are all reported to be null. Can the authors speculate on these differences?
6. One of the main conclusions from this study is that ATFS-1 likely binds directly to innate immune genes that are in common with ATF-7. Since this is such a pivotal finding, the authors should validate some candidate genes from the referenced ChIP seq datasets using ChIP qPCR. Also, are there predicted ATFS-1 binding sites (PMID 25773600) in these promoters?

Significance

As mentioned in my comments, some of the findings of the current manuscript have been shown before. Nonetheless, the authors do describe new insights into the mechanism of how mitochondrial stress signaling promotes host resistance to infection, which is noteworthy.

This manuscript would be of value to researchers in the fields of mitochondrial biology, mitochondrial stress signaling (including the UPRmt field), host-pathogen interactions, and longevity determination.

My expertise is in stress signaling in the context of longevity and host-pathogen interactions.

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Reviewer #1:

This paper shows that transient genetic induction of the IMD innate immune pathway during Drosophila development, has long term effects on adult health and lifespan. The paper is well-written, the experiments are well designed and executed, and the data are without exception good quality. The data also support the specific conclusions well. The experiments take full advantage of the Drosophila system to pinpoint the effect on lifespan to long term activation of inflammation in the gut, which is interlinked and dependent upon changes in the microbiota. However the analysis is not comprehensive, because neural-specific effects on starvation resistance are not followed up, and because the etiology of the changes in microbiota is not mapped out. I should also say that I do not fully agree with the conclusion in the last sentence of the Abstract (the most important general conclusion), that the study "demonstrates a tissue-specific programming effect" of early transient IMD function. Since the lifespan shortening was shown to be dependent upon increased gut Gluconabacter, I would not call this "programming" (though the term is vague enough to mean most anything.) Instead, I would refer to the effect as a host-environment interaction. If it were "programming" of, for instance, the genetic or epigenetic sort, it would not be so easy to reverse.

Response1-1: We thank the reviewer for the fair evaluation of the manuscript. We agreed with the point of "programming" effect: it might be a bit overstatement. We would like to make our conclusion modest and avoid the ambiguous word in the last sentence of the abstract.

A few other minor comments:

1. Several experiments, the authors use GFP (Fig S1) or the IMD targets DptA or Dro (Fig S2) to validate the induction of IMD-CA. Why have they not directly measured the expression of IMD-CA. This would seem to be logical and technically easy, by qPCR.

Response1-2: We will perform qPCR of Imd gene.

1. In Fig 4 we see and experiment in which animals were "supplemented" with Alkaline Phosphatase, a protein. How was this done and why does it work? Is AP a gut luminal protein?

Response1-3: It is a luminal protein and thus ingestion of the protein works just as endogenous one. This is also proved in the literature (Kühn F et al., JCI insight, 2020). The protein targets, for example, peptidoglycan to attenuate its immuno-stimulative capacity. We will add the explanation in the text.

1. The results in Fig 5 are really where the paper begins to determine a mechanism for the lifespan shortening. However, these results are rather weak, and they don't extend very far. The increase in Gluconobacter is mild (Fig 5C), and is not clear in the 16S rRNA sequencing experiment (Fig 5A). Furthermore, it is not clear that Glunconobacter specifically is the source of the lifespan shortening, of just bacteria in general (Fig 5E).

Response1-4: Why we are focusing on this bacterial genus is because we have already shown in our previous paper that increase of Gluconobacter shortens organismal lifespan (Kosakamoto H et al., Cell Reports, 2020). We also reported that Gluconobacter is increased in response to the (necrosis-induced) immune activation, the situation of which is strikingly similar in the larval IMD activation in the present study. As we proved before, we wanted to perform the gnotobiotic/monoassociation experiment here to show sufficiency of the bacterium for the lifespan-shortening phenotype, however preliminary experiments implied that combining Germ-free with the GeneSwitch system is technically difficult as it caused higher lethality. This might be because the drug RU486 shows a different bioavailability/ dynamics in the GF flies.

Significance:

Although this paper addresses in interesting topic using an elegant and effective experimental strategy, the final results (Fig 5) and conclusions are modest. The analysis doesn't extend far enough to demonstrate how long term changes in microbiota arise from short term developmental changes in innate immune activity. Moreover, there is no detailed data concerning how the altered microbiota alter lifespan. Thus, while the results are interesting and the findings open avenues for further studies on the topic, the significance of the paper is modest, in its current state. Further analysis of how the microbiota is permanently changed, and why this affects lifespan, could enhance the paper. However, it is not clear that any simple, quick experiments could dramatically advance the findings from where they are now.

Response1-5: We would like to add the data that IMD activation in the larvae increased the Gluconobacter already in the larval gut. This data mechanistically suggests that microbiome alteration in the larval gut persists into adulthood, demonstrating how larval immune signalling influences adult immune activity. This data should strengthen a concept that even a transient and mild immune activation in juvenile stage can mess up the microbiota and permanently trigger the inflammatory pathology.

Reviewer #2:

In this manuscript, the authors study the impact of ubiquitously activating the IMD pathway only during larval stages on subsequent adult life. They report a shortened lifespan due to IMD pathway activation in the larval gut and a resistance to starvation linked to its activation in the nervous system. While there is apparently no activation of the IMD pathway in very young adult flies, the expression of some IMD-dependent antimicrobial peptide (AMP) genes is reported from 7-10 flies onwards. This expression is lost upon treating the adults with antibiotics, which also rescues the shortened lifespan phenotype. It correlates with a possible increase in the proportion of Gluconobacter in the microbiota.

While the study looks interesting, it is not clear whether the results, especially those of survival studies and RTqPCR experiments, have been replicated in independent experiments. This is essential to warrant their conclusions. In this respect, this reviewer notes some important variability in the lifespan studies (e.g., Fig. 2B vs. Fig. 4E): how do the authors account for a lifespan that is shortened almost by half in Fig. 4E? Also, Fig. S2B is not convincing given the observed variability. More data points are required to reach a conclusion.

Response2-1: We would like to mention that all experiments have been replicated at least twice. We admit that the phenotypes of larval IMD activation such as lifespan shortening effect and inflammatory response in adult gut are indeed quite variable, empirically depending on seasons. This is not surprising to us since many immune-metabolic phenotypes as well as lifespan of the flies are variable between seasons. We assume that this would imply that the effect is through gut microbiota. In Japan, we have a typical seasonal change in the temperature/ humidity that greatly influences gut microbial situation, even though we use an incubator which allows constant temperature/humidity setting. It is therefore we need to carefully compare the phenotype of flies in the same experiment, and this is where the GeneSwitch works effectively.

Regarding Fig. S2B, we could increase the number of samples in Fig. S2B in new experiment.

The authors suggest in their Discussion some kind of epigenetic mechanism transmitting the information of IMD pathway activation having occurred at larval stages. Whether this depends on a change of metabolism remains to be demonstrated, in as much it is likely that there is a major metabolic "reset" occurring during metamorphosis to prepare the individual to the new environmental conditions encountered as an adult. It is also likely that larvae in the wild grow in a microbe-rich slurry and are likely to experience intestinal infections. As noted by the authors themselves on the top paragraph of p7 (line numbers are unreadable), the larval gut is degenerated during metamorphosis and thus the enterocytes that have produced AMPs are no longer present. One possibility would be that there is an early dysbiosis already occurring during larval stages and that the young adults re-infect themselves, for instance through contact with the meconium. The authors' experiments with antibiotics are the key to this study. However, one would like to observe results of the converse experiment, that is, treating larvae with antibiotics (a better control would be to bleach the embryos to generate axenic flies) and then raising the hatched adult flies in a conventional manner. In this way, the authors may determine whether the influence of early IMD pathway activation occurs through "self" mechanisms or whether it entails a contribution from the microbiota. It might also be useful to use reporter transgenes such as Dpt-LacZ to document where in the gut IMD activation takes place in the adult and to monitor whether there is any weak signal that would not be picked up by RTqPCR in newly hatched flies.

Response2-2: We highly appreciate the reviewer for pointing out this important caution. We now checked the dysbiosis in the larval gut (by qPCR of Gluconobacter) and found that it is increased already. For detail, please see our response1-4/1-5. This would strikingly improve the study.

Regarding monitoring IMD activation by the reporter, we plan to do this experiment in our next project. Obviously, a remained question is how epigenetic mechanism in a particular cell/locus mediates the phenotype. This is our next goal and thus lies beyond the scope of this paper.

Specific comments

1. The GS system used in this study requires multiple controls, as a study from the Serroude laboratory has reported a driver-dependent leakiness of expression independent of exposure to RU486 (Poirier et al., Aging Cell, 2008). Thus, it would be good to check this with a cross to a UAS-GFP driver and examining the 10 and 40-day time points. The same should be done with antibiotics-treated flies as regards DptA and Drosocin expression (Fig. 5C &D: the age of the adult flies is not specified; it would also be positive to examine the distribution of Acetobacter and Gluconobacter at 10 and 40 days).

Response2-3: We believe the backcrossed UAS-LacZ would be suitable as a control. For key experiments, we checked that RU486's side effect and confirmed it was not the case. What we have not been confident in this respect is the gut microbiota, and therefore we would test whether Gluconobacter is increased just by RU486 or not. Regarding Fig. 5C&D, we used young (day 10-old) flies. We did not examine the Aceto/Gluco at older days, but we assume that they are still in the gut microbiota. How ageing involves microbial change in this and many other contexts is our ongoing project.

1. The authors state at the bottom of p6 that JAK-STAT-dependent AMP expression was detected. Fig. 4C shows a significant expression of Drsl2. As far as this reviewer recalls, Buchon et al. had demonstrated a dependence on the JAK-STAT pathway of Drsl3. It would also be worth looking at Turandot genes. As regards an involvement of the Toll pathway, it is not clear whether Drosomycin is significantly expressed as it shows a 32-fold increase in Fig. 4C, yet is not found in Table S2. This issue should be clarified using RTqPCR and it may be worth monitoring also the expression of BomS1.

Response2-4: We would like to add the qRT-PCR of TotA,C, Drs, and BomS1 in the revised manuscript.

Minor points

a) It is surprising to observe an expression driven by the TIGS2 transgene in the larval fat body as it appears to be solely expressed in the intestine in adults. In which epithelial cell type of the intestine is TIGS2 expressed?

Response2-5: We were also surprised (and disappointed indeed) by the fact that TIGS2 shows broader expression pattern in the larvae. As far as we observed, it expresses at least in the enterocytes (strongly in anterior midgut).

b) The authors have carefully defined an optimal dose of RU486 at 1 µM. Why use 20µM Fig. S1, or 50µM (Fig. S6)? Of note, the Flygutseq indicates that Alp9&10 are downregulated in enterocytes upon P. entomophila challenge.

Response2-6: We used 1µM at first, only to have realised that 1µM is too mild to carefully assess the expression pattern of the driver. Thank you for the note, we would cite the paper to generalise our finding.

c) Fig. 1B&C: are the flies used in C) escapers as hardly any flies survive the 5µM RU486 challenge B)?

Response2-7: We prepared more than 1000 embryos for this and many other experiments. One percent of survivors is enough to produce flies in Fig. 1C.

d) Fig. 1D: do the authors know why there is such a difference between DptA and Drosocin?

Response2-8: We greatly appreciate for this comment. There seemed to be a miscalculation here. We have repeated the same experiment again, and now they showed similar magnitude of induction. We would revise this figure.

e) Fig. 2E: the caption does not allow to recognize which curve is LacZ RU and which one is IMD[CA] (dashed line?).

Response2-9: We would amend the caption.

f) Methods: the authors mention that they have dissected crop and Malpighian tubules. As no crop data are reported, does it mean that the crop and MT have been pooled in the same sample; please, clarify.

Response2-10: Sorry for our confusing writing. We have revised the text now to clarify we have "removed" crop and MTs.

Significance:

This study takes place in a context of the influence of infections during early life on subsequent fitness at the adult stage of organisms. With respect to mammals, it is important to note that Drosophila melanogaster undergoes a full metamorphosis that yields a thoroughly novel life form adapted to a new aerial life style. Thus, an influence of the larval stage on the imago is definitely interesting. The senior author has already published interesting work on this topic by showing that oxidative stress experienced during larval stages modifies adult fitness through an indirect action on the larval microbiota. This work is going to be of interest to investigators working on the microbiota and also on intestinal infections, let alone the community of entomologists.

Response2-11: We are really happy to see this comment. We believe that it is important to provide evidence and elucidate mechanisms of how gut microbiota alteration acts as a key factor to exert a life-long effect on the host physiology by a transient event occurred at a juvenile stage.

Drosophila host defense against infections, intestinal infections, host-pathogen interactions

Reviewer #3

Summary

In their manuscript "Activation of innate immune signalling during development predisposes to inflammatory intestine and shortened lifespan" Yamashita et al. have used the Gene Switch system to temporally overexpress imd in Drosophila larval stages and followed the possible effect on adult food intake, starvation resistance and lifespan. Specifically, the authors show that activating the IMD pathway in Drosophila larvae leads to decreased lifespan, lower adult body weight and lower food intake. Furthermore, the authors claim that adult flies develop inflammation in the gut, and, as a consequence, a change in the gut microbiome. The study aims to show the effect of prolonged immune system activation at an early developmental stage on adults.

Major comments

The authors' main conclusion is that IMD activation during development results in adult inflammatory gut, which affects the lifespan of the flies as well as food intake and starvation resistance. Mifepristone (RU486) is used to induce gene expression under GeneSwitch drivers. Using mifepristone is a bit controversial when lifespan effects are being studied. The authors should state that there are various earlier studies showing that mifepristone affects lifespan and also metabolism (e.g. reduces mitochondrial functions and activates AMPK). Although it is fairly reliable that the effects that the authors are seeing are resulting from the IMD pathway activation, it can also be a stress response caused by a combination of mifepristone treatment + IMD activation.

Response3-1: We would like to carefully discuss this possibility by citing the relevant literature.

The authors show that mifeprestone concentration of 5 µM is causing severe lethality and low body weight in DaGS>IMDCA animals. The concentration of 1 µM doesn't give the same effect, but already induces gene expression (as confirmed by imaging in Fig. S1B). Throughout the study, the concentration of 5 µM is still used and the authors claim that the phenotype seen in DaGS>IMDCA animals is suggesting that IMD activation impairs larval growth. However, can this be a case of toxicity/synthetic lethality caused by high concentration of RU486? Why wasn't 1 µM concentration used for the experiments, if it's sufficient to induce gene expression? Is there a possibility of using another temporal induction method causing less stress/toxicity for the flies? Furthermore, authors show that 1 µM mifepristone treatment shortens female lifespan, which is contradictory to the earlier literature. Citations are needed in here. Also, the decrease in female lifespan looks like it is non-significant, what statistics were used in this analysis? The methods section says OASIS2 software was used, but no further details are provided.

Response3-2: We apologise our unclear writing. We used 1 µM throughout the study, not 5 µM to avoid the drug's toxicity. We have not tested other method as GS works well by carefully optimising the RU486 doses. For statistics of lifespan, we would like to add the detailed information in the method section.

Only under 10% of in DaGS>IMDCA flies exposed to 5 µM RU486 eclose, yet in Fig. 1C showing the results of body weight measurements, n=20-50. How were the DaGS>IMDCA flies obtained if under the experimental conditions only a few of them develop successfully? At which developmental stage do the flies die? Why were only male flies used for this experiment?

Response3-3: Please see our Response2-7 We did not carefully check the developmental stage, but it apparently died at early stages of the larva. We usually use male flies for body weight, as female's body weight is understandably affected by the number of eggs inside of the body, making it difficult to discuss the phenotype of developmental growth.

More evidence is needed before concluding that the IMD lifespan effect is coming from the inflammatory intestine. TIGS driver is used to express genes of interest in the gut and fat body. No specific drivers for only the gut or only the fat body are used. Can it be claimed that the effect seen is coming purely from the gut expression? Is it possible that the fat body, which is the main organ responsible for the AMP production is actually responsible for enhanced IMD pathway target AMPs expression (as shown in Fig. S2A; the fold change is higher in the gut that in the fat body)? Was the gut not inflamed or damaged in larvae as there were no upd3 expression?

Response3-4: Thank you for raising this important point. Indeed, we have tried to seek for larval gut- (or fat body)-specific GeneSwitch but no drivers were suitable unfortunately. We admit that our conclusion is not thoroughly backed by the data, so we would carefully discuss this in the revised manuscript. Nevertheless, our new data showing dysbiosis in the larval gut now indicates that this is where the irreversible phenotype resides.

If the authors want to state that the effect is coming from inflammatory gut and that the lifespan effect and feeding/starvation resistance effect is coming from other tissues, why did the authors still decide to use the daughterless driver to study the IMD effect on lifespan, rather than gut or fat body driver, especially if they show that the feeding rate is changed (IMD OE in neurons) as this can also affect the microbiota (which they state is because of inflammatory gut)?

Response3-5: We used DaGS driver simply because it was stronger in terms of the lifespan phenotype. One can assume that the decreased feeding of the DaGS>IMDCA flies might influence the increased Gluconobacter, inflammatory gut, and the shortened lifespan. However, these phenotypes were going to the opposite direction, as decreased feeding theoretically leads to decrease the gut bacteria and extend lifespan. We would like to use a gut-specific (or even cell-type specific) GeneSwitch driver for further mechanistic study, but it may take a huge effort. Our take-home message of the present study is that the juvenile-restricted inflammatory experience causes early dysbiosis, which trigger persistent inflammatory gut in adult, and thereby shortens lifespan. We believe this is adequately supported by the data.

Immune responses are costly and that's one reason why their negative control is so important. The authors could state possible effects between continuously activated immune system (IMD pathway in larvae) and trade-offs in size and life-span in adult flies (+ citations to related studies). The role of constitutively activated IMD in larvae could have been confirmed by using alternative method for activating IMD, e.g. knock out of a negative regulator. Additional controls could have been used, e.g. DaGS background strain without the daughterless driver crossed with the IMDCA , or in the experiment where the gut microbiota was checked (this experiment was lacking the DaGS >LacZ + mifepristone treatment and only had DaGS>IMDCA flies with and without the mifepristone treatment). Usually in Drosophila genetics more control crosses are needed, for e.g. two different constructs of the OE IMD strains e.g. GD and KK backgrounds. The efficiency of the IMD OE could have been directly measured with qPCR and not only shown by measuring the expression of target AMPs.

Response3-6: We would like to make sure the point clearer. The phenotype observed in our study is not related to the trade-off between size and lifespan since we used the 1µM of RU486, which did not affect body size (Fig. 1C) but did shorten the lifespan (by larval but not adult IMD activation). In this sense, we tried to avoid the strong immune activation in the larva as it disturbed the development. Regarding other method for activating IMD, we were not able to use knockouts because we need to make it temporal manipulation in larvae. Alternatively, we had tested PGRP-LC overexpession. When it was expressed strongly in the larvae, it led to the lethality. When it was mild, we observed the shortened lifespan just as in IMDCA overexpression. This new data would support our conclusion well. Please note that we use IMD OE not RNAi (GD and KK lines are RNAi lines).

Regarding gut microbiota, we would like to check whether DaGS>LacZ + RU86 affects Gluconobacter or not. Regarding, efficiency of IMD OE, we would like to perform qPCR of IMD gene.

One of the conclusions drawn is that adults develop gut tissue damage as a result of inflammation. The authors could provide further evidence of this by utilizing microscopy to recognize possible changes in gut epithelia (with appropriate controls).

Response3-7: We appreciate for the suggestion. Somewhat intriguingly, we have not observed any difference in the number of ph3 positive cells, a hallmark of tissue damage-induced ISC proliferation. This is consistent with our preliminary observation that aged flies after larval IMD activation did not show "smurf" phenotype, an indicator of gut barrier dysfunction. In the revised manuscript, we would like to add some qPCR data to test whether upd3/JAK-STAT pathway is activated to detect the tissue damage and carefully discuss the point.

The methods section could be more detailed and clearer to the reader. The statistical analyses used for e.g. survival rates should be described in more detail. The sustained alkaline phosphatase treatment should also be described in more detail, as currently the methods do not clearly state how long the flies were treated with Alp. The description of antibiotic cocktail treatment in the materials and methods should not be under the stocks and husbandry section, as it implies that all flies used were all the time maintained on an antibiotic cocktail<br> Methods sections could be arranged to resemble more the order of the results sections and more details should be added. It would be challenging to repeat the experiments the way as they have been described.

Response3-8: We would like to amend the method section accordingly.

Minor comments

The efficiency of the IMD OE was not directly measured with qPCR, only the expression of target AMPs were measured. The authors should show the activation efficiency of the IMD expression.

Response3-9: Please see our Response1-2

Figure 1B, are these females or males?

Response3-10: It includes both sexes. We add this explanation in the methods.

Fig1 E. in the transcriptome analysis the negative control should have been also treated with mifepristone<br> Response3-11: Due to financial reason, we could not perform RNAseq analysis for all the samples. We believe showing specific activation of IMD pathway in the IMDCA + RU486 compared the negative control IMDCA -RU486 is sufficient.

For the experiment presented in Fig. S6, females are used, although for the majority of other experiments, only male flies are used?

Response3-12: We have done qPCR in males as well. We add this data in the revised manuscript.

In Fig. S1C, DaGS>GFP expression is induced in 3rd instar larvae by 20 µM RU486. Is concentration this high not toxic for the larvae?

Response3-13: In this experiment, we wanted to see the expression pattern of the driver. Please also see our Response2-6.

The fact that developmental IMD activation increased DptA expression in the adult gut suggested that an irreversible change occurred in this tissue. - what is meant by irreversible change? Can this claim be made?

Response3-14: What we meant by "irreversible" here was that there was a permanent increase of immune activity by the larval IMD activation. It would have been inappropriate to describe the phenotype, so we would avoid this word in the revised manuscript.

Alp results are interesting. Does IAP expression decrease in adults as they age? The authors used "sustained Alp supplementation" to rescue the reduced lifespan phenotype in adults. How long were the flies treated with Alp? This should be mentioned in the materials and methods

Response3-15: According to the literature, IAP expression is decreased during ageing in (Kühn F et al., JCI insight, 2020). In this experiment, we used life-long IAP supplementation (from day 2 onward). This would be mentioned in the revised manuscript.

The description of antibiotic cocktail treatment in the materials and methods should not be under the stocks and husbandry section, as it implies that all flies used were all the time maintained on an antibiotic cocktail.<br> In the qRT-PCR section, the analysis method could be added (copy number method/ΔΔCt)<br> Line 49-50 is missing a reference<br> Line 81, PGAM5 is mentioned without further explaining what it is<br> Line 229 - what is meant by inflammatory vicious cycles?<br> Line 314 - what is meant by thrifty phenotype?<br> In figures showing lifespan, a different color code could be used where yellow and orange/red lines represent different genotypes/treatments; it is hard to visually distinguish the colors that are used at the moment<br> Figure legend for Fig. 4C - AP could be written out as alkaline phosphatase already here. Also in the legend for Fig. 4 it says E twice (instead of E and then F)<br> Fig. 5A - a title for x-axis could be added to make it clearer that this represents the proportion of the bacterial taxa in the gut<br> Fig. S2A - LacZ is mentioned in the description but not shown in the figure

Response3-16: We would amend these in the revised manuscript.

Were there possible cross tissue contaminations in the adult gut samples? where possible contaminations checked e.g. with fatbody specific primers? This should be checked as fatbody is known to produce more AMPs when immune activated, than the gut tissue.

Response3-17: We are well-trained in the dissection of the gut. All the fat body was carefully removed by dissection. Especially when abdominal samples do not show any difference in Fig. 4B, we did not agree that the contamination would explain the data.

CFU analysis: were the flies surface sterilized briefly in ethanol prior dissections?

Response3-18: Yes, flies were surface sterilized by serial washes of 3% bleach and 70% ethanol. We add this procedure in the method section.

Fig2 B-C, the differences between the females and males are not drastic enough to decide to use only males later on. E. typo in starvation. DA>IMD males have decreased starvation resistance without and with the mifepristone treatment?

Response3-19: We decided to use males as females have a slight negative side effect of RU486. DaGS>IMDCA have increased starvation resistance only with the mifepristone treatment. We apologise that our figure caption is not clear. We would amend this in the revised manuscript.

Significance

The topic presented in this manuscript is interesting and relevant for both the fields of aging and immunology and partially explains why early life experiences are important for the wellbeing of the individual later in life. Some of the findings presented in the manuscript are novel, at the same time some of these same issues have been examined in papers related to immune priming/training/memory. The reported findings of the manuscript would be of interest for an audience that is interested about aging and lifespan related issues, as well as immunology and metabolism.

Response3-19: This reviewer's evaluation of the significance of the study is very encouraging. We believe that the phenotypes observed in the manuscript would give wide interest to the biologist working on this hot topic: how early-life event induces later-life health.

Field of expertise: Innate Immunity; Drosophila; Metabolism; Host-Pathogen Interactions; Biomedicine

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Referee #3

Evidence, reproducibility and clarity

Summary

In their manuscript "Activation of innate immune signalling during development predisposes to inflammatory intestine and shortened lifespan" Yamashita et al. have used the Gene Switch system to temporally overexpress imd in Drosophila larval stages and followed the possible effect on adult food intake, starvation resistance and lifespan. Specifically, the authors show that activating the IMD pathway in Drosophila larvae leads to decreased lifespan, lower adult body weight and lower food intake. Furthermore, the authors claim that adult flies develop inflammation in the gut, and, as a consequence, a change in the gut microbiome. The study aims to show the effect of prolonged immune system activation at an early developmental stage on adults.

Major comments

The authors' main conclusion is that IMD activation during development results in adult inflammatory gut, which affects the lifespan of the flies as well as food intake and starvation resistance. Mifepristone (RU486) is used to induce gene expression under GeneSwitch drivers. Using mifepristone is a bit controversial when lifespan effects are being studied. The authors should state that there are various earlier studies showing that mifepristone affects lifespan and also metabolism (e.g. reduces mitochondrial functions and activates AMPK). Although it is fairly reliable that the effects that the authors are seeing are resulting from the IMD pathway activation, it can also be a stress response caused by a combination of mifepristone treatment + IMD activation. The authors show that mifeprestone concentration of 5 µM is causing severe lethality and low body weight in DaGS>IMDCA animals. The concentration of 1 µM doesn't give the same effect, but already induces gene expression (as confirmed by imaging in Fig. S1B). Throughout the study, the concentration of 5 µM is still used and the authors claim that the phenotype seen in DaGS>IMDCA animals is suggesting that IMD activation impairs larval growth. However, can this be a case of toxicity/synthetic lethality caused by high concentration of RU486? Why wasn't 1 µM concentration used for the experiments, if it's sufficient to induce gene expression? Is there a possibility of using another temporal induction method causing less stress/toxicity for the flies? Furthermore, authors show that 1 µM mifepristone treatment shortens female lifespan, which is contradictory to the earlier literature. Citations are needed in here. Also, the decrease in female lifespan looks like it is non-significant, what statistics were used in this analysis? The methods section says OASIS2 software was used, but no further details are provided.

Only under 10% of in DaGS>IMDCA flies exposed to 5 µM RU486 eclose, yet in Fig. 1C showing the results of body weight measurements, n=20-50. How were the DaGS>IMDCA flies obtained if under the experimental conditions only a few of them develop successfully? At which developmental stage do the flies die? Why were only male flies used for this experiment?

More evidence is needed before concluding that the IMD lifespan effect is coming from the inflammatory intestine. TIGS driver is used to express genes of interest in the gut and fat body. No specific drivers for only the gut or only the fat body are used. Can it be claimed that the effect seen is coming purely from the gut expression? Is it possible that the fat body, which is the main organ responsible for the AMP production is actually responsible for enhanced IMD pathway target AMPs expression (as shown in Fig. S2A; the fold change is higher in the gut that in the fat body)? Was the gut not inflamed or damaged in larvae as there were no upd3 expression?

If the authors want to state that the effect is coming from inflammatory gut and that the lifespan effect and feeding/starvation resistance effect is coming from other tissues, why did the authors still decide to use the daughterless driver to study the IMD effect on lifespan, rather than gut or fat body driver, especially if they show that the feeding rate is changed (IMD OE in neurons) as this can also affect the microbiota (which they state is because of inflammatory gut)?

Immune responses are costly and that's one reason why their negative control is so important. The authors could state possible effects between continuously activated immune system (IMD pathway in larvae) and trade-offs in size and life-span in adult flies (+ citations to related studies). The role of constitutively activated IMD in larvae could have been confirmed by using alternative method for activating IMD, e.g. knock out of a negative regulator. Additional controls could have been used, e.g. DaGS background strain without the daughterless driver crossed with the IMDCA , or in the experiment where the gut microbiota was checked (this experiment was lacking the DaGS >LacZ + mifepristone treatment and only had DaGS>IMDCA flies with and without the mifepristone treatment). Usually in Drosophila genetics more control crosses are needed, for e.g. two different constructs of the OE IMD strains e.g. GD and KK backgrounds. The efficiency of the IMD OE could have been directly measured with qPCR and not only shown by measuring the expression of target AMPs.

One of the conclusions drawn is that adults develop gut tissue damage as a result of inflammation. The authors could provide further evidence of this by utilizing microscopy to recognize possible changes in gut epithelia (with appropriate controls).

The methods section could be more detailed and clearer to the reader. The statistical analyses used for e.g. survival rates should be described in more detail. The sustained alkaline phosphatase treatment should also be described in more detail, as currently the methods do not clearly state how long the flies were treated with Alp. The description of antibiotic cocktail treatment in the materials and methods should not be under the stocks and husbandry section, as it implies that all flies used were all the time maintained on an antibiotic cocktail

Methods sections could be arranged to resemble more the order of the results sections and more details should be added. It would be challenging to repeat the experiments the way as they have been described.

Minor comments

The efficiency of the IMD OE was not directly measured with qPCR, only the expression of target AMPs were measured. The authors should show the activation efficiency of the IMD expression.

Figure 1B, are these females or males?

Fig1 E. in the transcriptome analysis the negative control should have been also treated with mifepristone

For the experiment presented in Fig. S6, females are used, although for the majority of other experiments, only male flies are used?

In Fig. S1C, DaGS>GFP expression is induced in 3rd instar larvae by 20 µM RU486. Is concentration this high not toxic for the larvae?

The fact that developmental IMD activation increased DptA expression in the adult gut suggested that an irreversible change occurred in this tissue. - what is meant by irreversible change? Can this claim be made?

Alp results are interesting. Does IAP expression decrease in adults as they age? The authors used "sustained Alp supplementation" to rescue the reduced lifespan phenotype in adults. How long were the flies treated with Alp? This should be mentioned in the materials and methods

The description of antibiotic cocktail treatment in the materials and methods should not be under the stocks and husbandry section, as it implies that all flies used were all the time maintained on an antibiotic cocktail.

In the qRT-PCR section, the analysis method could be added (copy number method/ΔΔCt)

Line 49-50 is missing a reference Line 81, PGAM5 is mentioned without further explaining what it is Line 229 - what is meant by inflammatory vicious cycles? Line 314 - what is meant by thrifty phenotype?

In figures showing lifespan, a different color code could be used where yellow and orange/red lines represent different genotypes/treatments; it is hard to visually distinguish the colors that are used at the moment

Figure legend for Fig. 4C - AP could be written out as alkaline phosphatase already here. Also in the legend for Fig. 4 it says E twice (instead of E and then F)

Fig. 5A - a title for x-axis could be added to make it clearer that this represents the proportion of the bacterial taxa in the gut

Fig. S2A - LacZ is mentioned in the description but not shown in the figure

Were there possible cross tissue contaminations in the adult gut samples? where possible contaminations checked e.g. with fatbody specific primers? This should be checked as fatbody is known to produce more AMPs when immune activated, than the gut tissue.

CFU analysis: were the flies surface sterilized briefly in ethanol prior dissections?

Fig2 B-C, the differences between the females and males are not drastic enough to decide to use only males later on. E. typo in starvation. DA>IMD males have decreased starvation

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors study the impact of ubiquitously activating the IMD pathway only during larval stages on subsequent adult life. They report a shortened lifespan due to IMD pathway activation in the larval gut and a resistance to starvation linked to its activation in the nervous system. While there is apparently no activation of the IMD pathway in very young adult flies, the expression of some IMD-dependent antimicrobial peptide (AMP) genes is reported from 7-10 flies onwards. This expression is lost upon treating the adults with antibiotics, which also rescues the shortened lifespan phenotype. It correlates with a possible increase in the proportion of Gluconobacter in the microbiota.

While the study looks interesting, it is not clear whether the results, especially those of survival studies and RTqPCR experiments, have been replicated in independent experiments. This is essential to warrant their conclusions. In this respect, this reviewer notes some important variability in the lifespan studies (e.g., Fig. 2B vs. Fig. 4E): how do the authors account for a lifespan that is shortened almost by half in Fig. 4E? Also, Fig. S2B is not convincing given the observed variability. More data points are required to reach a conclusion.

The authors suggest in their Discussion some kind of epigenetic mechanism transmitting the information of IMD pathway activation having occurred at larval stages. Whether this depends on a change of metabolism remains to be demonstrated, in as much it is likely that there is a major metabolic "reset" occurring during metamorphosis to prepare the individual to the new environmental conditions encountered as an adult. It is also likely that larvae in the wild grow in a microbe-rich slurry and are likely to experience intestinal infections. As noted by the authors themselves on the top paragraph of p7 (line numbers are unreadable), the larval gut is degenerated during metamorphosis and thus the enterocytes that have produced AMPs are no longer present. One possibility would be that there is an early dysbiosis already occurring during larval stages and that the young adults re-infect themselves, for instance through contact with the meconium. The authors' experiments with antibiotics are the key to this study. However, one would like to observe results of the converse experiment, that is, treating larvae with antibiotics (a better control would be to bleach the embryos to generate axenic flies) and then raising the hatched adult flies in a conventional manner. In this way, the authors may determine whether the influence of early IMD pathway activation occurs through "self" mechanisms or whether it entails a contribution from the microbiota. It might also be useful to use reporter transgenes such as Dpt-LacZ to document where in the gut IMD activation takes place in the adult and to monitor whether there is any weak signal that would not be picked up by RTqPCR in newly hatched flies.

Specific comments

1. The GS system used in this study requires multiple controls, as a study from the Serroude laboratory has reported a driver-dependent leakiness of expression independent of exposure to RU486 (Poirier et al., Aging Cell, 2008). Thus, it would be good to check this with a cross to a UAS-GFP driver and examining the 10 and 40-day time points. The same should be done with antibiotics-treated flies as regards DptA and Drosocin expression (Fig. 5C &D: the age of the adult flies is not specified; it would also be positive to examine the distribution of Acetobacter and Gluconobacter at 10 and 40 days).
2. The authors state at the bottom of p6 that JAK-STAT-dependent AMP expression was detected. Fig. 4C shows a significant expression of Drsl2. As far as this reviewer recalls, Buchon et al. had demonstrated a dependence on the JAK-STAT pathway of Drsl3. It would also be worth looking at Turandot genes. As regards an involvement of the Toll pathway, it is not clear whether Drosomycin is significantly expressed as it shows a 32-fold increase in Fig. 4C, yet is not found in Table S2. This issue should be clarified using RTqPCR and it may be worth monitoring also the expression of BomS1.

Minor points

a) It is surprising to observe an expression driven by the TIGS2 transgene in the larval fat body as it appears to be solely expressed in the intestine in adults. In which epithelial cell type of the intestine is TIGS2 expressed?

b) The authors have carefully defined an optimal dose of RU486 at 1 µM. Why use 20µM Fig. S1, or 50µM (Fig. S6)? Of note, the Flygutseq indicates that Alp9&10 are downregulated in enterocytes upon P. entomophila challenge.

c) Fig. 1B&C: are the flies used in C) escapers as hardly any flies survive the 5µM RU486 challenge B)?

d) Fig. 1D: do the authors know why there is such a difference between DptA and Drosocin?

e) Fig. 2E: the caption does not allow to recognize which curve is LacZ RU and which one is IMD[CA] (dashed line?).

f) Methods: the authors mention that they have dissected crop and Malpighian tubules. As no crop data are reported, does it mean that the crop and MT have been pooled in the same sample; please, clarify.

Significance

This study takes place in a context of the influence of infections during early life on subsequent fitness at the adult stage of organisms. With respect to mammals, it is important to note that Drosophila melanogaster undergoes a full metamorphosis that yields a thoroughly novel life form adapted to a new aerial life style. Thus, an influence of the larval stage on the imago is definitely interesting. The senior author has already published interesting work on this topic by showing that oxidative stress experienced during larval stages modifies adult fitness through an indirect action on the larval microbiota. This work is going to be of interest to investigators working on the microbiota and also on intestinal infections, let alone the community of entomologists.

Drosophila host defense against infections, intestinal infections, host-pathogen interactions

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Referee #1

Evidence, reproducibility and clarity

This paper shows that transient genetic induction of the IMD innate immune pathway during Drosophila development, has long term effects on adult health and lifespan. The paper is well-written, the experiments are well designed and executed, and the data are without exception good quality. The data also support the specific conclusions well. The experiments take full advantage of the Drosophila system to pinpoint the effect on lifespan to long term activation of inflammation in the gut, which is interlinked and dependent upon changes in the microbiota. However the analysis is not comprehensive, because neural-specific effects on starvation resistance are not followed up, and because the etiology of the changes in microbiota is not mapped out. I should also say that I do not fully agree with the conclusion in the last sentence of the Abstract (the most important general conclusion), that the study "demonstrates a tissue-specific programming effect" of early transient IMD function. Since the lifespan shortening was shown to be dependent upon increased gut Gluconabacter, I would not call this "programming" (though the term is vague enough to mean most anything.) Instead, I would refer to the effect as a host-environment interaction. If it were "programming" of, for instance, the genetic or epigenetic sort, it would not be so easy to reverse.

A few other minor comments:

1. Several experiments, the authors use GFP (Fig S1) or the IMD targets DptA or Dro (Fig S2) to validate the induction of IMD-CA. Why have they not directly measured the expression of IMD-CA. This would seem to be logical and technically easy, by qPCR.
2. In Fig 4 we see and experiment in which animals were "supplemented" with Alkaline Phosphatase, a protein. How was this done and why does it work? Is AP a gut luminal protein?
3. The results in Fig 5 are really where the paper begins to determine a mechanism for the lifespan shortening. However, these results are rather weak, and they don't extend very far. The increase in Gluconobacter is mild (Fig 5C), and is not clear in the 16S rRNA sequencing experiment (Fig 5A). Furthermore, it is not clear that Glunconobacter specifically is the source of the lifespan shortening, of just bacteria in general (Fig 5E).

Significance

Although this paper addresses in interesting topic using an elegant and effective experimental strategy, the final results (Fig 5) and conclusions are modest. The analysis doesn't extend far enough to demonstrate how long term changes in microbiota arise from short term developmental changes in innate immune activity. Moreover, there is no detailed data concerning how the altered microbiota alter lifespan. Thus, while the results are interesting and the findings open avenues for further studies on the topic, the significance of the paper is modest, in its current state. Further analysis of how the microbiota is permanently changed, and why this affects lifespan, could enhance the paper. However, it is not clear that any simple, quick experiments could dramatically advance the findings from where they are now.

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Reply to the reviewers

We thank the reviewers for their appreciation of our work and for their constructive feedback. We have addressed their comments in the point-by-point answers below. We provide a largely revised manuscript as well as the plan for new experiments, following requests from the reviewers.

Reviewer #1 (Evidence, reproducibility and clarity (Required)): In their manuscript, Ronchi P. et al. present a thorough and very well detailed workflow for 3D correlative-light and electron microscopy of whole cells in large tissues. Their approach of iterative block trimming and florescence imaging combined with laser branding allowed them explore previously inaccessible tissues and questions. They imaged mammary gland organoids, and resolved the organization of the cells in the organoid and mitotic events. They also specifically targeted tracheal terminal cells of a 3rd instar Drosophila larvae labeled with cytoplasmic DsRed to study their ultrastructure, and several Drosophila ovarian follicular cells (FC) where the cytoplasmic motor protein dynein was knocked down (KD) by RNAi. In the tracheal cells, they observed connected secretory vesicles, probably delivering extra-cellular matrix to the trachea tube. They also found that the overall shape of dynein KD FCs is distorted comparted to WT, and that the localization of multi-vesicular bodies/endosomes inside the FCs changed from an apical to basal membrane localization. Although the approach is not entirely new, the manuscript certainly paves the way for future studies to obtain ultrastructural information from large specimens and combine it with meaningful fluorescence information, it's also beautiful and polished.

\*Minor comments:**

1. The authors state that they (line 145) that they found the optimal concentration of UA and the best compromise between EM contrast and fluorescence preservation. However, no detail is provided as to how these parameters were experimentally determined. *

UA concentration can be optimized in a number of ways, including varying incubation temperature and time. We decided to modify the speed at which the temperature was increased after the freeze substitution step at -90°C. We have experimentally compared 3°C/h vs 5°/h (described in the original on-section CLEM protocol by Kukulski et al) and found a considerable difference for some of the samples we used. This is now described in the revision (lines 152-159). While other protocols might work for some samples, we found this protocol to provide good quality imaging with a large variety of samples we have worked with (including some that are not included in the current paper, e.g. gastrulating Drosophila embryos or C. elegans larvae).

• More detail as to how the block face was mounted and kept parallel to the glass bottom dish would be helpful. *

This is now described in lines 182-185.

Also, what was the optical slice of the confocal and what was the increment in Z?

The information is now included in lines 191-192.

• Have the authors tried fluorophores with shorter wavelength (like GFP)? And if so, have they estimated the penetration depth in resin? This would be informative because many GFP lines already exist in the Drosophila model.*

In the current version, we have limited our study to red fluorescent proteins because UA is autofluorescent in green. This could cause problems when imaging at shorter wavelengths. We have discussed this in lines 442-444. However, we agree that an analysis of the behavior of GFP in confocal imaging of the block could improve our work and increase the potential applicability of this method. We are therefore planning an experiment to compare the behavior of EGFP and mCherry during confocal imaging of the block. This experiment will be included in a future revised version.

• In figure 6 i, how did the authors identify the structures to be MBVs close to the basal surface in the mutant seeing as they do not look like the MVBs seen in WT cells?*

In both cases, we identified MVBs as vesicles with a clear lumen containing one or more vesicles of homogenous size. We have included a paragraph in the Material & Methods on “multivesicular body quantification” where this is specified (lines 597-599). The only difference between MVBs of WT and KD cells was their size (shown in Fig. 6j,k,l), and therefore the identification was unambigious.

Similarly, how were the structures identified as endosomes in figure 5f?

We thank the reviewer for pointing this out. We agree that it is impossible to discriminate between endocytic and exocytic vesicles in our static data. We have therefore rephrased this as “membrane trafficking” (line 355, line 358, line 946).

Can the authors quantify the total MVBs in the apical/basal membranes from both RNAi KD and WT?

We have now segmented all MVBs in 5 KD cells and 5 neighboring WT cells in 4 different oocytes. Representative images, as well as a quantitative analysis of the distribution of MVBs, are shown in Fig. 6m-o. When we segmented MVBs for this analysis, we realized that WT cells showed large MVBs in their apical side (~5-10% of total MVBs) while in KD cells this population was almost completely absent. This is consistent with a role of dynein in MVB fusion. The data are now included in Fig. 6p. We thank the reviewer for her/his suggestion to have a more rigorous analysis of the MVBs, which allowed us to make another interesting discovery.

• The motivation/question in the case of Drosophila samples was clear but not so obvious in the case of the mammary gland organoids. It would be nice if the authors could give a bit more information.*

We have included a justification for the use of organoids in lines 226-235.

• In the introduction (line 124). The dimensions are given in microns and millimeters, which can be a bit confusing. *

We have changed this (line 132).

• In the discussion (lines 427-431), "sample preparation protocols compatible with fluorescence preservation have proven satisfactory for FIB-SEM milling and imaging" have also been shown by others (Porrati et al., 2019).*

We agree with the reviewer and indeed Porrati et al., 2019 was cited in the introduction. We have not claimed that we have shown this for the first time. For completeness, we cite the paper again in the discussion (line 469).

• Figure 1:
  • It would be helpful if the cell referred to in g was highlighted.*

As suggested, we have indicated the cell with an arrowhead.

- Is the cell in (h) the one in g or in a as written?

We apologize for the mistake. It is indeed the one in g. We have corrected this (line 874).

- Is the image in (k) inverted compared to (i)?

The image in k is not inverted compared to i. We are showing raw images of the confocal and FIB-SEM datasets and therefore the two volumes are rotated 90º with respect to each other along the Y axis. As we have realized that this can be confusing for the readers, we have introduced a sentence in Materials and Methods to describe the different orientations between confocal and FIB-SEM datasets (lines 586-589).

*Figure 2:

• In panel d it seems that some numbers on the x axis were duplicated.*

We apologize for the mistake. We have corrected figure 2.

*Figure 5:

• How does the perfect overlap confirm the accuracy of targeting?*

We agree with the reviewer that the overlap is not a measure of accuracy. We have removed the sentence from the legend.

- In panel (e) it was not particularly easy to understand what is the basal lamina.

We have manually segmented the 2 basal membranes in different colors. We hope the reviewer will find this representation clearer.

- In panel (g) the fused vesicle is not as clear as the movie. I also found it open to interpretation whether this is in fact a fused vesicle.

We agree with the reviewer that a 3D object can be better appreciated in the stack image sequence rather than in a single 2D image. However, to help the visualization of the event in the figure, we have shown the 3 ortho-slices in a perspective view in Fig. 5g. This was the best representation we have found. The video with the stack will be available to the readers for a better inspection.

We also agree that it is formally impossible to be sure whether the vesicle is in fact releasing material in the apical space or taking it up. Therefore, we describe now the event as “putative site of fusion…” (line 947).

*Reviewer #1 (Significance (Required)):

The increasing demand for volume electron microscopy brings a lot of challenges to correlative light and volume electron microscopy workflows. Although the methods used by the authors are not new, their combination is original. The manuscript will certainly contribute to the field of correlative light and volume EM and provide a rather detailed protocol that can be reproduced by others. The workflow is also more efficient than what was previously achieved using x-ray instead of light microscopy(Bushong et al., 2015; Karreman et al., 2016).*

We thank the reviewer for the careful examination of our work and for the positive statement. We are aware that many of the methods used have already been described by others, but we believe that their combination is original and very powerful.

Reviewer #2* (Evidence, reproducibility and clarity (Required)):

In this manuscript, Ronchi et al describe a workflow designed to facilitate the identification and downstream relocation of fluorescently tagged regions of interest within millimetre scale samples, ending with focused ion beam SEM acquisition of the target area. The work follows a logical progression, is well thought out, explained, and illustrated, with proof of concept experiments that are followed up by examples of systems where the potential for the application of the workflow in a 'real' biological question is demonstrated.

For me, the title reads better as ...targeting for FIB SEM acquisition... *

We have edited the title according to the reviewer’s suggestion

I have only minor suggestions for the revision of the manuscript from this initial version. The introduction, and introductory paragraphs for the two model systems would benefit from some revision to make them more concise however.

We have revised and shortened the introduction and introductory paragraphs for the model systems and we hope the reviewer will find it more concise.

\*Summary** Line 22 - omit large. *

Done (line 29)

Introduction Line 66 - It's probably clearer to discuss this concept as conductivity rather than grounding. We have changed this sentence (line 76)

Line 105 - Peddie and Collinson 2014 is not the correct reference for this statement. Presumably this is supposed to be Peddie et al 2014? ** We thank the reviewer for spotting this mistake. We have changed the citation (line 1110)

Line 124 - The external diameter of the carrier would give 7 mm2, but the internal diameter is smaller, so this size is slightly overstated.

We totally agree. The internal diameter of the carrier is 2mm and therefore the area 3.14 mm2. We have corrected the statement (line 132).

Results General comment - I find the use of NxNxN/N nm3 to be a confusing way of expressing the measurements, so would suggest splitting these up to express as: N nm3 or NxNxN nm.

To avoid confusion, we have now opted for: N nm x N nm x N nm.

Line 141 - no water was used in the FS mixture, and so wasn't needed for preservation of fluorescence? Dry/100% acetone? If no water is needed, this detail should be discussed. We added a clarification of this point (lines 148-150)

Line 142 - could the authors elaborate on the statement about timing and sample types, to give a better understanding of the context. The sentence referred to other possible applications (e.g. cell monolayers would require shorter FS time). However, as the method described here is aimed at large 3D samples, we find that longer FS times (72h) are always required. We have therefore removed the sentence (line 151).

Line 150 - on the choice of fluorophores, did the authors examine any shorter wavelengths, or was the decision to use red/far red based on any other evidence? Anecdotally, red and far red fluorophores may offer better preservation and less longevity in this context, but could the authors elaborate on their reasoning behind the choice shown here?

As replied to reviewer 1, point 3:

In the current version, we have limited our study to red fluorescent proteins because UA is autofluorescent in green. This could cause problems when imaging at shorter wavelengths. We have discussed this in lines 442-444.

However, we agree that an analysis of the behavior of GFP in confocal imaging of the block could improve our work and increase the potential applicability of this method. We are therefore planning an experiment to compare the behavior of EGFP and mCherry during confocal imaging of the block. This experiment will be included in a future revised version.

Line 168 - did immersion in water give rise to any distortion of the resin, or is HM20 sufficiently hydrophobic that this was not a concern? Mismatches in refractive indices (resin, water, glass, oil) could also presumably give rise to some small inaccuracies in depth prediction?

We observed a little distortion of the block face, due to hydration during the imaging step. However, as noticed during trimming at the microtome, this distortion was small and we could achieve a flat surface after removing 1-2 mm. Therefore this was not relevant for our measurements. We however now mention this in the discussion (lines 453-455). Mismatches of refractive indices also introduce inaccuracies, but these aberrations are reduced the closer the target is to the surface. Therefore, our predictions become more precise after each trimming step to approach the target.

Line 169 - was it possible to quantify the increase in signal? If the block is being hydrated, but the block is not absorbing water (re above point), then it must only be surface fluorophores that are hydrated

The quantified increase in fluorescence signal at the surface is now mentioned here (line 187) and can be observed in Fig. 2b. Indeed, only surface fluorophores are hydrated and we argue that this is an important player in the fluorescence intensity increase.

Line 179 - presumably this is a result of the surface of the block being hydrated (re above points). This is mentioned later, but could be explicitly stated here to make the point more strongly.

We now state this also in line 186.

Line 188 - Peddie et al 2014 contains some limited data for mCherry in sections that could be worth mentioning in support of the findings of reduced photobleaching rates

Thank you for pointing this out. We now cite Peddie et al 2014 (line 208-209)

Line 268 - It is not explicitly stated earlier, but multiple targets at similar depths would also be possible, presumably We have included a sentence to address this possibility (line 292-293)

Discussion Line 421 - sections cannot be repeatedly imaged without bleaching too much? Please elaborate on this statement to help strengthen the point as it isn't mentioned earlier in the results.

Our experience with in section fluorescence imaging is that fluorescent proteins are not very stable and bleach rather quickly. However, as we have not measured this with the same setup and with the same samples, we do not have a rigorous proof for this statement. As we believe the comparison with sections is not an important point here, we have removed the sentence (line 463)

Line 435 - FIB SEMs and 2Pi systems are not really so 'common' in the sense suggested, so this final statement should be reworded.

We have changed the sentence (lines 475-477)

M&Ms Line 540 - grooves, not groves

Changed (line 589)

Figure 3 legend Overall, it's a workflow comprising many methods, so it's best described as a schematic of the workflow.

Changed (line 900)

Confocal panel - target, not targets, and depth is misspelt.

We thank the reviewer for spotting these mistakes. We have corrected the figure*

*

Figure 4 legend Line 834 - as far as I can see, this is a different organoid that isn't shown in a and b, so this text should be removed.

The organoid is indeed a different one. We meant that the targeting was performed as shown in a and b. However, as the sentence could generate confusion, we have removed it (line 932).

Figure 5 legend Line 840 - was, not is

Changed (line 937)

Figure 6 a) It would help with clarity to also put e.g. white arrows on the WT epithelium

As we use arrows and arrowheads to indicate different events in the image, we have used green asterisks to label the nucleus of the WT cell and a red asterisk for the KD, as we have done in all the panels in figure 6, where both cell types are present in the same image.

f,g) It isn't really clear on first viewing what these images show, so they would benefit from some labels.

We have added labels to indicate all the cells represented in the images as well as the space in between (VM, vitelline material). Microvilli are now indicated with arrowheads. We have also explained in the figure legend that here we show in detail the structures indicated by black arrows in Fig. 6a, to help give a context to the high mag detail (lines 964-965).

\*Minor stylistic comments** There should be a space between numbers and units; this is inconsistent throughout. *

We have corrected this.

The use of black versus white text on the figures is inconsistent.

We have fixed this.

Table 1 - is it in the supplementary material or not? If it is, it should be referenced as such in the text. The formatting could use some refinement to match the standard of the other figures.

The table is supplementary material. We have now referenced it as such and we have reformatted it.

Capitalisation is inconsistent throughout.

We have revised the text.

The manuscript describes a workflow that connects several pre-existing methods to enable precision targeting of individual fluorescently tagged structures within a larger sample volume. The possibility for multi-modal imaging within a single embed specimen facilitates correlation of data for structure, with that of function. The work will be of interest to all scientists in the field of correlative microscopy

We thank the reviewer for her/his positive evaluation.

Reviewer #3* (Evidence, reproducibility and clarity (Required)):

The manuscript is written very clearly overall. I would like to raise a number of issues that the authors might address. Most are at the level or proof-reading.

The workflow still depends on availability of a specialized confocal microscope with two-photon laser excitation for marking the region of interest. A tweak to the method might simply be to scratch or etch markings onto the planed surface near the edges. Provided a motorized stage is available on the light microscope, the region of interest could be located precisely with reference to those, and then relocated in the SEM. It would be enough to suggest this, or another similar method, for those who don't have access to the two-photon microscope.*

In our view, the 2pi branding is important to position the FIB-SEM acquisition with high precision, reliability and confidence. However, we agree with the reviewer that there are other approaches to accomplish this task, which we now mention in the text. One is to simply measure the distance from the edges or corners of the block (lines 256-259). Another, could be to manually introduce landmarks (lines 259-260).

The second is to clarify in the text that the top-down view of the confocal microscopy is orthogonal to that of the FIB. This appears as a note in the caption to Figure 1, but it is an important point to align the expectations of readers who are not closely familiar with the methods.

We agree with the reviewer that this is a point that requires further clarification. We have described this in Materials & Methods in the paragraph “Image processing, dataset registration, visualization and segmentation” (lines 586-589).

The legend labels in Figure 1 do not match the figure itself, as if it were recompiled from an earlier draft: g-j) refers next to a).

We apologize for the mistake. We have corrected it.

The decrease in fluorescence intensity with depth into the specimen remains a bit ambiguous. The significant part of the text is dedicated to the suggestion that inherent protein fluorescence is affected by water content in the resin. After cutting back from the surface, are the originally deeper layers still dim, or do they become brighter? In other words, is the effect chemical or optical?

As we wrote in the discussion, probably both optical effects and hydration play a role in the observed fluorescence drop. The hydration we describe probably only takes place on the block surface when dipping the block in water for imaging. Therefore, when we expose deeper layers after removing the resin on top, they do become brighter. However, we cannot completely disentangle the optical and hydration effect. To make this clearer, we have explained the point in more detail in the discussion (lines 452-455). At the same time, we are planning a new experiment to compare the fluorescence signal in the presence or absence of water in the dish, which will allow us to discriminate between the two effects.

• Loss of confocal intensity with depth would be expected on the basis of a refractive index mismatch to the design parameters of the objective, especially for high numerical aperture. The objective is specified as multi-immersion but no further details are given. *

Details of the lense we used are now given in Materials and Methods (lines 539-540)

Another easy test would be to embed fluorescent beads as intensity standards. There could also be absorption of the fluorescence emission by the resin and stain, but such a strong effect in a few tens of microns would suggest that the block is quite dark. That seems inconsistent with the images in supplementary figures. Personally I was not bothered by the dimming in depth, since the conclusions do not depend on quantitative fluorescence intensities.

We agree with the reviewer that, although the fluorescence intensity drop is an effect that is worth describing because it has an implication for the identification of fluorescent targets in the block, our method does not rely on quantitative imaging. In all cases, we were able to detect fluorescence signal even very deep from the block surface and this was enough to target those cells at the FIB-SEM.

In some cases pre-embedding correlative imaging can be quite successful, for example in studies of Jost Enninga (e.g., Mellouk et al, Cell Host & Microbe 2014) or Eric Jorgensen (Watanabe et al, Nature Methods 2011). Do the authors see a distinction between adherent

cell cultures and unsupported tissues or tissue sections?

We completely agree with the reviewer that pre-embedding CLEM can be extremely successful and it is a very valuable tool, especially for the study of dynamic event is cell cultures. However, while for adherent cells the targeting is essentially a 2D problem and is facilitated by the fact that cells can be identified on the surface of the block under the SEM beam, for larger 3D samples the situation is much more complicated. We often lack landmarks and surface references and an anisotropic deformation occurs during sample prep, making targeting and localization prediction extremely inaccurate.

Other investigators have insisted that FIB-SEM requires especially heavy labelling. What was done differently here to make the light labeling possible? Such clues may be very useful to ongoing developments in the literature. Also, the present protocol skips osmium staining entirely. The authors must have compared images with and without osmium. What visible features do we lose as a result?

We provide a detailed freeze substitution protocol in table S1, such that the method can be easily reproduced. Although FIB-SEM imaging of osmium-free samples is not very common, it has been shown by others before (Porrati et al., 2019), with a slightly different FS protocol.

We found that our sample preparation is good enough for the detection of all membranous organelles, but also microtubules, centrioles and other subcellular structures. We did not observe any big difference compared to the more standard protocols containing osmium (line 136).

Perhaps the greatest challenge to large volume electron microscopy is to deal with rare events. Correlative fluorescence light-electron microscopy effectively addresses the issue of finding the region of interest in a two-dimensional specimen such as a thin section or even a monolayer cell culture. For tissues the solutions are still at large. It is almost always impractical to image an entire organ at the resolution required to see macromolecules (work of Harald Hess being the exception that proves the rule). The issue is especially acute where the imaging is destructive, as in the case of serial block-face and FIB-SEM tomography. MicroCT has been used so far as the method of choice in the work-up to locate the region of interest within a large specimen, but the approach requires expensive equipment and time-consuming analysis. Furthermore, it can provide directional clues solely on the basis of morphology. Fluorescence would be a far simpler tool, and more informative when labeling is directed to specific molecular components. The manuscript of Ronchi et al provides a much-needed demonstration and detailed set of instructions for 3D CLEM en route to FIB-SEM volume imaging. The examples are presented are both convincing and esthetic. Success depended on integration of a number of factors, including changes to the specimen preparation, so the workflow will be very useful. In short, I recommend publication.

We thank the reviewer for the generous comments.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

The manuscript is written very clearly overall. I would like to raise a number of issues that the authors might address. Most are at the level or proof-reading.

The workflow still depends on availability of a specialized confocal microscope with two-photon laser excitation for marking the region of interest. A tweak to the method might simply be to scratch or etch markings onto the planed surface near the edges. Provided a motorized stage is available on the light microscope, the region of interest could be located precisely with reference to those, and then relocated in the SEM. It would be enough to suggest this, or another similar method, for those who don't have access to the two-photon microscope.

The second is to clarify in the text that the top-down view of the confocal microscopy is orthogonal to that of the FIB. This appears as a note in the caption to Figure 1, but it is an important point to align the expectations of readers who are not closely familiar with the methods.

The legend labels in Figure 1 do not match the figure itself, as if it were recompiled from an earlier draft: g-j) refers next to a).

The decrease in fluorescence intensity with depth into the specimen remains a bit ambiguous. The significant part of the text is dedicated to the suggestion that inherent protein fluorescence is affected by water content in the resin. After cutting back from the surface, are the originally deeper layers still dim, or do they become brighter? In other words, is the effect chemical or optical? Loss of confocal intensity with depth would be expected on the basis of a refractive index mismatch to the design parameters of the objective, especially for high numerical aperture. The objective is specified as multi-immersion but no further details are given. Another easy test would be to embed fluorescent beads as intensity standards. There could also be absorption of the fluorescence emission by the resin and stain, but such a strong effect in a few tens of microns would suggest that the block is quite dark. That seems inconsistent with the images in supplementary figures. Personally I was not bothered by the dimming in depth, since the conclusions do not depend on quantitative fluorescence intensities.

In some cases pre-embedding correlative imaging can be quite successful, for example in studies of Jost Enninga (e.g., Mellouk et al, Cell Host & Microbe 2014) or Eric Jorgensen (Watanabe et al, Nature Methods 2011). Do the authors see a distinction between adherent cell cultures and unsupported tissues or tissue sections?

Other investigators have insisted that FIB-SEM requires especially heavy labelling. What was done differently here to make the light labeling possible? Such clues may be very useful to ongoing developments in the literature. Also, the present protocol skips osmium staining entirely. The authors must have compared images with and without osmium. What visible features do we lose as a result?

Perhaps the greatest challenge to large volume electron microscopy is to deal with rare events. Correlative fluorescence light-electron microscopy effectively addresses the issue of finding the region of interest in a two-dimensional specimen such as a thin section or even a monolayer cell culture. For tissues the solutions are still at large. It is almost always impractical to image an entire organ at the resolution required to see macromolecules (work of Harald Hess being the exception that proves the rule). The issue is especially acute where the imaging is destructive, as in the case of serial block-face and FIB-SEM tomography. MicroCT has been used so far as the method of choice in the work-up to locate the region of interest within a large specimen, but the approach requires expensive equipment and time-consuming analysis. Furthermore, it can provide directional clues solely on the basis of morphology. Fluorescence would be a far simpler tool, and more informative when labeling is directed to specific molecular components. The manuscript of Ronchi et al provides a much-needed demonstration and detailed set of instructions for 3D CLEM en route to FIB-SEM volume imaging. The examples are presented are both convincing and esthetic. Success depended on integration of a number of factors, including changes to the specimen preparation, so the workflow will be very useful. In short, I recommend publication.

I would like to raise a number of issues that the authors might address. Most are at the level or proof-reading.

The workflow still depends on availability of a specialized confocal microscope with two-photon laser excitation for marking the region of interest. A tweak to the method might simply be to scratch or etch markings onto the planed surface near the edges. Provided a motorized stage is available on the light microscope, the region of interest could be located precisely with reference to those, and then relocated in the SEM. It would be enough to suggest this, or another similar method, for those who don't have access to the two-photon microscope.

The second is to clarify in the text that the top-down view of the confocal microscopy is orthogonal to that of the FIB. This appears as a note in the caption to Figure 1, but it is an important point to align the expectations of readers who are not closely familiar with the methods.

The legend labels in Figure 1 do not match the figure itself, as if it were recompiled from an earlier draft: g-j) refers next to a).

The decrease in fluorescence intensity with depth into the specimen remains a bit ambiguous. The significant part of the text is dedicated to the suggestion that inherent protein fluorescence is affected by water content in the resin. After cutting back from the surface, are the originally deeper layers still dim, or do they become brighter? In other words, is the effect chemical or optical? Loss of confocal intensity with depth would be expected on the basis of a refractive index mismatch to the design parameters of the objective, especially for high numerical aperture. The objective is specified as multi-immersion but no further details are given. Another easy test would be to embed fluorescent beads as intensity standards. There could also be absorption of the fluorescence emission by the resin and stain, but such a strong effect in a few tens of microns would suggest that the block is quite dark. That seems inconsistent with the images in supplementary figures. Personally I was not bothered by the dimming in depth, since the conclusions do not depend on quantitative fluorescence intensities.

In some cases pre-embedding correlative imaging can be quite successful, for example in studies of Jost Enninga (e.g., Mellouk et al, Cell Host & Microbe 2014) or Eric Jorgensen (Watanabe et al, Nature Methods 2011). Do the authors see a distinction between adherent cell cultures and unsupported tissues or tissue sections?

Other investigators have insisted that FIB-SEM requires especially heavy labelling. What was done differently here to make the light labeling possible? Such clues may be very useful to ongoing developments in the literature. Also, the present protocol skips osmium staining entirely. The authors must have compared images with and without osmium. What visible features do we lose as a result?

Significance

Perhaps the greatest challenge to large volume electron microscopy is to deal with rare events. Correlative fluorescence light-electron microscopy effectively addresses the issue of finding the region of interest in a two-dimensional specimen such as a thin section or even a monolayer cell culture. For tissues the solutions are still at large. It is almost always impractical to image an entire organ at the resolution required to see macromolecules (work of Harald Hess being the exception that proves the rule). The issue is especially acute where the imaging is destructive, as in the case of serial block-face and FIB-SEM tomography. MicroCT has been used so far as the method of choice in the work-up to locate the region of interest within a large specimen, but the approach requires expensive equipment and time-consuming analysis. Furthermore, it can provide directional clues solely on the basis of morphology. Fluorescence would be a far simpler tool, and more informative when labeling is directed to specific molecular components. The manuscript of Ronchi et al provides a much-needed demonstration and detailed set of instructions for 3D CLEM en route to FIB-SEM volume imaging. The examples are presented are both convincing and esthetic. Success depended on integration of a number of factors, including changes to the specimen preparation, so the workflow will be very useful. In short, I recommend publication.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In this manuscript, Ronchi et al describe a workflow designed to facilitate the identification and downstream relocation of fluorescently tagged regions of interest within millimetre scale samples, ending with focused ion beam SEM acquisition of the target area. The work follows a logical progression, is well thought out, explained, and illustrated, with proof of concept experiments that are followed up by examples of systems where the potential for the application of the workflow in a 'real' biological question is demonstrated.

For me, the title reads better as ...targeting for FIB SEM acquisition...

I have only minor suggestions for the revision of the manuscript from this initial version. The introduction, and introductory paragraphs for the two model systems would benefit from some revision to make them more concise however.

Summary

Line 22 - omit large.

Introduction

Line 66 - It's probably clearer to discuss this concept as conductivity rather than grounding.

Line 105 - Peddie and Collinson 2014 is not the correct reference for this statement. Presumably this is supposed to be Peddie et al 2014?

Line 124 - The external diameter of the carrier would give 7 mm2, but the internal diameter is smaller, so this size is slightly overstated.

Results

General comment - I find the use of NxNxN/N nm3 to be a confusing way of expressing the measurements, so would suggest splitting these up to express as: N nm3 or NxNxN nm.

Line 141 - no water was used in the FS mixture, and so wasn't needed for preservation of fluorescence? Dry/100% acetone? If no water is needed, this detail should be discussed.

Line 142 - could the authors elaborate on the statement about timing and sample types, to give a better understanding of the context.

Line 150 - on the choice of fluorophores, did the authors examine any shorter wavelengths, or was the decision to use red/far red based on any other evidence? Anecdotally, red and far red fluorophores may offer better preservation and less longevity in this context, but could the authors elaborate on their reasoning behind the choice shown here?

Line 168 - did immersion in water give rise to any distortion of the resin, or is HM20 sufficiently hydrophobic that this was not a concern? Mismatches in refractive indices (resin, water, glass, oil) could also presumably give rise to some small inaccuracies in depth prediction?

Line 169 - was it possible to quantify the increase in signal? If the block is being hydrated, but the block is not absorbing water (re above point), then it must only be surface fluorophores that are hydrated and give rise to this increase in signal?

Line 179 - presumably this is a result of the surface of the block being hydrated (re above points). This is mentioned later, but could be explicitly stated here to make the point more strongly.

Line 188 - Peddie et al 2014 contains some limited data for mCherry in sections that could be worth mentioning in support of the findings of reduced photobleaching rates.

Line 268 - It is not explicitly stated earlier, but multiple targets at similar depths would also be possible, presumably.

Discussion

Line 421 - sections cannot be repeatedly imaged without bleaching too much? Please elaborate on this statement to help strengthen the point as it isn't mentioned earlier in the results.

Line 435 - FIB SEMs and 2Pi systems are not really so 'common' in the sense suggested, so this final statement should be reworded.

M&Ms

Line 540 - grooves, not groves

Figure 3 legend Overall, it's a workflow comprising many methods, so it's best described as a schematic of the workflow. Confocal panel - target, not targets, and depth is misspelt.

Figure 4 legend Line 834 - as far as I can see, this is a different organoid that isn't shown in a and b, so this text should be removed.

Figure 5 legend Line 840 - was, not is

Figure 6 a) It would help with clarity to also put e.g. white arrows on the WT epithelium f,g) It isn't really clear on first viewing what these images show, so they would benefit from some labels.

Minor stylistic comments

There should be a space between numbers and units; this is inconsistent throughout. The use of black versus white text on the figures is inconsistent. Table 1 - is it in the supplementary material or not? If it is, it should be referenced as such in the text. The formatting could use some refinement to match the standard of the other figures. Capitalisation is inconsistent throughout.

Significance

The manuscript describes a workflow that connects several pre-existing methods to enable precision targeting of individual fluorescently tagged structures within a larger sample volume. The possibility for multi-modal imaging within a single embed specimen facilitates correlation of data for structure, with that of function. The work will be of interest to all scientists in the field of correlative microscopy.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In their manuscript, Ronchi P. et al. present a thorough and very well detailed workflow for 3D correlative-light and electron microscopy of whole cells in large tissues. Their approach of iterative block trimming and florescence imaging combined with laser branding allowed them explore previously inaccessible tissues and questions. They imaged mammary gland organoids, and resolved the organization of the cells in the organoid and mitotic events. They also specifically targeted tracheal terminal cells of a 3rd instar Drosophila larvae labeled with cytoplasmic DsRed to study their ultrastructure, and several Drosophila ovarian follicular cells (FC) where the cytoplasmic motor protein dynein was knocked down (KD) by RNAi. In the tracheal cells, they observed connected secretory vesicles, probably delivering extra-cellular matrix to the trachea tube. They also found that the overall shape of dynein KD FCs is distorted comparted to WT, and that the localization of multi-vesicular bodies/endosomes inside the FCs changed from an apical to basal membrane localization. Although the approach is not entirely new, the manuscript certainly paves the way for future studies to obtain ultrastructural information from large specimens and combine it with meaningful fluorescence information, it's also beautiful and polished.

Minor comments:

1. The authors state that they (line 145) that they found the optimal concentration of UA and the best compromise between EM contrast and fluorescence preservation. However, no detail is provided as to how these parameters were experimentally determined.
2. More detail as to how the block face was mounted and kept parallel to the glass bottom dish would be helpful. Also, what was the optical slice of the confocal and what was the increment in Z?
3. Have the authors tried fluorophores with shorter wavelength (like GFP)? And if so, have they estimated the penetration depth in resin? This would be informative because many GFP lines already exist in the Drosophila model.
4. In figure 6 i, how did the authors identify the structures to be MBVs close to the basal surface in the mutant seeing as they do not look like the MVBs seen in WT cells? Similarly, how were the structures identified as endosomes in figure 5f? Can the authors quantify the total MVBs in the apical/basal membranes from both RNAi KD and WT?
5. The motivation/question in the case of Drosophila samples was clear but not so obvious in the case of the mammary gland organoids. It would be nice if the authors could give a bit more information.
6. In the introduction (line 124). The dimensions are given in microns and millimeters, which can be a bit confusing.
7. In the discussion (lines 427-431), "sample preparation protocols compatible with fluorescence preservation have proven satisfactory for FIB-SEM milling and imaging" have also been shown by others (Porrati et al., 2019).
8. Figure 1:

• It would be helpful if the cell referred to in g was highlighted.
• Is the cell in (h) the one in g or in a as written?
• Is the image in (k) inverted compared to (i)? Figure 2:
• In panel d it seems that some numbers on the x axis were duplicated. Figure 5:
• How does the perfect overlap confirm the accuracy of targeting?
• In panel (e) it was not particularly easy to understand what is the basal lamina.
• In panel (g) the fused vesicle is not as clear as the movie. I also found it open to interpretation whether this is in fact a fused vesicle.

Significance

The increasing demand for volume electron microscopy brings a lot of challenges to correlative light and volume electron microscopy workflows. Although the methods used by the authors are not new, their combination is original. The manuscript will certainly contribute to the field of correlative light and volume EM and provide a rather detailed protocol that can be reproduced by others. The workflow is also more efficient than what was previously achieved using x-ray instead of light microscopy(Bushong et al., 2015; Karreman et al., 2016).