Peer review of: miRNA-1-3p is an early embryonic male sex-determining factor in the Oriental fruit fly (2020)

Reviewers' comments:
Reviewer #1 (Remarks to the Author):
This paper presents an important advance in understanding the remarkable variety of genetic circuits
that control sex determination. The authors convincingly demonstrate that the micro RNA miR-1-3p is
a major player determining sex for the oriental fruit fly, and that it does so by reducing the level of
the transcript from the master, positively-autoregulating sex-switch gene transformer (tra) in this
species. Importantly, miR-1-3p is both necessary AND sufficient for male development. The authors
show that miR-1-3p acts very early in embryogenesis to determine sex. Since miR-1-3p is shown to
be autosomal, it cannot itself be the primary masculinizing signal from the male-determining Y
chromosome of this species, but its early regulation of tra suggests that it is likely to be an immediate
target of the Y signal and, as such, may lead to the identification of the primary signal itself.
Manipulating miR-1-3p can generate remarkably complete sex transformations in either direction.
Only one other example of a small RNA's key involvement in sex determination has been reported
(piRNA in the silk moth). Interestingly in that case the RNA is actually the primary sex-determining
signal arising from the heteromorphic sex chromosome (W) but its job is to feminize the animals,
contrary to the masculinizing role of miR-1-3p. Moreover, the silk moth doesn't use a tra ortholog.
These results are significant and should be of interest to a wide audience. There are, however, some
problems with the paper that need to be addressed.
Major points:
 (1) In addition to fairly numerous typos (e.g. 781: ration), there are serious problems with the
 grammar in this manuscript in many places that will need to be fixed (e.g. 191-194). Perhaps the
 Nature editorial staff will help the authors out. The authors misuse "which" repeatedly and have
 consistent problems with plurals.
 (2) The authors need to give the reader some idea of what degree of development corresponds to the
 "hours after oviposition" that they describe. Is the embryo cellularlized at the time of injections, and if
 so, how do the various injected materials (micro-RNAs, RNAi, CRISPR) get to their targets?
 (3) In any presentation of sex transformation results, understanding the nature of those
transformations, and the degree to which they are or are not complete, is essential. This is particularly
true in this case, since tra is known to positively autoregulate. The authors give the reader no
description of sexual dimorphism to help us understand their criteria for sex transformation. They say
that some of the transformations allow fertility, yet they do not list what fraction of the transformed
animals ARE fertile. They say that incomplete sex transformation are observed (mainly, it appears, as
abnormalities in ovaries), but their description of intersexuality is inadequate. Clearly intersexuality is
expected, since none of the the various treatments described that masculinize or feminize the animals
affect all the target animals. Moreover it seem unlikely that the CRISPER/CAS9 modification of target
genes would modify those alleles in EVERY potentially dimorphic cell. If sexual differentiation in this
species is cell autonomous, in light of what is known about tra, one would expect the authors to have
observed mosaic intersexuality among at least some of the treated progeny, and not true (cellular)
intersexuality. The specific nature of intersexuality can be one of the most useful pieces of information
for understanding the operation of the sex-determination circuitry. The minimal description the
authors provide in Fig. 5 of supposed incomplete feminization (no mention is made of incomplete
masculinization, by the way) is inadequate (indeed it does NOT look like mosaic intersexuality, since
the one picture of the supposed abnormal sexual phenotype is actually symmetric). Were the
genetalia mosaic, and if so, how? In presenting their data, the authors must distinguish complete sex
transformation from incomplete sex transformation, and they must provide a more scholarly and
convincing description AND discussion of intersexuality (or account for its general absence). If they
remove the superfluous information that they have included in this manuscript, they should have no
problem doing so within space constraints.
(4) We are told that feminized XY flies are fertile, but the authors give no data on the F1 sex ratios.
 When mated to wildtype males, was the expected skewing in sex ratio (and progeny death in the case
 of YY progeny) observed? Analysis of the progeny would be the most convincing way to show that the
 authors are indeed dealing with sex-reversed XY animals and should have been reported. Since the
 authors say that they did the matings, why do they not tell us the results! We also need to know
 whether sex-reversed XX males were also fertile (much less whether any analysis of THEIR progeny
 had been done) -- or NOT. This information must be included in the manuscript.
 Less important points:
 (5) Lines 31 & 32: "up to 92% (77%)" may be fine for advertisements, but it is not sufficiently precise
 for a Scientific article. What does "up to" even mean here? Just state the result.
 (6) The experiment described in the paragraph starting on line 231 using a means (the white/brown
 Y-linked pupa marker) to establish chromosomal sex reversals seems clearly adequate to establish the
 relevant conclusions. Hence there would seem to be no reason to include the other, more indirect,
 presumably preliminary experiment (the paragraph beginning at 214 and described in Fig. 6).
 (7) While tra has (finally) been found to be is present in a number of higher insects and to be involved
 in their sex determination, it is misleading (line 272) to characterize it as being "widely conserved"
 since it evolves so rapidly as to make the orthologs very difficult to identify in even closely related
 species.
 (8) Line 295: It is not necessary to review the functions of various miRNAs. Suffice it to say what is in
 line 294. Nobody doubts miRNAs are functionally important -- these other functions are irrelevant to
 the current paper.
 (9) Fig 3: why refer to "expression levels" rather than simply "levels"?
 (10) Fig 5: Line 753. The figure legend should clearly state WHAT was injected when injections are
 first mentioned, not first in the second part of the figure.
 Fig. 6 (although this figure and its associated text is unnecessary; Fig. 7 suffices). Panel A is
 unnecessary -- the mode of action of CRISPR/Cas9 is well known. The protospacer and PAM sequences
 targeted should simply be included in M&M. If this figure does end up in the final manuscript, the
 authors must indicate that the individuals in red are the PRESUMED feminized males based on an
 expectation of 1:1 sex ratio (actually it is unclear why the authors didn't estimate 25 rather than 24,
 since only 25 would have given a 1:1 sex ratio; moreover the figure would be more clear if the
 estimated number of transformed chromosomal males was indicated IN the red bar, with the number
 of estimated TRUE females indicated IN the white bar).
 Reviewer #2 (Remarks to the Author):
 Sex determination mechanisms are bewilderingly diverse and we are only at the beginning of
 uncovering the various genes involved. Sex is typically determined by a cascade of genes that is
 conserved at the bottom but undergoes frequent turnover at the top (primary signals). This is
 particularly true for the male-determining genes in insects. Four such genes have been described in
 
the last few years from flies and mosquitoes and they are all non-homologous. Intriguingly, although
 they all induce the splicing of transformer and doublesex in the embryonic stage into the male mode,
 they may do so in different ways. Peng et al report the identification of a paternally inherited micro-
 RNA that functions as an (intermediate) male determiner. Although it is not the primary signal (Y-
 linked M factor) it identifies yet another type of regulation of sex is determination in dipteran insects.
 This is an interesting finding that adds to our knowledge of the complexity and evolutionary lability of
 the sex determination process.
 The presented functional analyses with knock-down and induction studies are sound and the results
 are well-presented. Nevertheless, there are some concerns that need to be addressed, or at least be
 acknowledged by the authors. Why was the focus on embryonic stages 6-9 hours? Why did the
 authors not consider identifying the M factor in this study? They appear to have all the material
 (embryonic transcripts) so why not looking at earlier embryonic timepoints?
 The fact that the miR-1-3p is expressed in both males and females rightfully led the authors to
 conclude that it cannot be Y-linked. However, the conclusion that it is autosomal (e.g. line 31) appears
 premature. Can they exclude that it is X-linked? Why did they not attempt to identify it in the genome
 sequence (https://www.ncbi.nlm.nih.gov/assembly/GCF_000789215.1)? If this was not possible, they
 should at least mention this in the text. Can they exclude the existence of multiple copies, one of
 which is on the Y, and transmitted via sperm to eggs?
 The interpretation of the data also requires consideration. It is shown that miR-1-3p is expressed
 more in embryos that were assigned to be XY because these embryos express male tra mRNA. In
 principle this could be caused by this tra splicing. In XX individuals (assigned XX because of the
 presence of female tra mRNA) there is less miR-1-3p, that, in principle, could be caused by TRA. So if
 miR-1-3p lowers tra transcription, it needs to be shown that tra expression in males is lower than in
 females. This may be reflected in the injection experiments, but it should be mentioned. The action of
 miR-1-3p is then likely stabilisation. The target sites described in 133-135 (UTR of a gene?) do not
 reveal if the target is male or female specific (probably not specific). Why not CRISPR the target sites
 of tra? Is the maternally provided tra mRNA also degraded?
 The Introduction lacks coherence and the different paragraphs are unbalanced. The first paragraph
 starts with mentioning the diversity of sex determination mechanisms but then strongly focuses on
 details of the Drosophila sex determination cascade, which is just one example, and an exceptional
 one, that is not related much to the study presented as it does not have an M factor. The second
 paragraph lacks a closing sentence. Focussing the introduction on species that do have M would be
 more appropriate. What was the purpose of the study (cf line 92)? To determine the crucial sex
 determining window, but then the miRNA was accidentally hit upon? If so, present it that way.
 There are a number of inaccurate or in appropriate statements throughout the manuscript:
 - In the title and rest of the text the term “male-biased” is used. The term is not entirely correct as
 the miRNA works before sex determination, i.e. it is not male-biased but male-inducing. The term is
 also confusing with other genomic studies that compare gene expression levels between the sexes.
 - Why calling the M-factor “MDF” as M-factor is typically used in the literature?
 - The piRNAs do not act on tra, and are therefore also inappropriately placed in the intro. In addition
 they are feminizing not masculinizing.
 - Throughout the paper “splicing of tra” or any other gene is used, when the splicing of the pre-mRNA
 (primary transcript) is meant.
 For more specific terminology see below under minor comments
 There are a number of methodological issues:
 - The first experiment described in lines 104-115 is not included in the M&M or is it line 441-442
 (which would be in the wrong spot of the M&M)? Why only take 5-7h for this screen? Taking earlier
 time points would have eliminated the uncertainty whether the 5h amplification is still maternal
 
provision of tra mRNA.
 - N=1 per category is tricky for mixed-sex small RNA datasets, N=3 per non-mixed category is on the
 lower acceptable end for quantitative analyses according to the LGTC.
 - Supplementary table 2 shows the normalized abundance of particular miRNAs and this is the same
 data that was used for the tests (line 130) that showed that these increased significantly at hpo 7
 compared to 5 and 6. How does this work? As in many cases the hpo 7 value is lower than the other
 two categories. The amount of reads after filtering is not noticeably different between the 3 libraries.
 - Why only look at miRNA when the only (?) other known small RNA sex determination factor is a
 piRNA in Bombyx?
 - miR-276a-3p and miR12-5p were suggested from the luciferase assay to target tra, yet these fell of
 the candidate list at the in vivo test. Could they still be involved, but in example earlier than the
 measured 10h post-injection time point? Have they been tested in single-sex samples to examine
 whether they are male-specific?
 - Line 167: where does the identification of Dicer-1 in B. dorsalis come from? Predicted annotation
 from genome assembly? Why are the different sample categories of supplementary figure 6A not
 mentioned in the M&M?
 Minor comments
 Line 23: what is “male determination”?
 Line 27: what is “a male-biased RNA”?
 Line 37: what is “and intermediate male determiner”?
 Lines 59-60: this is not entirely correctly phrased: Mdmd prevents the zygotic activation of the tra
 loop, but not activation of tra itself
 Lines 53-61: The recently discovered M in Musca is inaccurately described. Mentioning the CWC22
 paralog would be appropriate. M in Musca is not necessarily Y-linked. The word “similarly” in line 61 is
 inappropriate.
 Lines 60-61: remove once “splicing”, moreover, genes are not spliced, the transcropts are
 Line 65: “none have yet to be identified” means that they have all been identified!
 Lines 70-76: difficult to read, split up into two sentences. This sentence also contains inaccuracies
 Line 80: SIT is not previously introduced and not well integrated in the text here
 Line 86: should “downstream factors” not be “upstream factors” in the cascade?
 Line 94: what is meant with “a male-biased expression”, better: is expressed only in male embryos?
 Also “Line 195-196: is male-biased expressed in the male embryo”
 Lines 104-114: Looks like the sex of the embryo is determined by assessing the tra spliceforms. It is a
 bit misleading to say that male spliceforms occur in XY embryo’s, if the labelling of XY is derived from
 the identification of such a spliceform.
 Line 116: why do the authors expect such RNAs to be present?
 Line 131: How do you know the miRNAs are autosomal?
 Line 192-193: check phrasing (English)
 Line 194: patter = pattern
 Line 272-273: replace “cases” by “orders” and delete last part of sentence
 Lines 290-297: these seem results that are not described in the result-section itself. Here it just
 distracts from the discussion on candidate primary signals in sex determination.
 Line 296: delete “which”
 Line 322 and throughout the manuscript: The use of “while”. Strictly speaking, “while “is used to refer
 to time, so “whereas” would be the better term
 Line 337: the term “M factor” is introduced here for the first time, needs explanation
 Line 356 hints to the use of this miRNA in other tephritid species. Is it known to be conserved in other
 model systems of this family?
 Line 366-367: why is the sex ratio of the white pupae strain different from 1:1?
 Line 500: “all experiments were repeated at least 3 times” The small RNA sequencing was presumably
 not. Are the other sample sizes mentioned in the manuscript the cumulative number of all these
 experiments, or of the larger main experiment (versus non-described pilot studies)?
 
Reviewer #3 (Remarks to the Author):
 This manuscript by Peng et al. describes a role for miR-1-3p in male sex determination in the oriental
 fruit fly, Bactrocera dorsalis. Key experiments are presented at the end of the paper showing that
 CRISPR-based mutation of miR-1 leads to sex reversal of XY individuals and, conversely, that miR-1
 agomir injections leads to sex reversal of XX individuals. These key experiments are complemented by
 expression and molecular analyses supporting the regulation Bdtra by miR-1. Overall, the experiments
 are technically sound and properly controlled, the results are clearly presented and appropriately
 interpreted and, for the most part, the text is well written. However, there are a few concerns,
 outlined below, that should be addressed to strengthen the manuscript.
 (1) The conclusion that sex determination occurs between 6 and 7 hpo does not seem supported by
 the data. Sex specific splicing is detected at 6 hpo, indicating that the process of sex determination
 has already begun at this time.
 (2) miR-1 expression level should be shown prior to 6hpo in Fig 4C. Presumably there should be a
 sexually dimorphic switch in miR-1 expression that leads to sex-specific splicing of tra at 6 hpo. If
 miR-1 expression is the same at 5 hpo (or 4 hpo) as it is at 6hpo, then it cannot be the presumed
 trigger that causes the switch in tra splicing.
 (3) Ideally, the authors would support the effect of miR-1 on tra with Western blots of Tra protein
 levels in wildtype and miR-1 mutant males and females.
 (4) The authors should show that injection of a miR-1-insensitive version of the tra transcript
 containing a mutation in the putative miR-1 binding site leads to sex reversal of XY individuals. This
 does not seem like a difficult experiment, and would provide significant additional support for the
 model. In addition, the authors could consider analyzing the effects of CRISPR-based mutations in the
 miR-1 binding site of the tra 3’UTR.
 (5) One issue that needs to more fully addressed is how the authors reconcile the sexually dimorphic
 role of miR-1 in Bactrocera dorsalis with its presumably non-dimorphic role in muscle. Is the sexually
 dimorphic expression that the authors describe in Fig 4C specific to early embryogenesis? Is miR-1
 expressed at equivalent levels in males and females at later stages? The authors should show a
 broader temporal profile of miR-1 expression to address these issues.
 (6) I’m not sure that it is appropriate to conclude that miR-8-3p, miR-10-5p, miR-308-3pm, miR-10-
 3p and miR-305-5p don’t regulate Bdtra in human cells (lines 148-149). Isn’t it possible that
 orthologues of these miRNAs are endogenously expressed in HEK293T, leading to luciferase repression
 in the absence of the mimics?
 (7) There are some issues with the writing. Awkward sentences include those on lines 71-76, lines
 107-109, and lines 191-194.
 Minor Comments
 (1) Line 95: miR-1 acts to regulate Bdtra transcription? The authors haven’t shown this, but have
 shown an effect on Bdtra transcript level and splicing.