A histone demethylase links the loss of plasticity to nongenetic inheritance and morphological change

Plasticity is a widespread feature of development, enabling phenotypic change based on the environment. Although the evolutionary loss of plasticity has been linked both theoretically and empirically to increased rates of phenotypic diversification, molecular insights into how this process might unfold are generally lacking. Here, we show that a regulator of nongenetic inheritance links evolutionary loss of plasticity in nature to changes in plasticity and morphology as selected in the laboratory. Across nematodes of Diplogastridae, which ancestrally had a polyphenism, or discrete plasticity, in their feeding morphology, we use molecular evolutionary analyses to screen for change associated with independent losses of plasticity. Having inferred a set of ancestrally polyphenism-biased genes from phylogenetically informed gene-knockouts and gene-expression comparisons, selection signatures associated with plasticity’s loss identify the histone H3K4 di/monodemethylase gene spr-5/LSD1/KDM1A. Manipulations of this gene affect both sensitivity and variation in plastic morphologies, and artificial selection of manipulated lines drive multigenerational shifts in these phenotypes. Our findings thus give mechanistic insight into how traits are modified as they traverse the continuum of greater to lesser environmental sensitivity.

3.By ablating spr-5 and blocking the function of its protein product (which demethylates histone H3K4), the genetically assimilated phenotypes were recapitulated in the lab, and mutants demonstrated increased phenotypic variance.The latter conclusion suggests that mutations to spr-5 in nature may act as a capacitor for subsequent evolutionary change by revealing new phenotypic targets to selection.
4.The polyphenic effects of spr-5 carried through one generation, indicating that spr-5 can mediate plasticity transgenerationally.
5.In 10 generations of artificial selection on epigenetic variation, the authors selected for both increased and decreased production of the Eu morph.Thus, they demonstrated that selection on epigenetic variation can lead to the evolutionary shifts in plastic responses (i.e., genetic accommodation broadly, genetic assimilation specifically).

Validity
Based upon my expertise (see below for more information), I found the data interpretations to be valid and compelling.Not only were the results of individual approaches valid, but the fact that multiple, complementary approaches reinforced a variety of conclusions was especially convinving.For example, the potential role of spr-5 in genetic assimilation was established by ablating the gene, blocking its product, and through artificial selection.

Significance
For more than a century, and increasingly in the past few decades, a variety of theories have been proposed regarding whether and how non-genetic phenomena such as phenotypic plasticity and trans-generational epigenetic modifications might constrain, promote, or otherwise modify the trajectory of adaptive evolution.Accumulating empirical evidence has supported some of these ideas, which are the subject of a major debate within Evolutionary Biology (i.e., whether the Modern Synthesis should be revised as the Extended Evolutionary Synthesis to account for these less traditional mechanisms).However, few, if any, papers that I can recall address these issues in such a thorough and detailed way.This manuscript describes a series of complementary studies and experiments through which several of these important threads are woven together with convincing empirical support.These include the roles of genetic assimilation of previously plastic responses, trans-generational inheritance of epigenetic modifications, and the potential for non-genetic variation to act as evolutionary capacitor.In my view, this is an exceptional paper that is likely to become a classic study of the mechanistic basis genetic assimilation, epigenetic inheritance, and their evolutionary consequences.The integration of bioinformatics, comparative transcriptomics, direct genetic manipulation, morphometrics, and experimental evolution paint an extraordinarily detailed and compelling picture of how genetic assimilation has likely repeatedly occurred in this genus of nematodes, and how the mechanism of genetic assimilation might act as a capacitor for further evolutionary change.
Data and Methodology I judged the methods to be elegant, logical, and mutually supportive.The data appear valid and reliable, insofar as my expertise allows me to fully evaluate them.While I do not directly engage in molecular approaches in my own lab, I collaborate biologists who do, and am confident in my ability to evaluate the results of molecular studies with respect to questions of mechanisms of evolutionary and trans-generational inheritance.I cannot comment on the validity of the molecular methods, but the interpretation of their results seem sound.I do have expertise in morphometric methods, and I do find these approaches and results to be valid.

Analytical approach
The analytical approaches are valid.
Suggested Improvements I have only minor suggested improvements: Fig. 1A-Is this phylogeny reproduced from reference 7 (Fig. 2 therein), or generated as part of the comparative genomic tests for genetic assimilation?I suspect the phylogeny came from reference 7, which would then be used to identify comparisons of interest for the comparative genomic analysis described in the present study.If that's the case, then the figure legend should cite reference 7.
296: change to "were scored" instead of "where scored" 298: I interpret "under standard laboratory conditions" to indicate that individuals from these three strains were raised in conditions that typically generate low proportions of the Eu morph.Can the authors cite a reference for their "standard laboratory conditions," or otherwise describe them briefly?Given that the authors are investigating a polyphenism, the details of the environmental conditions are important.
306: What R version, and which R package(s) were used?

Clarity and Context
The text is well-written and the figures and tables are clear, thorough, and should be accessible to a wide audience.This clarity is especially important given that this manuscript uses a variety of integrative approaches, so any given reader might not be expert in every aspect of the paper.

References
The refences cited are appropriate in that they support the broad theoretical basis of the manuscript, as well as the methodological approaches.
Reviewer Expertise My expertise is in the role of plasticity in evolutionary adaptation, particularly with respect to the evolution of morphology.I collaborate on projects involving bioinformatic and genomic approaches, so I feel confident in my ability to evaluate the rationale and results of all aspects of the manuscript.However, I do not myself use molecular techniques, so I am not an expert in the specific methodologies by which these results are generated.
Reviewer #2 (Remarks to the Author): The article 'A regulator of nongenetic inheritance mediates the evolution and loss of plasticity' by Levis and Ragsdale reports the finding of a histone tail modifying enzyme (spr-5) that is associated with morph-biased gene expression between two types of feeding morphology and that has been under positive selection in two lineages that are fixed for one type of feeding morphology.Since spr-5 is also a known and demonstrated mediator of epigenetic inheritance, the authors interpret spr-5 as an "epigenetic bridge" that enables (transgenerational) plasticity and that is the target of selection during genetic assimilation.
The manuscript is addressing an interesting idea and presents some suggestive results that are broadly consistent with these ideas.However, the presented data is also consistent with a number of alternative interpretations (see below) that are not sufficiently acknowledged, and conclusion do not rigorously follow from the results.Several additional lines of evidence would be require to makes this a truly convincing piece of work.For example, more information on the function of spr-5 in the lineages that are fixed for one morph would be desirable and strengthen the case.I have several major criticisms about the rationale presented in the study and the soundness of the interpretations.
Given the evidence presented, the authors make quite far-reaching statements.For example, in lines 51-53: the authors have established two lines with knock-outs in two switch genes that cause the nematodes to constitutively express one of the two morphs.Using differential gene expression between the two lines, they identify genes with a morph-biased gene expression.Having done this for two Pristionchus species and retaining the overlap of these morph-biased gene, they claim that they identified a 'core set of environmentally sensitive genes ancestral to Pristionchus'.Calling these genes 'environmentally sensitive' is quite a stretch since they really are differentially expressed between two mutant lines, and it is far from given that the transcriptomic signature of a CRISPR-induced morph is the same as that of an environmentally-induced morph.As a side, the reader is never told what environmental cue naturally induces the morphs.Why are not naturallyoccurring morphs used to identify a set of environmentally sensitive genes?In addition, using two species with unclear phylogenetic positions (after all the reader is told, those could be very closely related, highly derived sister species) is not strong evidence for the set of 'genes inferred to be ancestral to the entire genus' (line 53).
-selection-based analysis (lines 54-70): This section would greatly benefit from more details and it's very hard to interpret how convincing the data actually is.How many genes were identified as positively selected in the two species that allegedly recently lost plasticity?How many genes in the two species that lost plasticity longer ago?Also, no evidence is provided that the two events of plasticity loss are actually on different time scales since the phylogeny in Fig. 1 is not dated.Related to this, I am not convinced that looking for genes that have experienced positive selection in the past is the right type of analysis here.Why would a gene with a morph-biased expression be under positive selection in a lineage constitutively expressing one of the morphs?Given the direction of morph-biased expression, a really important gene might as well has become pseudogenized or lost its function in the lineage that fixed the morph in which it's not expressed.At the very least, the analysis should be performed directional, meaning to look for overlap of type-A-biased genes that are under positive selection in species only exhibiting type-A (but not type-B) morphologies.At present, this analysis seems poorly thought-through, superficially conducted and insufficiently described.
-the authors selected spr-5 among the 19 genes that were identified as having a morph-biased gene expression in Pristionchus and having experienced positive selection in at least one species of the two lineages that lost plasticity.What about the other 18 genes?Given their equally strong association with the morphs as spr-5, it is well conceivable that their ablation might also have caused differences in the morph-expression, similar to spr-5.What would this mean for the interpretation of the role of spr-5?-arguably using a loss of spr-5 function to test whether this modification could allow directional selection upon new morphologies as observed in species with fixed morphs is not ideal.Ablating gene function is rather the opposite of mimicking the effect of positively selected alleles, and therefore I am not sure what the biological relevance of a spr-5-negative organism in the context of this study is.Since the logic here is reverse to what I would have thought is relevant to test, I do not follow the interpretation of the authors, and the far-reaching conclusion that they draw based on this experiment.
-minor question: are the 838 genes identified as differentially expressed in both species concordantly differentially expressed?I.e., are the 838 genes up-and down-regulated in the same morphs between the two species?If not, those genes should be filtered to retain only those with consistent expression changes since the disconcordant ones are probably false-positives.
Overall, I find the presented ideas interesting and the presented results suggestive, but there are several important gaps in the logic that unfortunately mean that the conclusions are not fully supported by the presented evidence.

Key Results
This manuscript describes an integrative and complementary set of approaches to address the roles of developmental plasticity and epigenetic inheritance in evolutionary processes.Using a clade of nematode worms that exhibit an ancestral trophic polyphensim, and which has undergone repeated episodes of genetic assimilation, the authors come to the following main conclusions: 1.The polyphenic switch mechanisms characterized in the model P. pacificus are general to the genus, and thus can be manipulated to identify morph-biased genes ancestral to the entire Pristionchus clade.
2.Independent episodes of genetic assimilation in Pristionchus have involved positive selection on a similar set of morph-biased genes.One of these genes, spr-5, is a known regulator of trans-generational, epigenetic inheritance, suggesting that evolutionary changes to this epigenetic modifier may be an important mechanism of genetic assimilation.
3.By ablating spr-5 and blocking the function of its protein product (which demethylates histone H3K4), the genetically assimilated phenotypes were recapitulated in the lab, and mutants demonstrated increased phenotypic variance.The latter conclusion suggests that mutations to spr-5 in nature may act as a capacitor for subsequent evolutionary change by revealing new phenotypic targets to selection.
4.The polyphenic effects of spr-5 carried through one generation, indicating that spr-5 can mediate plasticity transgenerationally.
5.In 10 generations of artificial selection on epigenetic variation, the authors selected for both increased and decreased production of the Eu morph.Thus, they demonstrated that selection on epigenetic variation can lead to the evolutionary shifts in plastic responses (i.e., genetic accommodation broadly, genetic assimilation specifically).

Validity
Based upon my expertise (see below for more information), I found the data interpretations to be valid and compelling.Not only were the results of individual approaches valid, but the fact that multiple, complementary approaches reinforced a variety of conclusions was especially convinving.For example, the potential role of spr-5 in genetic assimilation was established by ablating the gene, blocking its product, and through artificial selection.

Significance
For more than a century, and increasingly in the past few decades, a variety of theories have been proposed regarding whether and how non-genetic phenomena such as phenotypic plasticity and trans-generational epigenetic modifications might constrain, promote, or otherwise modify the trajectory of adaptive evolution.Accumulating empirical evidence has supported some of these ideas, which are the subject of a major debate within Evolutionary Biology (i.e., whether the Modern Synthesis should be revised as the Extended Evolutionary Synthesis to account for these less traditional mechanisms).However, few, if any, papers that I can recall address these issues in such a thorough and detailed way.This manuscript describes a series of complementary studies and experiments through which several of these important threads are woven together with convincing empirical support.These include the roles of genetic assimilation of previously plastic responses, trans-generational inheritance of epigenetic modifications, and the potential for non-genetic variation to act as evolutionary capacitor.In my view, this is an exceptional paper that is likely to become a classic study of the mechanistic basis genetic assimilation, epigenetic inheritance, and their evolutionary consequences.The integration of bioinformatics, comparative transcriptomics, direct genetic manipulation, morphometrics, and experimental evolution paint an extraordinarily detailed and compelling picture of how genetic assimilation has likely repeatedly occurred in this genus of nematodes, and how the mechanism of genetic assimilation might act as a capacitor for further evolutionary change.
Data and Methodology I judged the methods to be elegant, logical, and mutually supportive.The data appear valid and reliable, insofar as my expertise allows me to fully evaluate them.While I do not directly engage in molecular approaches in my own lab, I collaborate biologists who do, and am confident in my ability to evaluate the results of molecular studies with respect to questions of mechanisms of evolutionary and trans-generational inheritance.I cannot comment on the validity of the molecular methods, but the interpretation of their results seem sound.I do have expertise in morphometric methods, and I do find these approaches and results to be valid.

Analytical approach
The analytical approaches are valid.

Clarity and Context
The text is well-written and the figures and tables are clear, thorough, and should be accessible to a wide audience.This clarity is especially important given that this manuscript uses a variety of integrative approaches, so any given reader might not be expert in every aspect of the paper.

References
The refences cited are appropriate in that they support the broad theoretical basis of the manuscript, as well as the methodological approaches.
Reviewer Expertise My expertise is in the role of plasticity in evolutionary adaptation, particularly with respect to the evolution of morphology.I collaborate on projects involving bioinformatic and genomic approaches, so I feel confident in my ability to evaluate the rationale and results of all aspects of the manuscript.However, I do not myself use molecular techniques, so I am not an expert in the specific methodologies by which these results are generated.

Suggested Improvements
I have only minor suggested improvements: Fig. 1A-Is this phylogeny reproduced from reference 7 (Fig. 2 therein), or generated as part of the comparative genomic tests for genetic assimilation?I suspect the phylogeny came from reference 7, which would then be used to identify comparisons of interest for the comparative genomic analysis described in the present study.If that's the case, then the figure legend should cite reference 7.    296: change to "were scored" instead of "where scored"   298: I interpret "under standard laboratory conditions" to indicate that individuals from these three strains were raised in conditions that typically generate low proportions of the Eu morph.Can the authors cite a reference for their "standard laboratory conditions," or otherwise describe them briefly?Given that the authors are investigating a polyphenism, the details of the environmental conditions are important.  Escherichia coli   306: What R version, and which R package(s) were used?   Reviewer #2 (Remarks to the Author): The article 'A regulator of nongenetic inheritance mediates the evolution and loss of plasticity' by Levis and Ragsdale reports the finding of a histone tail modifying enzyme (spr-5) that is associated with morph-biased gene expression between two types of feeding morphology and that has been under positive selection in two lineages that are fixed for one type of feeding morphology.Since spr-5 is also a known and demonstrated mediator of epigenetic inheritance, the authors interpret spr-5 as an "epigenetic bridge" that enables (transgenerational) plasticity and that is the target of selection during genetic assimilation.    The manuscript is addressing an interesting idea and presents some suggestive results that are broadly consistent with these ideas.However, the presented data is also consistent with a number of alternative interpretations (see below) that are not sufficiently acknowledged, and conclusion do not rigorously follow from the results.Several additional lines of evidence would be require to makes this a truly convincing piece of work.For example, more information on the function of spr-5 in the lineages that are fixed for one morph would be desirable and strengthen the case.I have several major criticisms about the rationale presented in the study and the soundness of the interpretations.Given the evidence presented, the authors make quite far-reaching statements.For example, in lines 51-53: the authors have established two lines with knock-outs in two switch genes that cause the nematodes to constitutively express one of the two morphs.Using differential gene expression between the two lines, they identify genes with a morph-biased gene expression.Having done this for two Pristionchus species and retaining the overlap of these morph-biased gene, they claim that they identified a 'core set of environmentally sensitive genes ancestral to Pristionchus'.Calling these genes 'environmentally sensitive' is quite a stretch since they really are differentially expressed between two mutant lines, and it is far from given that the transcriptomic signature of a CRISPR-induced morph is the same as that of an environmentallyinduced morph.As a side, the reader is never told what environmental cue naturally induces the morphs.Why are not naturally-occurring morphs used to identify a set of environmentally sensitive genes?In addition, using two species with unclear phylogenetic positions (after all the reader is told, those could be very closely related, highly derived sister species) is not strong evidence for the set of 'genes inferred to be ancestral to the entire genus' (line 53).
"Our approach used genetic perturbations in common genetic backgrounds and environmental conditions, which allowed us to distinguish genes associated with the polyphenism per se from others whose expression might also be variously influenced by environmental cues [Forsman 2015 Heredity].Further, this approach excluded effects that might be idiosyncratic to individual cues, which in Pristionchus include crowding, starvation, and other metabolic influences [Bento et al. 2010  -selection-based analysis (lines 54-70): This section would greatly benefit from more details and it's very hard to interpret how convincing the data actually is.How many genes were identified as positively selected in the two species that allegedly recently lost plasticity?How many genes in the two species that lost plasticity longer ago?Also, no evidence is provided that the two events of plasticity loss are actually on different time scales since the phylogeny in Fig. 1 is not dated.Related to this, I am not convinced that looking for genes that have experienced positive selection in the past is the right type of analysis here.Why would a gene with a morph-biased expression be under positive selection in a lineage constitutively expressing one of the morphs?Given the direction of morph-biased expression, a really important gene might as well has become pseudogenized or lost its function in the lineage that fixed the morph in which it's not expressed.At the very least, the analysis should be performed directional, meaning to look for overlap of type-A-biased genes that are under positive selection in species only exhibiting type-A (but not type-B) morphologies.At present, this analysis seems poorly thought-through, superficially conducted and insufficiently described."We next tested if the strength of selection acting on genes in each of our assimilated species has been relaxed relative to the strength acting on polyphenic species.Our rationale was threefold: first, plasticity can be lost due to selection or drift [Pál and Miklós 1999;Pigliucci et al. 2006;Masel et al. 2007;Vigne et al. 2021]; second, genes not associated with the phenotype that was canalised during genetic assimilation might have experienced relaxed selection following plasticity's loss [West-Eberhard 2003;Van Dyken and Wade 2010]; third, this analysis would identify additional targets whose evolutionary history is similar during independent cases of assimilation.As with our inference of positive selection, we observed a limited set of once polyphenism-biased genes (18 total) with signatures of relaxed selection across both assimilation events (Extended Data Table 3).Moreover, five of these genes were also present in our set of shared genes experiencing positive selection.This suggests that accumulated variation in these genes-whether by selection, drift, or both-is an important contributor to genetic assimilation and its associated diversification.These comparisons thus point to a set of once morph-biased genes that were potentially key targets of evolution associated with multiple, independent losses of developmental plasticity in Diplogastridae.
-the authors selected spr-5 among the 19 genes that were identified as having a morph-biased gene expression in Pristionchus and having experienced positive selection in at least one species of the two lineages that lost plasticity.What about the other 18 genes?Given their equally strong association with the morphs as spr-5, it is well conceivable that their ablation might also have caused differences in the morph-expression, similar to spr-5.What would this mean for the interpretation of the role of spr-5?         spr-5   spr-5  -arguably using a loss of spr-5 function to test whether this modification could allow directional selection upon new morphologies as observed in species with fixed morphs is not ideal.Ablating gene function is rather the opposite of mimicking the effect of positively selected alleles, and therefore I am not sure what the biological relevance of a spr-5-negative organism in the context of this study is.Since the logic here is reverse to what I would have thought is relevant to test, I do not follow the interpretation of the authors, and the farreaching conclusion that they draw based on this experiment.
-minor question: are the 838 genes identified as differentially expressed in both species concordantly differentially expressed?I.e., are the 838 genes up-and down-regulated in the same morphs between the two species?If not, those genes should be filtered to retain only those with consistent expression changes since the disconcordant ones are probably false-positives.    Overall, I find the presented ideas interesting and the presented results suggestive, but there are several important gaps in the logic that unfortunately mean that the conclusions are not fully supported by the presented evidence.   Levis & Ragsdale have revised their manuscript entitled 'A regulator of nongenetic inheritance mediates the evolution and loss of plasticity' in the light of my and others' comments.The authors have made some modifications to the MS and added additional analyses in an attempt to strengthen their arguments.However, I find that substantial weaknesses remain, and several claims are not sufficiently supported by the results.
The most problematic claim is that spr-5 has played a role in assimilation (and exaggeration) or feeding morphologies in nature (abstract, lines 7-8).In response to my previous comment, the author have added a test for relaxed selection in addition to the test for positive selection.Unfortunately, addition of this test exposed severe problems with these analyses: the gene spr-5 is identified as both under diversifying/positive as well as under relaxed selection in the very same lineages (Pbu + Pel + Ltex).This result is simply not possible and probably a sign of some deeper issue with these analyses.It is also more than unfortunate that the authors have chosen to show these results only in the Extended Data, since the results of these analyses would be highly relevant for the reader.
In addition to this major issue, the set-up of the selection analyses are convoluted and the reporting is not logical: rather than analyzing all data (lineages) at once, the authors chose to first use a taxonomicallyrestricted dataset, and then a larger dataset.However, the results of these analyses are not sufficiently reported, and the rationale for this 2-step-approach is not justified.It is also unclear if the morph-biased genes identified in these selection analyses are more than one would expect to find based on chance alone (Extended Data Table 1 should contain this information).
Since I do not think that the presented results supports the main claim of the paper, namely that evolutionary modification of spr-5 has 'mediated the evolution and loss of plasticity' (title), I recommend the authors to reconsider the framing of the study.Showing that spr-5 has an effect on the expression and environmental sensitivity of mouth morphologies in lab strains of 2 species is not sufficient to conclude that this gene has actually played a role during the evolutionary process.Large parts of the manuscript (abstract lines 14-18) are mere speculations and reach far beyond the actual results reported in the study.
In order to strengthen the role of spr-5 in mediating evolution and loss of plasticity via nongenetic inheritance, the following evidence would be required: -the role of spr-5 in evolutionary lineages with modified feeding morphologies should be investigated in more detail.Part of this could be rigorous selection test, but also analyses of spr-5 expression levels.The current paper hones in on coding-changes as the only possible mechanism of change in a gene's function over time, but expression levels are equally plausible mechanisms (perhaps more so for plasticity-led evolution).
-the suggested mechanism of transgenerational inheritance via di-methylation of H3K4 marks should be substantiated.The fact that Bizine induces a phenocopy of the spr-5 mutant is suggestive, but actual analyses of histone tail modifications (e.g. through CHIP-seq) would be required to robustly establish inheritance of histone modification as the mechanism of transgenerational persistence of the phenotype.
-to make the argument that spr-5-mediated epimutations fuel transgenerational shifts in plasticity and morphology (last section of results), the selection experiments should be repeated with the appropriate control, namely an inbred wild-type strain.The authors refer to Ref. 15 saying that selection on inbred lines fails to drive any shift, but this test should be repeated as replicate along with the spr-5 lines and shown alongside in Fig. 4B.

Minor comment:
-line 224: 'for that phenotype' should be delete.The fact that spr-5 plays a role in DNA damage repair might facilitate accumulation of new variation in general, but not specifically for that phenotype.

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Reviewer #2 (Remarks to the Author): Levis & Ragsdale have revised their manuscript entitled 'A regulator of nongenetic inheritance mediates the evolution and loss of plasticity' in the light of my and others' comments.The authors have made some modifications to the MS and added additional analyses in an attempt to strengthen their arguments.However, I find that substantial weaknesses remain, and several claims are not sufficiently supported by the results.
The most problematic claim is that spr-5 has played a role in assimilation (and exaggeration) or feeding morphologies in nature (abstract, lines 7-8).In response to my previous comment, the author have added a test for relaxed selection in addition to the test for positive selection.Unfortunately, addition of this test exposed severe problems with these analyses: the gene spr-5 is identified as both under diversifying/positive as well as under relaxed selection in the very same lineages (Pbu + Pel + Ltex).This result is simply not possible and probably a sign of some deeper issue with these analyses.It is also more than unfortunate that the authors have chosen to show these results only in the Extended Data, since the results of these analyses would be highly relevant for the reader.2) In addition to this major issue, the set-up of the selection analyses are convoluted and the reporting is not logical: rather than analyzing all data (lineages) at once, the authors chose to first use a taxonomically-restricted dataset, and then a larger dataset.However, the results of these analyses are not sufficiently reported, and the rationale for this 2-step-approach is not justified.It is also unclear if the morph-biased genes identified in these selection analyses are more than one would expect to find based on chance alone (Extended Data Table 1 should contain this information).     spr-5       Since I do not think that the presented results supports the main claim of the paper, namely that evolutionary modification of spr-5 has 'mediated the evolution and loss of plasticity' (title), I recommend the authors to reconsider the framing of the study.Showing that spr-5 has an effect on the expression and environmental sensitivity of mouth morphologies in lab strains of 2 species is not sufficient to conclude that this gene has actually played a role during the evolutionary process.Large parts of the manuscript (abstract lines 14-18) are mere speculations and reach far beyond the actual results reported in the study.
In order to strengthen the role of spr-5 in mediating evolution and loss of plasticity via nongenetic inheritance, the following evidence would be required: -the role of spr-5 in evolutionary lineages with modified feeding morphologies should be investigated in more detail.Part of this could be rigorous selection test, but also analyses of spr-5 expression levels.The current paper hones in on coding-changes as the only possible mechanism of change in a gene's function over time, but expression levels are equally plausible mechanisms (perhaps more so for plasticity-led evolution).  only   spr-5    spr-5  -the suggested mechanism of transgenerational inheritance via di-methylation of H3K4 marks should be substantiated.The fact that Bizine induces a phenocopy of the spr-5 mutant is suggestive, but actual analyses of histone tail modifications (e.g. through CHIP-seq) would be required to robustly establish inheritance of histone modification as the mechanism of transgenerational persistence of the phenotype.  spr-5         spr-5P.pacificus      spr-5     -to make the argument that spr-5-mediated epimutations fuel transgenerational shifts in plasticity and morphology (last section of results), the selection experiments should be repeated with the appropriate control, namely an inbred wild-type strain.The authors refer to Ref. 15 saying that selection on inbred lines fails to drive any shift, but this test should be repeated as replicate along with the spr-5 lines and shown alongside in Fig. 4B Nature; Bose et al. 2012 Angew Chem; Werner et al. 2017 Sci Rep]."