Genes associated with ant social behavior show distinct transcriptional and evolutionary patterns

While all three reviewers are enthusiastic about the study, several important concerns were voiced by all of them. All reviewers pointed out that this paper does not provide the necessary statistical details to be able to assess the quality of the work. This is certainly the most important concern, as hypothesis acceptance/rejection—which is the central message of the study—fully depends on gene expression analysis and its interpretation. The respective comments are combined below and it will be necessary to address them before a final decision about acceptance can be reached.

The statistical analysis for this project, as for most other bioinformatics projects, is quite complex, and we chose to present the complete analytical pipeline and data as a supplement to make it completely reproducible. We may have relied too much on our supplement containing the complete analysis, omitting details from the main text. In this revision we spent a lot of time addressing statistical questions and included the relevant details in the main text. We also added several additional analyses.

More specifically:

The authors investigate the “novel social genes” vs the “gene toolkit” hypotheses. This is certainly interesting and worthwhile. However, one general issue I have with this (and most other) studies on the topic is that it is not clear what “exactly” constitutes evidence for one hypothesis or the other.

For example, the authors here state that the percentage of genes differentially expressed in the same context in the two ants is small (∼3%). However, the overlap is marginally significant (fifth paragraph of the Results section). So the question is, what percent overlap exactly would constitute support for the toolkit hypothesis? 50%? 25%? 10% 5%?

The point is that it isn't clear how and when authors reject or fail to reject the toolkit/novel hypotheses because there is never an explicit significance or overlap threshold provided. The authors are not alone in having to deal with this issue, and so I don't want to lay this completely at their feet, but it would be nice if they stated explicitly what exactly would constitute evidence, or lack thereof, for the toolkit hypothesis somewhere before they get to the results.

We agree completely. We struggled to come up with a satisfying approach to quantitatively test these hypotheses, but finally came to the conclusion that, as currently described in the literature, both the “genetic toolkit” and “novel social genes” hypotheses are somewhat ambiguous, such that it is not currently possible to really test these hypotheses. Similarly, a recent book chapter by Adam Wilkins (2013) points out that the concept of a developmental genetic toolkit is widely accepted, but it is also very unclear what actually makes up the genetic toolkit, so that the hypothesis is very difficult to actually test. Because these two hypotheses are entrenched in the literature—and the idea of a genetic toolkit underlying social behavior is frequently cited as the major finding of sociogenomic research—we describe them in the Introduction to motivate our work. In the Discussion, we explain how our results fit with these two hypotheses, but then we move on to our main, and we believe, most exciting point: the genes we identified as being associated with ant division of labor show different patterns of connectivity and evolutionary conservation, and thus the genetic architecture of ant division of labor includes both highly connected and conserved genes as well as more loosely-connected and evolutionarily labile genes.

Related to this issue, I wanted more detail about the analyses comparing expression patterns between taxa. Did the authors just ask if the same genes were differentially expressed between behavioral types in the two taxa to be viewed as 'consistent' with the toolkit model? Or did a particular gene have to be differentially expressed in the same direction in both taxa? (The latter, I think, although this wasn't clear.) And did a gene need to be significantly differentially expressed to be counted? Or was it sufficient that it show the same directionality in expression, regardless of significance? Directionality without significance is as important as significance, given that the studies in the taxa had different power, used different methods, etc. These are not trivial issues and they may affect the outcome and interpretation of the results. I urge the authors to look into this more closely.

Following this suggestion we conducted the suggested analysis using the fire ant data. When we look at just the direction of expression, or the fold-change in expression across the genome, we find results very similar to those obtained when we only consider differentially expressed genes. Whereas we previously found a 3.2-3.8 percent overlap in differentially expressed genes between the fire ant and pharaoh ant data set, the analysis based on the correlation of log fold change between nurse and forager samples in the two species involves thousands of genes, but explains only 2% of the variance. So, the results of the two analyses are consistent. This significant but seemingly low overlap is also consistent with previous studies interpreted as supporting the genetic toolkit hypothesis. For example, Woodard et al. (2014) found 18 brain-expressed genes associated with feeding behavior in both the bumblebee Bombus terrestris and the paper wasp Polistes metricus, which was more than expected by chance. Considering only genes with identifiable homologs between the two study species and A. mellifera, this corresponds to an overlap of 7.5% (18/239), but considering all 2,563 identified B. terrestris feeding-associated genes, this corresponds to an overlap of only 0.7% (18/2563).

In the third paragraph: The authors state they are interested in the “molecular mechanisms of social interactions (e.g. social signal production, reception and response)”. They refer to genes related to social behavior throughout the manuscript. But are their expression profiles indeed reflecting social information producing/processing skills? Or morphological changes related to other functions, such as exposure to exterior environments? They do not state they used whole ants or just ant heads for transcriptome profiling, which is highly crucial for interpreting the results (especially given that some other studies have used the animal head).

We agree that these are very important points. We used whole ant bodies and we emphasize this point more in the revised text. We also agree that the differentially expressed genes we observed may be related to a wide range of physiological and behavioral processes, and not just social signal production and response. The underlying physiological processes are particularly intermeshed because by definition, age-based division of labor in social insects means that the individuals are aging as they transition from nursing to foraging tasks. We have clarified these issues in the revised text.

In the third paragraph of the Results section: “Of these contrasts, only foragers and nurses had significantly different gene expression patterns.” This is not well explained. Four categories are compared and 2 of these are said to have different expression. What is the reference here; are the other two categories (grooming and trophallaxis) not different from these two? Or perhaps I am missing something?

This can be partly followed in the Supplementary Material, but should be referred in the main text, e.g. it seems as if all samples were grouped together in the DE analysis. The foragers and nurses were most different as they represent the youngest and oldest. I would have stated this explicitly.

There were four behavioral categories: foragers, nurses, and workers engaged in trophallaxis and grooming. We wished to see which of the categories were transcriptionally distinct from the others, and made comparisons of the focal category vs all of the others. This section was indeed unclear and we re-wrote it with extra detail.

I am also concerned somewhat about the PCA in the Supplementary Material: There seems to be two groups emerging, but this is likely technical (I would guess sample processing dates). It might be difficult to control for this, but if possible, could improve DE analysis significantly.

All the samples were processed simultaneously and in the same facility. We cross-checked the samples, and the two groups don’t correspond to sequencing lanes or to any other discernable categories. The within-sample replicates, except for the loosely defined behavioral category ‘trophallaixis’ are close to each other, suggesting that the biological signal is strong in the data. Most importantly, the separation between the clusters does not correlate with any biological signal detected in the data. Finally, worker samples on the first day of eclosion (age 0) are an outlier on this plot. As these workers are just beginning their transition to adult life, with numerous physiological changes, such as cuticle hardening, it is logical to expect that they would be separate from the others. If we discount these points, there is far less evidence for the existence of separate groups in the scatter.

In the third paragraph of the Results section: “There were 1217 forager- and 1247 nurse-upregulated genes”. What was the p-value cutoff? How did the authors control for multiple-testing? (This can also be followed in the Supplementary Material, but should be referred in the main text.)

We followed the standard practice of 0.05 cutoff after using FDR to adjust for multiple comparisons. We now specify this in the new Statistical Analysis section of the Methods.

In the fourth paragraph of the Results section: “(…) it separated workers into two distinct classes based on age” If I understand what was done, I think the authors might be overinterpreting: the algorithm will separate the profiles into 2 classes if k=2, and n classes if k=n. Thus, without additional analysis I think one cannot decide on the existence of distinct classes. The authors could consider applying some other test; e.g. check the slope of the expression-age curve.

We were interested in testing whether our temporal data could be classified into two groups, corresponding to nurses and foragers, and, if so, where would the transition point be. In the analysis, k=2 refers not to the number of classes, but to the number of nearest neighbors considered by the k-nearest neighbor classifier to make the distinction. We obtain basically the same result with k=2 and k=3, which is within the range of the rule-of-thumb recommendations (references listed in KNN section of the complete analysis). We also include a simple cluster diagram as Figure 1—figure supplement 1, to show that the there is indeed a breakpoint before day 12. We have also clarified the logic behind this analysis in the text.

In the fifth and sixth paragraphs of the Results section: In the gene expression conservation analysis, we are given no information how many genes are used in the comparisons (i.e, the number of genes showing DE in both this and the other datasets, as well as background genes). If the numbers are low, they could instead check the effect size of orthologous genes identified as DE for honeybee, for example. Was the honeybee data generated by Manfredini et al., 2014? If not, the authors should state that.

We added the numbers of genes, which were indeed low, and a parallel analysis using effect sizes (log fold expression change) for fire ants, which produced the same result. Unfortunately, for the honey bee study, only the list of differentially expressed genes is publicly available, so that we could not perform a similar analysis for the honey bee data set. The unavailability of previous data sets is one reason that we have strived to make our full analysis available and completely transparent, as well as making all of the data available.

Most importantly, if the honeybee data was generated from the brain (as done by quite a few studies) and the data in this study from the whole body, this could also be a reason for finding limited overlap.

In comparisons with the Fisher's exact test, it would be useful to state what the background is (non-DE genes, genes up-regulated in the other category, or both?).

The expression “whether genes differentially expressed in these categories of workers were more likely conserved” is a bit confusing, as it also implies sequence conservation, but I think the authors mean conservation with respect to correlated changes.

The honeybee data was indeed generated from the brain, and this is certainly a plausible reason for the low observed overlap. We have added this very important point to our discussion, qualifying our conclusions in this light. In the revised manuscript we focus much less on the proportional overlap of the pharaoh ant and fire ant/honey bee data sets, because of these methodological limitations of the comparisons, and as discussed above, it is difficult to interpret what exactly these overlaps mean.

In the seventh paragraph of the Results section: Connectivity—this could be more explicitly defined, such as emphasizing that the prediction comes from transcription data correlations (e.g. not protein-protein interaction data), and that it depends on how the modules are defined. I think the authors could also discuss potential biases here. Depending on the signal/noise ratio of a gene and the module size, how would connectivity be affected? One would want to make sure that these factors are not influential on the reported result.

We added a more detailed description of WGCNA to the Methods section, including citations to studies evaluating WGCNA performance. For our measure of connectivity, we used the total connectivity of a gene, which is less sensitive to how modules are defined, and most likely reflect the overall role of the gene, beyond the modules we detect in our data set. Although the authors of the WGCNA package suggest that the method can run on normalized count data, in the course of considering potential biases, we found the gene lengths varied somewhat among behavioral categories. We then re-ran the analysis using FPKM data, which are length-standardized. This analysis also captured major network effects, but had a much better fit to the data. In particular, we had to use a smaller soft thresholding level before an approximately scale-free topology of the network was observed (a WGCNA requirement). We were also able to detect many more modules at the same cutoff levels, suggesting greater network resolution.

The most obvious remaining bias from this sort of analysis is that genes with low expression and low variability will not be detected as differentially expressed. Indeed, this effect can clearly be seen in Figure 2B, with the average expression level of non-differentially expressed genes is lower. However, contrary to what you would expect if the pattern was driven by this bias, the nurse-upregulated genes show lower connectivity than non-differentially expressed genes (Figure 2A). We also explicitly control for expression level by including expression level in our GLM analyses.

Figure 2: Would it not be informative to add a violin plot (similar to A and B) for dN/dS? Especially so, as lower conservation among up-regulated genes is one of the paper's main points. But no information is given regarding the magnitude of the effect. The authors could also plot expression versus connectivity.

We have added each of these suggested plots and have also added plots showing the effects of connectivity and expression on whether genes had identifiable fire ant and honey bee orthologs (Figure 3).

In the sixth paragraph of the Results section: There is little discussion on the GO analysis. Does the UV response pathway have to do with sudden exposure to the sun? At least would one not expect to see the same pathway up-regulated in foragers of other taxa?

Please indicate the p-value cutoffs for the GO analysis. This is also found in the Supplementary Material, but should be in the main text or Methods.

We have added further discussion of the GO analysis and include the full set of GO terms enriched for both the forager- and nurse-upregulated genes as well as each module separately. We do not dwell on GO terms since approximately 50% of all genes in our analysis do not even have identifiable orthologs, so we cannot generally be confident about inferring function of differentially-expressed genes or gene modules.

It would be helpful if the authors addressed the following:

What is the estimated genome size? What was the CEGMA assembly score for the de novo genome assembly? What was the average coverage per sample for the genomic and transcriptomic data?

As we mention in response to Reviewer 1, a genome project was not the goal of this study. That being said, as the quality of the reference genome assembly is important to this study, we now include quality control statistics in the Results, such as coverage statistics and CEGMA, as requested. Unfortunately, there is no independently estimated size of the M. pharaonis genome.

The main conclusion that “genes unregulated in foragers and nurses were on average less connected and more rapidly evolving” (ninth paragraph of the Results section) relies heavily on the assumption that they are working with a high-quality transcriptome and that their orthology assignments are correct.

How did they evaluate this? A table with summary statistics would be very useful. How many transcripts had homology to the fire ant and/or the honey bee? How was the paralog problem dealt with, particularly with respect to the molecular evolution analyses?

As with all studies involving gene orthology, particularly with-non models species, there is no genome-wide gold standard that allows the performance of a method to be evaluated. Because the data set is based on transcriptomic data, there will necessarily be false negatives associated with poorly expressed transcripts. That being said, our choice of reciprocal best hit is well justified, based on comparisons of various available methods, as it has high specificity, though at the cost of sensitivity, as it ignores paralogous relationships for genes that have been duplicated in one of the lineages (Chen et al., 2007).

Another important consideration is that we used an independently assembled genome to estimate evolutionary rates. Consequently, our measurements of nucleotide-level changes were not dependent on the quality of the transcriptome, except that some regions of the gene may be missing due to poor transcript coverage. So, transcript quality should not bias the evolutionary rate estimates.

Similarly, for the network analyses: Were these co-expression networks calculated only on significant transcripts or on all transcripts? How was a significant “network” determined? Two of the modules had > 8000 transcripts in each of them. Does that mean all 8000 transcripts show tightly-correlated expression levels?

The networks were calculated using all transcripts and all samples. There are no measures of module significance per se, and the actual module structure may change if different cutoffs are chosen in the analysis (see Supplementary File 2). Indeed, in the current analysis, the number of modules is greater than the original analysis. The effect of cutoff on the number of modules can be seen in the Supplementary File 2. As described above, we use WGNA to estimate total network connectivity (i.e. “kTotal” in WGCNA) for each node (i.e. gene), and present the module trait correlation heat map as a low-dimensional visualization of the underlying transcriptional changes.

As we discuss in the manuscript, the true measure of a module’s validity may be its repeatability across different studies within and between lineages. Thus, it will be important to cross-check the modules found in our data with future studies conducted using comparable methodology. This is another reason we are including the complete data with our analysis.

Finally, why didn't the authors include Polistes in their comparative analyses? There are at least 2 studies on Polistes, both of which are already cited in this manuscript. This seems like it would be another independent data point worth discussing.

The Polistes paper wasp studies focus on reproductive division of labor between queens and workers and do not include data on worker age polyethism, and are thus not directly comparable with our study. Even though age polyethism is thought to be widespread in social insects, the transcriptomic basis of age polyethism has only been studied in the honey bee Apis mellifera and the fire ant Solenopsis invicta, with the fire ant study only comparing the two extremes of workers inside the nest and workers outside the nest (Manfredini et al., 2014).