Reviewer's report 1
Ron Fouchier, National Influenza Center and Department of Virology, Erasmus Medical Centre, Rotterdam, The Netherlands (nominated by Andrey Rzhetsky)
In the manuscript, in particular in the abstract, the authors refer to phenotype changes while the phenotype is only INFERRED from genetic data. For instance, antigenic changes are inferred from amino acid replacements in proposed epitopes, and changes in virus fitness are inferred from rapid displacement of existing lineages. It would be better to stick to the facts; e.g. refer to amino acid substitutions in antigenic sites rather than antigenic change and to use the term fitness with more care.
Author response: Antigenic changes are not, exactly, inferred from changes in the (proposed) epitopes but, of course, when we notice differential patterns for replacements in the epitope regions, we believe that it makes sense to interpret these differences as being relevant to the evolution of the virus antigenicity and fitness. We went through the corresponding language throughout the paper and made minor changes, in particular, in the Abstract, to emphasize that we are talking about "apparent" antigenic changes. As far as viral fitness is concerned, there is no inference involved inasmuch as the rate of displacement of pre-existing lineages is what, actually, defines fitness. Thus, apart from the aforementioned small modifications, we believe that we have been sticking to the facts to begin with.
Background, 4th paragraph, and Results, 3nd paragraph, and Methods section Please specify the "antigenic positions of the HA1 domain". The paper by Ratner et al. is in Russian, which is not a language that everyone is familiar with. The method section further refers to a statistical analysis and a structural analysis, without providing us with a list of positions that are considered to represent epitopes. It is tricky to take either of these papers as the gold standard for where the epitopes are located. It would thus be good to list the "antigenic positions" in HA1 here.
Author response: The problem here is that the positions of the epitopes in the particular isolate for which they have been reported were projected on the multiple alignment of the HA sequences. Thus, the specific coordinates in that particular isolate would hardly help much. In the revision, we expanded the explanation of the procedure under Methods (section on Analysis of Selection Pressures, 2nd paragraph). The relevance of Ratner's paper here is unclear as it is not about antigenic positions per se but about evidence of positive selection in HA. We felt that it was highly desirable to cite this paper as the first one (to our knowledge) that presented such evidence. It is available in English translation.
Background, last paragraph, Results, 4th paragraph, and Discussion section on "bias" While I fully agree that the influenza sequence databases are heavily biased towards "outlier" strains (with unusual antigenic properties as compared to other viruses isolated during the same epidemic), it is incorrect to assume that the sequence collection analyzed here is not biased. First of all, the sequences are primarily from short epidemics in New York State and New Zealand. With a virus that circulates (and evolves) globally, this bias has large implications for the type of work described here. In addition to geography, there may be several other biases (sampled patient populations, inclusion criteria for the sequencing project, etc.) that could affect the fitness discussions that follow. The authors have not addressed this issue at all, and simply assume that their dataset is good enough. I am not so sure.
Author response: This is, indeed, an important issue, and we agree that we did not address it in sufficient detail in the original version. However, there are relatively straightforward arguments to the effect that geographical or other bias is extremely unlikely to account for the pattern of stasis-rapid change that we consistently observe in influenza evolution. These arguments are presented in the revision (Discussion, 6th paragraph).
Results, 2nd paragraph:
It is not clear to me what the results described here add to the information provided in the papers by Barr et al., and Holmes et al. that described the reassortant viruses in detail (refs [7
] and [8
]). Could thus be shortened.
Author response: Surely, these papers have described the reassortant viruses. However, a critical facet is missing there, namely, the demonstration that "...reassortant strain is completely replaced by the non-reassorted Fujian strain ("late Fujian") from 2004 onwards" (quote from our revised paper, Results, 2nd paragraph; so this clarification was added.
Results, 2nd paragraph from the end:
Only data from the US are included, when the authors state that 2000–2001 and 2002–2003 were H1N1 seasons. While this may be true in the US, it certainly was not true for many other parts of the world. Should the competition between fit and less fit variants of H3N2 viruses and those of the H1N1 subtype not be considered at the global scale? Surely, with influenza viruses moving from Northern hemisphere to Southern hemisphere and back with the seasons, the viruses evolve and compete on a global scale, not just in the US.
Author response: The pattern was the same for New York State and New Zealand which is shown in the revised Figure . We do not have comparable depth of data for other parts of the world, unfortunately.
On the analyses of H1N1 strains (results and discussion)
The authors indicate that there was no positive selection in H1N1. Despite the apparent lack of positive selection, there have been vaccine updates in H1N1 strains because of antigenic drift between 1995 and 2005 (e.g. A/New Caledonia/2000). The question than arises; Do we need positive selection for antigenic drift to occur? If not, we cannot rely on sequences to identify when vaccine updates are necessary?
Author response: We never claimed that antigenic drift strictly requires positive selection. What we do claim is that there is no evidence of substantial positive selection in H1N1 during the analyzed time interval, and accordingly, the dominance of H1N1 in some seasons was caused by the lack of highly fit H3N2 isolates rather than by emergence of novel and highly fit H1N1 viruses. In order to present the data on H1N1 evolution in a more compelling manner, we included Figure which shows the extensive mixing of isolates from different years in the phylogenetic tree of H1N1.
I have some doubts about the interpretation of periods of "stasis" and of "rapid evolution". Could this distinction not be primarily due to incomplete nature of the sequence set, temporally and spatially? While there may be relative stasis locally among the strains that were sequenced in certain seasons in NY or NZ, using a "perfect" dataset (every single flu strain globally is sequenced) the authors would probably find "rapid evolution" somewhere at any given time? This then would raise the question of how predictable the "rapid evolution" would be, and how useful such analyses would be in predicting the dominant strains of the next season.
Author response: As indicated above, this is an important issue but we believe it is, effectively, logically impossible to explain our conclusions by the incompleteness of the data (Discussion, 6thparagraph).
On the final conclusion of the authors that the common view of influenza virus evolution as a positive selection-driven process is incomplete
I am not convinced that the view of long periods of stasis punctuated by short periods of fitness described here is not primarily due to the use of a biased dataset. If the authors disagree with this opinion (which I guess they would) it would be good to discuss the issue of bias, rather than just waiving it.
Author response: Yes, we do disagree, i.e., we do not see how the present results can be explained by biases in the data and we did include the relevant discussion (see the responses above).
I found the parallel amino acid replacements in different genetic lineages interesting.
The last point worth mentioning is that prediction of the predominant strain of the next influenza season is not the primary task of the influenza surveillance network that serves the WHO vaccine strain selection process. The primary task is to identify the emergence of strains that are antigenically distinct and (as the result) will dominate the next season. This way, the number of vaccine strain updates can remain limited, which is important because of cost, the interest of vaccine manufacturers, and perhaps vaccine efficacy. It is unnecessary to update the vaccine based on genetic changes that do not affect the antigenic properties of the virus.
Author response: We certainly never claimed that it is necessary to change (update) the vaccine on the basis of sequence changes per se. The salient considerations are different: i) it might be possible to predict the future dominant strains by sequence comparison, ii) the HI test is not necessarily reflective of all relevant antigenic changes, so sequence analysis might help identify other such changes.
Reviewer's report 2
David Krakauer, The Santa Fe Institute
Review of "Punctuated interpandemic evolution of influenza A virus"
The recent availability of broadly sampled influenza genomes spanning the years 1995–2005 provides an opportunity for a systematic analysis of genetic trends correlated with the emergence of flu pandemics. In this paper, the authors adopting a phylogenetic framework, report a punctuated mode of virus evolution, in which diversity accumulates during periods of stasis and outbreaks are facilitated by selection against common strains. Epistasis among sites of the HA gene provide one explanation for the "neutral" delays attending new outbreaks, where multiple compensatory changes are required for fixation of a new adaptive variant. This paper nicely serves to illustrate that a constant rate model for microbial evolution, in which virulence is treated in terms of the independent contribution of amino acids in an epitope, coupled to a simple competitive exclusion principle based on replicative advantage, is too simple. Rather, new strains can be generated neutrally long before their advantages are felt in a new selective context, where this context shifts according the efficacy of host immunity to dominant epitopes and the rates of recombination events promoting antigentic shift. I find the research very interesting, but I do find, however, the final discussion of vaccine development a little gratuitous given the findings of the paper and perhaps an unnecessary appeal to the utility of basic research.
Author response: We appreciate these insightful comments. However, the discussion of the implications of the findings on influenza evolution for vaccine development, in our view, has nothing to do with "an ...appeal to the utility of basic research". On the contrary, in the specific case of influenza, vaccine development and the basic trends in virus evolution are inextricably (and traditionally) linked, and not considering the implications of our findings would be strange. This being said, the corresponding part of the discussion was modified to make it less evaluative.
1. I distrust the use of the term fitness in the abstract (end of the Results section) to explain dominance, as in this sentence, it provides no new information and sounds vaguely circular.
Author response: Hard to agree. We believe that the current wording, indeed, describes the situation properly: due to the drop of the relative fitness of the previously dominant H3N2 isolates, the H1N1 isolates become dominant.
2. The final sentence of the results section of the abstract could be stated more clearly. How about "The increase in dominance of H1N1 in some seasons is most likely facilitated by an increased resistance to the incumbent H3N2 lineage during a period of stasis."
Author response: Again, we find the original wording to be more precise, even if slightly more complicated. The issue is, indeed, about the increase in the fraction of resistant hosts, not just "resistance" in general terms. The preceding sentence, though, has been reworded for clarity.
3. The final sentence of the conclusion of the abstract is rather odd. How could parallel replacements serve as predictors of new dominant strains?
Author response: Why not? The isolates that undergo parallel changes are likely to be doing so due to positive selection and might become dominant. This is explained in the Discussion. We do recognize, however, that this is speculative and the language in the Abstract has been softened accordingly.
4. I do worry a little about the lack of statistical significance for some of the results, given that they are described as striking.
Author response: Point well taken, "striking" removed.
5. Figure is rather impenetrable and could use a better explanation
Author response: We added a new Figure (such that the original Figure became Figure ) that, hopefully, provides such a explanation, at least with regard to the procedure used to determine lineage extinction times.
6. I wonder whether it is not appropriate to simulate (through bootstrapping for example) a null expectation for the pattern of recurrent amino acid substitutions in the data. It is hard to intuit how unlikely these events are.
Author response: We felt that this was beyond the scope of the present work (it might become a subject of a future study). Indeed, the main point here is the non-random distribution of the parallel mutations across the lineages, and to establish this, simulation does not seem to be required.
7. I am not yet convinced that what is being described is competition among strains (last paragraph of the Results). Competition implies a finite supply allocated over a potentially more abundant demand population, thereby promoting competitive exclusion. Here it is not clear that the immune suppression of one strain is what allows another to invade, or rather a simple suppression of one and an indifference to another. This would be more like sorting than selection in Wimsatts' usage with shifting indifference allowing outbreaks. Perhaps a little more detail on mechanism would help to make this distinction clear?
Author response: There are some semantic issues involved here that we are not entirely confident about. Regardless, there does seem to be a competition (over a finite supply of susceptible individuals) between H1N1 and H3N2, the outcome of which depends on the fraction of the population that is naïve to each of the respective viruses at a given time and evolution of the viruses themselves that may allow them to escape immunity.
8. In the Discussion, an increase in fitness is associated with rapid exploration of the adaptive landscape. But this is not really correct. Selection increases the rate of hill climbing to a local peak, but suppresses variance over the landscape as a whole. As the authors argue earlier in the paper, it is neutral evolution in the functionally "static" period that promotes effective search, then new variants are fixed through a rapid bout of selection.
Author response: Yes, we must agree with this point. The phrase in question was modified to indicate that, under selection, only specific areas on the landscape are quickly explored.
9. I think that the papers of Stadler and Fontana (e.g. current biology evodevo with RNA) on the role of neutrality in promoting innovation more suitable than Gould and Wagner.
Author response: We now cite Huynen, Stadler and Fontana, in addition to Gould and Wagner, along with a relevant paper by one of us (Lipman and Wilbur 1991, ref
10. A final remark on ds/dn ratios which offers an independent sites model of selection. Given the finding that epistasis is likely to be very important, I worry about the power of the ratio to reveal systematics trends. For example, there could be consistently strong directional selection, but little evidence of it, as a result of the compensatory changes required by epistasis. I guess when dn >> ds this might be sufficient to conclude directional selection, but when ds > dn we can not really know. This is hardly a unique failing of the current paper, but a common problem faced by the community of researchers intent on quantifying selection.
Author response: The ambition of this paper is less general than "quantifying selection". What we seek to demonstrate and what does seem to become apparent is the existence of major differences in the strength of selection between different time intervals during influenza virus evolution.
Reviewer's report 3: Christopher Lee, University of California-Los Angeles
This is a very interesting paper that sheds new light on a scientifically and medically important question. It will certainly be of interest to a broad audience of readers of Biology Direct. The data and analysis methods appear sound, although I have some questions about the graphical presentation and interpretation of the results. I also suggest that additional text and a figure explaining some of the paper's definitions and methods would be useful.
1. It would be helpful to have more explanation of exactly what criteria were used for choosing the set of sequences for identifying mutations and measuring dn/ds ratios. The methods section indicates that only 100 H3N2 HA sequences (of the 994 available) were used to obtain dn/ds estimates. But the manuscript doesn't explain how the 100 sequences were chosen, why so few were used, and how robust the dn/ds results would be if other samples of HA sequences were used. If the results have some dependence on the sample chosen, it would be useful to give some measure of their robustness (e.g. bootstrap).
Author response: We amended the text in question to indicate that the selected subsets represented all distinct side branches (i.e., all except some that were adjacent in the tree and were merged). It should be noted that the pattern of mutations mapped to the trunk branches and, accordingly, the dn/ds estimates for the trunk is highly robust to the specific choice of isolates from the side branches inasmuch as all of these branches are represented. Of course, the dn/ds estimate for the side branches themselves depends on the choice of isolates more strongly but this is not crucial for our conclusions. As for bootstrap or a similar test, this is, unfortunately, computationally prohibitive.
2. Given that the authors are having trouble showing statistical significance for the dn/ds results, I'd assume the authors are using all the counts they can get; thus, some further explanation of limiting the analysis to "100 HA sequences" would be helpful. Similarly, do the mutations counted in Fig. (and shown in Fig. ) comprise ALL mutations in all 994 H3N2 HA sequences, or just a subset? Is this (sub)set of sequences different from that used for the dn/ds calculations, and if so why? Alternatively, if this (sub)set does not include all mutations observed in the 994 sequences, what is the rationale for this different choice of sequences? Reading the text I thought the dn/ds counts in Fig. should be measured solely on trunk branches ("...positive selection in the epitope regions of each new dominant lineage..."), but the text doesn't explicitly say so. If the dn/ds numbers in Fig. are not specific to the trunk branches, it would be helpful if the authors could address how these results really relate to the "dominant lineage" they refer to.
Author response: See above. The maximum likelihood calculations of dn/ds were performed for a subset of 100 sequences for all branches and also for trunk and non-trunk branches separately as explained in the 3rd paragraph of the Results section and shown in Table . As indicated in the response to (1), this gives a complete picture of the mutations in the trunk. The rest of the analysis dealt with all 994 sequences; in particular, the data in Figure (former Figure ) includes all trunk mutations as is made explicit in the revised legend.
3. Since the dn/ds differences report in paragraph 3 of the results ("To determine whether positive selection...") were not statistically significant, it might make sense to move this paragraph after the following paragraph (describing Fig. and epitope vs. non-epitope Fisher tests), whose dn/ds differences were statistically significant. The current paragraph 3 could then be positioned as an extension of the statistically significant result, suggesting that there is indeed dn/ds>1 positive selection.
Author response: We understand the potential advantages of this order of presentation but we feel that the current order is more logically cogent: the results of the standard test are given first; these are suggestive but not compelling, so additional, less common tests are described, and these do show that differences in dn/ds values are statistically significant.
4. Distinguishing "trunk" vs. "non-trunk" branches is fundamental to much of the paper's analysis, but is not explained prominently (the definition is hidden in the Methods). Since the authors' criterion is quite simple, I think it should be explained prominently in the paper, at the first point these terms are used. I also think the definition of "dominant lineage" needs to be made explicit; e.g. does this always mean the trunk branch? Similarly, it would be helpful to clarify the distinction between "trunk branches" (column title in Table ) vs. "inter-clade branches" (column title in Table ).
Author response: The definition of the trunk is included in the revised background section (4thparagraph). As for the "inter-clade" branches, this is used for H1N1 because there was no real trunk in that tree; this is made explicit in the revised footnote to Table .
5. The precise definition of how H3N2 isolates are divided into "lineages" is a bit hard to follow, and would be greatly clarified by an explanatory figure. The Methods section "Extinction of Lineages..." bristles with graphical language ("below", "above", "proximal", "distal" etc.), but all these complicated descriptions are not easy to picture. The authors seem to be going to considerable trouble to describe a picture to the reader; I think it would be much easier to just show the picture as a figure, with all the relevant terms defined and labeled on the figure. As far as I can tell, extinction times are computed for each trunk branch node, based on the isolation times of its non-trunk descendants, but a figure could make the definition both clear and precise. For example, does the "90% extinction" criterion mean sorting the non-trunk descendant isolates by date, and finding the 90th percentile rank value of the isolate dates? The "trunk" vs. "non-trunk" definition (see above) could also be included in this figure. Since Biology Direct has no limit on pages or figures, this seems like an easy solution. I'm hoping this would also clarify Fig. (see next point).
Author response: The procedure employed to estimate extinction times is now illustrated in the new Figure ; we believe that this does, indeed, facilitate understanding of Figure (former Figure ).
6. In Fig. , why are extinction times shown for some trunk branch nodes, but not others? E.g. between the upper "41" and the "4" right above it, there are many trunk branch nodes, but extinction times are not shown for them. What is the criterion that determines which trunk branch nodes have extinction times computed for them?
Author response: The extinction times are given for all segments of the trunk bounded by precisely dated isolates. Without such dating, extinction time could not be estimated. This is noted in the last section of the Methods.
7. In Fig. , it would be helpful to label the left column "Extinction time (mo.)" and the right column "Mutations (n/s)".
Author response: done as suggested.
8. In Fig. , the use of color is potentially confusing (i.e. red/green means very different things for the lines vs. letters). I suggest that all mutations simply be printed in black, with BOLD for epitope mutations, and ITALICS for non-epitope mutations.
Author response: modified as suggested.
9. Comparing the amino acid mutation counts in Fig. vs. the mutations shown in Fig. , the numbers don't match, so it would be useful for the authors to clarify precisely the criteria for what mutations are included in the counts for Fig. vs. Fig. . I had assumed that the Fig. counts would only reflect trunk branches (to measure positive selection on the "dominant", trunk branch); am I wrong?
Author response: These figures ( and in the revision) present different data. Only those mutations in the trunk for which there are parallel mutations in side branches are shown in Figure . Thus, there is no reason to expect the same numbers.
10. It might be possible to improve the presentation of the data in Fig. . Specifically, we're asked to correlate two important types of data in this figure (extinction times and dn/ds numbers); both are quantitative, but are only presented as text, and are disconnected from each other by two layers of "mapping". I suggest that this be reformatted to show two separate results: the raw data for the extinction time result, and the correlation of extinction times vs. dn/ds mutation events.
The first reason for suggesting this is that the extinction time result is in fact an important result in itself, and I think readers of the current manuscript will have trouble understanding exactly how the authors got this result. I suggest the following graphic. Use the y-axis to represent the origination date of trunk branch nodes (i.e. inferred origination date of each lineage, with a point shown for each lineage), essentially drawn just like the time-axis currently shown on the right hand side of Fig. . Use the x-axis to show extinction times: draw a horizontal bar showing the extinction time for each lineage; optionally, you could also draw tick marks showing the raw isolate dates (relative to the lineage origination date). Hopefully this would allow readers to evaluate for themselves the raw data for the existence of two distinct phases of "stasis" vs. "rapid turnover". It would also be helpful to calculate some kind of p-value for this hypothesis, and to show a histogram of lineage extinction times so people can see "two peaks" (or at least, not one peak).
There are several options for showing the correlation vs. mutation counts. The mutation counts could simply be juxtaposed as text (as in the current Fig. ). Additionally, dates of individual mutation events (epitope, non-epitope, and synonymous, each with a distinct symbol) could be marked on the right hand side based on their inferred date, so that readers can see the raw data. Doing this as a separate figure (i.e. not within Fig. ) would be OK, if that helps reader comprehension by letting the reader focus on one result at a time.
Author response: We tried several alternatives to Figure (former Figure ) but, in the end, decided to stick to the original format. Hopefully, the new Figure does clarify at least some of it (also see the response to the next point).
11. Is it possible to include in the Fig. the dominance period of each subtype? This would make it easy to see whether the H3N2 stasis is associated with H1N1 dominance or not.
Author response: As per this suggestion, the H1N1 dominance intervals are now shown.
12. For a general audience, it would be helpful to add some explanation of what "Immune cross-protection" means, e.g. "low frequency of co-infection by both H1N1 and H3N2"
Author response: In this context, immune cross-protection simply means that individuals that develop immune response to H1N1 are less likely to get sick when infected with H3N2 and vice versa. Co-infection is not involved.
I hope some of these questions are helpful.