W. Ford Doolittle (Dalhousie University, Halifax, Canada)
Although there is much about this paper with which I wholeheartedly agree, and which I think admirably summarizes the state of play, the authors do seem a bit confused about what Eric Bapteste and I called Darwin's Tree of Life Hypothesis. In their understanding, we saw "the TOL as a hypothesis composed of three connected propositions: natural selection (and potentially other processes) drives modification, descent occurs with modification, and hierarchical patterns are produced by that process." What we wrote, though was:
"1. The pattern of groups subordinate to groups embraced by a unique inclusively hierarchical classification based on homologies (true affinities in Darwin's language) is indeed not arbitrary. It reflects an underlying natural reality with a natural cause, rather than ''some unknown plan of creation, or the enunciation of general propositions'' in Aristotelian logic, embedded in the practices of systematists.
2. That natural cause is historical, and in particular, it is direct descent with modification, a branching process whose branches will be recaptured in the most truly natural and correct classification, which might in principle be extended to include the last common ancestor (or ancestors) of all extant forms.
3. Modification is driven by natural selection." 
I now see this formulation as unduly wordy and prone to the sort of emphasis-altering paraphrasing O'Malley and Koonin offer. Bapteste and I could/should have offered a short form of our own, something like this: natural classifications are tree-like because the process that produces the characters on which they are based is tree-like (and selection is the driving force). The emphasis would be on "because", because Darwin's was, I believe, as in these lines from earlier in the same paragraph that O'Malley and Koonin quote:
"The limbs, divided into great branches, and these into lesser and lesser branches, were themselves once, when the tree was young, budding twigs, and this connection of the former and present buds by ramifying branches may well represent the classification of all extinct and living species in groups subordinate to groups."
Jerry Coyne, in his recent Why Evolution is True , similarly sees Darwin endorsing the Tree as an explanation, or more precisely as a prediction of his theory.
"Actually, the nested arrangement of life was recognized long before Darwin. Starting with the Swedish botanist Carl Linnaeus in , biologists began classifying animals and plants, discovering that they consistently fell into what was called a ''natural'' classification. Strikingly, different biologists came up with nearly identical groupings. This means that these groupings are not subjective artifacts of a human need to classify but tell us something real and fundamental about nature. But nobody knew what that something was until Darwin came along and showed the nested arrangement of life is precisely what evolution predicts. Creatures with recent common ancestors share many traits, while those whose common ancestors lay in the distant past are more dissimilar. The natural classification is itself strong evidence of evolution."
But surely the flaw or "circularity", the conflation of explanandum and explanans here should be obvious. We have a fact (Tree-like classification) and we come up with a theory (Tree-like evolution) to explain the fact. Then what do we predict in order to test our theory? Tree-like classification! Panchen's book, Classification, Evolution and the Nature of Biology , which caused me first to twig to the circularity issue, does outline some of the ways out of this. And of course Evolution is True , for those reasons and because of the overwhelming consilience of many lines of evidence.
Authors' response: Our question here would be whether Darwin and subsequent evolutionary biologists are using the logical structure of "X because Y" (explanatory, in that Y explains X). We are not convinced this is the logical structure Darwin was intending and believe it may better be described as abductive reasoning, which was outlined by Charles Peirce in 1903 in the form:
"The surprising fact, C, is observed;
But if A were true, C would be a matter of course,
Hence [because of C], there is reason to suspect that A is true" .
If we substitute C with hierarchical order and A with TOL, then the abductive structure of TOL reasoning is:
"The surprising fact, of hierarchical order, is observed;
But if the TOL were true, hierarchical order would be a matter of course,
Hence [because of hierarchical order], there is reason to suspect that the TOL is true".
This structure does not involve the "because" reasoning of causal explanation. Rather, it is ampliative in that it adds to what is known and is potentially able to improve understanding of the phenomena of interest. Abductive reasoning has been much discussed in philosophy of science, and has its critics as well as its advocates. More recently, abductive reasoning has been discussed in the form of "inference to the best explanation" as philosopher Peter Lipton points out:
"Inference to the Best Explanation can be seen as an extension of the idea of 'self-evidencing' explanations, where the phenomenon that is explained in turn provides an essential part of the reason for believing the explanation is correct. ... hypotheses are supported by the very observations they are supposed to explain. Moreover, on this model, the observations support the hypothesis precisely because it would explain them."
In other words, explanation comes prior to inference, and involves an evaluation of how well different hypotheses would explain existing evidence. The problem then becomes one of how to evaluate the "best" explanation, and the logical objection of circularity drops out of the picture (i.e., it's not a matter of one "proving" the other). However, we agree that in the following section, Doolittle is objecting to the outcome of the inference by arguing that the TOL is not the best explanation and certainly not the only explanation available to account for the "surprising fact" of hierarchical order.
Doolittle responds in a second review: I have only a folk-philosophical understanding to help me deal with this, but I swear that this abductive reasoning formulation has a "because" hidden underneath it. Why else would "hierarchical order" be a "matter of course" if the "TOL were true"? If by 'TOL' the authors mean to refer to the TOL hypothesis (as articulated above in bold), then the reason hierarchical order follows as a matter of course is because and only because a tree-like process is expected to produce the tree like-pattern of similarities and differences between organisms that is enshrined in a hierarchical classification.
Seems pretty because-ish to me: there is a causal connection between evolutionary branching and the disposition of traits on which hierarchical classification is based. We would not say, for instance, that "if E = mc2 were true, hierarchical order would be a matter of course" because even though E does equal mc2 we can think of no similar causal connection to hierarchy.
Possibly though, O'Malley and Koonin are not referring to the TOL hypothesis when they say "if the TOL were true, hierarchical order would be a matter of course" but to the TOL itself, that tree-like pattern of relationships between taxa that molecular phylogeneticists hope to reconstruct (some believing that they already have). Now that's circular: it's like saying "If there were a natural (aka true) tree-like or hierarchical pattern of relationships, hierarchical order would be a matter of course".
But the authors' thoughts do persuade me that there must be degrees of circularity. The goodness of fit between hierarchical classification and the TOL hypothesis does seem like some sort of support, or consistency with, or even evidence for it (in the sense that hierarchical classification is none of these for E = mc2). But surely it is not "proof". Surely it a standard part of scientific practice to expect that a hypothesis should make predictions about data not yet obtained, and of a different sort than the data which suggested the theory. Francisco Ayala, one of Darwinism's most stalwart supporters, accepts this too, writing that,
"If a hypothesis is formulated to account for some known phenomena, these phenomena may provide credibility to the hypothesis, but by themselves do not amount to a genuine empirical test of it for the purpose of validating it" .
I am also persuaded that "Inference to Best Explanation" is a valid way to do science, but also encouraged by what I take is the authors' admission that the existence of other defensible explanations for the same "surprising fact" strengthens our (mine and Eric Bapteste's) claim that whatever Darwin meant by the Tree "simile", it could/should now be taken as an hypothesis. But surely they would not have us believe that when only one explanation is apparent to the scientific community, it must be taken as fact.
Which gets us back to the "surprising fact of hierarchical order." Why "surprising"? Who was surprised (in 1859)? What is the null hypothesis here? Why should we expect disorder rather than order? Darwin's goal was to come up with a naturalistic explanation for an orderly pattern of relationships in nature to replace the supernaturalistic one then (and sadly still) hegemonic. ("Let the earth bring forth grass, plants yielding seed of each kind, and trees bearing fruit of each kind ..."). That there is such an orderly pattern doesn't discriminate between these views, for all we scientists embrace the former.
Doolittle's first response continued: But natural classification is not proof of evolution or of the existence of an underlying tree-like process. Not only is the logic shaky, there is an alternative. It is in principle possible, as Peter Gogarten and colleagues will argue elsewhere in this issue , that biased LGT can produce tree-like patterns from a process that is not itself tree-like. Maybe taxon A and taxon B appear to be sisters to the exclusion of C because they share genes more frequently, not an ancestor more recent. This too would be "descent with modification". So it is instead specifically (1) that descent with modification is a predominantly tree-like process and (2) that this tree-like process produces a tree-like pattern, that together make up Darwin's hypothesis. "Descent with modification" is often taken to mean tree-like evolution, but it needn't, and we probably should not even have used the term in the long-form of the Tree of Life Hypothesis. The word "genealogical" is equally squirrely. When we use it in a human context, unique family trees (usually only patrimonial ones) come instantly to mind, but in fact we are each at the end of 2N genealogies, going back N generations.
I think that when cladists say that trees branches are hypotheses they mean that they are hypotheses about relationships between specific taxa, not a general explanation for why there should be trees at all. So Darwin's Tree of Life Hypothesis, as Bapteste and I understand it, is not gently morphable into some looser Statistical Tree of Life (STOL) Hypothesis, as O'Malley and Koonin seem to suggest. An STOL could also arise from rampant gene transfer -- with no deep vertical signal -- provided there is some bias affecting LGT. And who could sensibly imagine that there would not be many biases? But such an STOL would be precisely not what Darwin's Tree of Life Hypothesis was about. So O'Malley and Koonin are partly right when they claim that Bapteste and I would "claim that accommodation and expansion are not legitimate ways in which to treat hypotheses." They would be fully right had they added "especially when the expanded hypothesis has transmogrified into something antithetical to its original form."
Authors' response: We tend to agree regarding the drastic and irreversible transformation of Darwin's TOL hypothesis and had already noted in the text the specific nature of cladist hypotheses. Darwin simply was not equipped to think of anything other than an organismal/species tree. He could not think of trees for individual genes because he was unaware of the existence of the latter. We note that Doolittle agrees with us regarding what we said about accommodation being rejected by Doolittle and Bapteste, but think the even stronger clause tacked on in this response would be hard to defend. It is not clear that the extended TOL hypothesis should be considered "antithetical" to Darwin's ideas even though it is indeed dramatically different. From today's perspective, Darwin's hypothesis is not properly defined as such a definition was outside the purview of the science of Darwin's day. With this realization, the purported circularity of the argument becomes less evident and less damning (even if abductive reasoning is not taken into account) -- we think it actually goes away. The fundamental tree-like character of evolution is not derived from an observed tree-like pattern of classification. On the contrary, this is an intrinsic feature of the evolutionary process that follows a fundamental observation of biology, namely the bifurcating character of gene replication and cell division. Under this view, the STOL can be conceived as a straightforwardly testable hypothesis. If anyone manages to show that there is no statistically significant trend of topologically congruent trees, the STOL will be found wanting in terms of predictive power and effectively refuted. So far it seems to have withstood the test. We agree that the biased HGT hypothesis of Gogarten, Doolittle and Lawrence is a viable alternative although there seems to be considerable uncertainty as to whether biased HGT could be the sole explanation for the observed tree-like patterns for gene ensembles, or just a complementary explanation to a genuine trend of vertical evolution [32, 119]. Testing this hypothesis poses conceptual and technical challenges but some approaches have been attempted, and the results seemed to contradict the most radical version of the biased HGT hypothesis . However, most of the work in this direction remains to be done. This is the main point we would like to make in this discussion: the STOL might turn out to be false but it is a bona fide hypothesis.
Doolittle responds in a second review: Well, OK, maybe "antithetical" is too strong, and of course it's a mug's game guessing what Darwin would think were he still here. And I will agree that the STOL hypothesis as stated above (that there are more congruent trees than expected by chance), though possibly unprovable at depth, is not only coherent but unavoidably true. But if -- as is possible -- the majority of the genes that make up any prokaryote's genome, determine its phenome and define its "relationships" to other prokaryotes actually arrived in that genome by lateral transfer rather than vertical descent, then I'd put money on the venerable bicentenarian saying "Oh, that's not what I had in mind at all!"
Doolittle's first response continued: It's not easy to argue against the value of the TOL as an heuristic or tool, but I'll try. If what undergirds such a TOL (which would be in actuality an STOL) are central tendencies, then we must always be careful to hedge statements we make about it. If we say something like "halophilic archaea arose from within the methanogens with the importation of bacterial genes for respiration" we need to be very careful to note that methanogens that far back in time need not have had any specific genes or capacities other than a taxon-defining 16S rRNA. To draw what I think is an apt analogy, we need to be similarly careful when we say something like "early English arose from several ancient Germanic languages" not to pretend that we would recognize it or any of those others if someone started speaking them to us on the street. The literature of language evolution is amazingly parallel to our own on these questions, but ahead of us in sophistication and realism, I think. For instance, Heggarty et al. in a 2011 paper on Germanic languages  say this about the evolution of English:
"If our real goal is to uncover the histories of the populations that spoke given languages, rather than abstract schemas intellectually satisfying for their binary purity, then it is served by using language data to arrive at a picture of the nature and degree of cohesion (or otherwise) of speech communities within a language family, through the story of its divergence. To this end, we must represent the historical and linguistic truth that English ultimately underwent a longer and more total isolation than did most continental varieties from each other. The approach that best uncovers this signal is to measure and represent the full impact of all those far-reaching changes that came to mark it out as so distinct from all other Germanic varieties in so many ways ... Furthermore, while English is widely assumed to have derived from a mixture of Germanic dialects--eminently logical also in terms of population history--this too cannot be represented in a tree model. That structure is inherently forced to oversimplify the most plausible history. Nor could it capture the clear possibility that of the dialectal mix that went to make up English, a greater part was of more western than northern Germanic character and provenience, but not exclusively so, especially at a time when the difference between those two groups may well have been very much a continuum still. It is such matters of degree, rather than mutually exclusive binary alternatives, that speak in favour of distance and network analyses for language history, and against tree-only ones."
We microbiologists must accept that this sort of messy historicity will also be appropriate for any true description of microbial evolution, however tightly we hug our statistical trees.
Authors' response: We too accept the inescapable messy historicity of any adequate description of evolution, especially (but by no means exclusively) when it concerns microbes. We are perhaps slightly at odds about whether statistical analyses can capture in a helpful way the fuzziness of evolutionary processes. Our reasoning is this: given such messiness, if we want to discover any patterns in this history, an organizing framework is badly needed, and the (S)TOL is one of the best frameworks for such a purpose. The STOL can be used as a framework for the construction of evolutionary scenarios, which is what much of evolutionary biology is about. The ultimate value of this framework is contingent on the robustness of the STOL hypothesis (see above). If the hypothesis stands up to rigorous examination and testing, the STOL can be reasonably considered a uniquely powerful heuristic. Should the hypothesis fail to stand up against such scrutiny, a tree for a universal gene like 16S RNA still can be used as a standard of comparison, without bestowing on it any special ontological status. Certainly, our advocacy of the STOL as a framework for evolutionary studies should not be taken as an attempt to invalidate promising complementary frameworks such as various kinds of evolutionary networks [121, 122].
Doolittle responds in a second review: It would be silly to claim that trees are not useful in the construction of evolutionary scenarios. But to the extent that any STOL is not the history of the lineages of organisms or genomes such studies address, but rather a summation of biases in LGT, we can be misled.
Nicolas Galtier (CNRS, Montpellier, France)
I much enjoyed reading this piece, which I think is a sound, balanced, well-written overview + opinion about an important topic -- Tree of Life (TOL) significance. The manuscript correctly makes clear that
(i) genomic evolution is far from 100% tree-like,
(ii) drawing a tree does not mean assuming that genomic evolution is 100% tree-like,
and reviews the way these two basic-looking statements have been acknowledged, and their relative importance weighted, by the scientific community. I feel I agree with most of the arguments made in the paper, some of which I tried to express in a previous Biology Direct review . I share the prediction that TOL will remain useful to evolutionary sciences in the forthcoming years, or decades. Here are a couple of thoughts that arose while reading this article, which I take the liberty to express although not all of them are tightly connected to the specific content of the manuscript.
The text says: "understanding of evolutionary history arguably should be the goal of all research in evolutionary biology". I would modulate. I think a large part of research in evolutionary biology is about the process, not the pattern. Besides history, we also would like to understand the evolutionary forces having shaped current biodiversity, including mutation, selection, drift, recombination, duplication, HGT, speciation, extinction, vertical inheritance. I note that the last five of these processes (i) implicitly acknowledge the relevance of the tree of cells, (ii) would be optimally studied if the tree of cells was known, and (iii) have been typically approached by taking the "average"/"central" tree as an estimate of the tree of cells - sometimes in a disguised way, by calling it "taxonomy".
Authors response: We fully agree and have modified the text in question to state:
"Treating all these non-tree-like processes as problems that obscure the "true" TOL greatly skews and limits the understanding of evolutionary history that is one of the central goals of evolutionary biology -- along with understanding processes and patterns of evolution ."
I would like to suggest that "falsifying" the TOL in the face of HGT would be equivalent to, e.g., falsifying the Linnean taxonomy in the face of gene flow, genetic incompatibilities, and hybridization. We know that the living world is not made of reproductively isolated groups of fully interbreeding individuals. Yet the species concept captures a lot of the information about genetical exchanges between living things (at least in animals and plants). We can debate the concept, refine it, call it insufficient, but we just cannot dismiss it.
Authors' response: Agreed. The use of the term "falsification", with its connotations of an exact hypothesis that can be decisively falsified by a single or even a few negative findings is problematic. We had noted that in the text, but had used the word casually in a few places ourselves. We have replaced these uses of falsification with broader terminology except where we cite others who use this exact term. And we think our discussion of heuristics harmonizes with the reviewer's thoughts on usefulness and information capture.
I wonder why the discovery of HGT in prokaryotes led to such extreme proposals as "Darwin was wrong" and "the TOL is dead", whereas the discovery of gene and genome duplication, gene loss, transposition, and incomplete lineage sorting, and other efficient anti-TOL processes, did not. If you think about it, the widely accepted vertebrate tree is a "tree of a few percent". The proportion of nucleotides in the human genome for which the personal history during the last 500 million years matches the canonical vertebrate tree is minute. Nobody complains when, in vertebrates, people discard paralogues (which they circularly identify thanks to prior speculations about the species tree), repeated elements and genes of viral origin, then build trees. In this taxon, it is undisputed that the species tree is a meaningful representation of evolution, however incomplete it may be, and however prevalent and interesting the anti-TOL processes may be (and they really are).
So why this difference? I think one reason is that in vertebrates we have a mental representation of evolving units (species) independently of their genomes. The species tree makes sense when you are interested in species. We would much like to learn about our vertebrate ancestors, irrespective of the fraction of genes we have vertically inherited from them. Vertebrate species are so neatly defined that we are happy to ignore the genealogical mosaicism of their genome, at best considered as a curiosity. Bacterial species, in contrast, are merely seen as identical bags of non-identical genes. Consequently, what matters in the first place (to us) in bacteria is the forest of gene trees, not the tree of bags. This might indeed reflect a genuine biological difference between the two groups (e.g., a more complex genotype-phenotype link in vertebrate than in bacteria), such that the TOL would actually have less scientific value in bacteria than in vertebrates. Alternatively, the difference of treatment might reflect our much deeper knowledge of (or interest in, or ability to perceive) the vertebrate than the bacterial biology and diversity.
Authors' response: We find this to be a deep comment a full discussion of which would require another manuscript perhaps the same size as this review article. We can offer only a few brief thoughts here. It is true that the gulf between the current perceptions of the status and importance of trees for vertebrates (and even animals in general), on one hand, and for bacteria and archaea, on the other hand, is huge. We can think of at least four reasons (certainly, not mutually exclusive) why this is the case. 1. To be fair, the vertebrate tree only becomes a "tree of a few percent" if the entire genome is considered. Looking at protein-coding genes only (indeed, less than 1.5% of mammalian DNA), the pan-vertebrate gene set is respectable (thousands of genes), and if in-paralogues are carefully taken into account, something like a "tree of half the genes" is possible, with topologies for individual genes being highly congruent. All the importance of the non-tree-like evolutionary processes notwithstanding, this is a far cry from the "tree of one percent" that is feasible for prokaryotes. 2. The vertebrate tree is, in a sense, "tangible", with internal nodes often associated with specific forms about which much is known from the fossil record. There is no fossil support for the tree of prokaryotes, and no chance ever to obtain such support, which certainly makes this tree less "real" than the tree of vertebrates. 3. For vertebrates, the concept of species is clearly defined and biologically meaningful despite some limitations. For prokaryotes, the species concept is fuzzy at best and meaningless at worst, its applicability appears to vary for different groups of bacteria and archaea, and there is no chance of a universal, biologically sound definition of species . Thus, if one chooses to speak of a "species tree", it is clear what is meant in the case of vertebrates but not in the case of prokaryotes. 4. The difference in the perception of trees is psychological and indeed reflects common and serious under-appreciation of the non-tree like aspects of evolution that are present and important in all life forms.
This leads me to my very last comment. The text says:
"This pluralistic perspective also suggests an additional issue of whether to separate representations and theories of eukaryote and prokaryote evolution, due to the different tempos, modes and outcomes of evolution involved. More than one account of evolutionary processes and mechanisms may be necessary to encompass the varieties of evolving life on the Earth."
I fully agree with the second sentence especially. HGT is one out of several anti-TOL evolutionary processes, and eukaryotes, by the way, are champions of HGT (partly, but not uniquely, through endosymbiosis) and of genome mosaicism. I am confident we would not question the relevance of the vertebrate tree even if we discovered substantial HGT in this group. I suggest that the distinct values we assign to the species tree in distinct taxa is determined by our representation of what species are, not by the way species evolve. If the genome of an insect and a Wolbachia strain once became physically merged and fully co-transmitted, we would comfortably call the resulting organism an insect. If such a fusion occurred between a bacterium and an archaeon, we would probably call the resulting organism a new domain of life. Non-tree-like evolution is everywhere. Scientists decide how meaningful it is.
Authors' response: Another truly interesting point. It is difficult to argue with the example given by the reviewer. Certainly, in these two cases, the interpretations of genome fusion would be quite different. Are the decision criteria "purely" subjective? Perhaps, they do not have to be. One criterion that immediately comes to mind is quantitative: if one of the merging genomes (the one designated as donor) makes a contribution that is orders of magnitude less than the contribution of the other partner (recipient), we will confidently identify the recipient as the main organism in the resulting chimera. In contrast, if the contributions of the partners are comparable, we will speak of a new domain or some such. This approach certainly works in the cases of Wolbachia-insect and bacterium-archaeon. However, it is easy to come up with counterexamples: about half of mammalian genomes consist of remnants of retrotranscribing elements but we have no problem at all classifying these organisms as vertebrates. Similarly, certain mesophilic archaea such as Methanosarcina acquired more than 20% of their genes from bacteria but all microbiologists agree that they remain archaea. Thus, the quantitative criterion is not entirely satisfactory, and a qualitative one may prove more appropriate. When genome fusion leaves the cell organization of the host (more or less) intact, we are comfortable to interpret the situation as "horizontal gene transfer as usual" -- these are the cases of Wolbachia and insect, Methanosarcina, and retroelements in vertebrates. By contrast, when genome fusion is accompanied by (or perhaps causes) a drastic change in cell biology, we are inclined to speak of the emergence of new domains or at least of major new groups of organisms. These are the cases of endosymbiosis in eukaryotes that lead to the emergence of new organelles, such as mitochondria and plastids. This qualitative criterion seems to make biological sense and applies also to the interpretation of trees. When a tree for a set of "core" genes reflects the continuity of cellular (organismal) biology, that tree remains relevant, even as one has to realize that it describes the evolution of a small fraction of the genetic material in the respective organisms. In contrast, when the biological continuity breaks down, so does the tree. In some senses, this distinction implies that ontological priority is given to cellular organization over genetic structure, and that morphological considerations trump molecular ones. There are potentially good epistemological reasons for accepting such hierarchies, but as pointed out by Galtier, it is of deep interest to reflect on how historical and psychological factors may have a role to play in preferences for certain explanations.
Christophe Malaterre (Institut d'Histoire et de Philosophie des Sciences et Techniques, CNRS, France)
In this paper, O'Malley and Koonin very convincingly argue that the notion of "Tree of Life" (TOL) covers two distinct concepts: (A) a hypothesis about the representation of the evolution and relatedness of organisms on Earth, (B) a heuristic tool that is useful to classify these organisms and that leads to new knowledge in evolutionary biology. In the first section of the paper, the authors review and clarify two main ways of understanding what the TOL is: the TOL notion may cover trees built from molecular phylogenetic studies of single genes, in particular the 16S and 18S rRNA genes; it may cover also trees built from the congruent phylogenetic signals of several genes, be they part of a "core genome" or chosen for the "central trend" that they exhibit. The authors then briefly compare these TOL tree-meanings to the "web of genomes" (or network) approach. In the second major section, they develop their main thesis on the two different concepts covered by the notion of TOL. First, the TOL can be understood as a scientific hypothesis. In this case, under a strict interpretation, this hypothesis has been refuted; yet under a modified interpretation that accommodates new findings into a "statistical TOL", this hypothesis still awaits refutation and is even useful. Second, the authors argue that the TOL can be understood as a heuristic tool, that is to say a concept that is not to be evaluated as true/false with respect to its correspondence to nature, but that is useful to the practice of science in at least two ways: as a conventional framework for classifying organisms or species, and as a means to "open up valuable lines of inquiry". In this case too, the TOL notion proves useful. In a short third section, the authors develop the idea that "the universal tree is not and has never been purely about right and wrong facts, but about the pragmatic knowledge-producing capacity of the TOL framework".
I find the conceptual clarifications of the TOL proposed by the authors extremely useful and enlightening. It is indeed crucial to realize that the TOL can cover at least two radically distinct concepts -- scientific hypothesis and heuristic tool -- and that it may therefore be evaluated in at least two different ways: with respect to its refutability or with respect to its usefulness. As such the paper is an extremely valuable conceptual contribution to the more general TOL debate.
Let me mention however two points that raise questions. The first one has to do with the notion of "hypothesis". Some may indeed argue that the TOL is not just any type of "hypothesis", but a hypothesis that tells us something about the real evolutionary relatedness among groups of organisms. In other words, it might be argued that the TOL is above all a scientific theory. Of course, following Poincaré , one may say that all generalizations and theories are hypotheses; yet they are particular types of hypotheses: hypotheses that are refutable while also well corroborated by observations , that include bridge principles that mediate their correspondence to observation data , that take the form of research programs constituted by a central core of propositions surrounded by a belt of protective assumptions , or even hypotheses that are constituted by classes of models isomorphic to certain domains of nature . It seems to me that taking a "theory" perspective on the TOL -- a perspective that is often implicit in the paper since it is indeed made reference to Popper and Lakatos among others -- could help the argument proposed by the authors in at least two respects. First, some philosophical models of scientific theories make it possible to account for theory modification or replacement over time; such a view could thereby help explain why the TOL is still around despite claims of its "refutation". Second, philosophical models of scientific theories also make it possible to discuss how theories relate to the real world (for instance via bridge principles); and a discussion of how the TOL as a hypothesis/theory does indeed relate to nature could indeed extend the argument of the paper, even if the authors purposefully restrain their arguments to non-ontological matters.
Authors' response: These are very useful thoughts on what it is that is being disputed in regard to the TOL. We have discussed above with our first reviewer (WFD) whether the TOL took the logical form in Darwin's thinking that Doolittle and Bapteste suggest it did. In this article, we mentioned the multi-propositional nature of Darwin's ideas about the TOL. These connected propositions, both core and contextual, might be most accurately described as a theory, as Malaterre suggests, and we could then engage in extended philosophical discussions of the correspondence of the TOL theory to aspects of the world. The TOL debates are both about the realness of the TOL and about its epistemological value, and in this article we argue that the two facets of the debate can be cleanly and profitably separated. Theories are something philosophy of science has focused on for decades. This attention has been illuminating but it has also obscured many other aspects of scientific practice. One of these has been how theories or core elements of theories are operationalized in workaday hypotheses such as claims about the TOL. This sort of activity is at least part of what we address in this article. Indeed, it would be useful to analyse the TOL as a theory, and to see how different philosophical accounts of theory interpret TOL claims and contestations, but pragmatic concerns guide our choices here. The extended discussion that Malaterre advocates, in which the TOL is examined as a theory, would no doubt be illuminating for TOL researchers.
A second point concerns the fact that, as shown by the careful and well-crafted section on "reinterpreting the TOL", the notion of TOL may be explicated in many different ways. As a result, some may argue that their ways of defining a TOL differ from those that are offered in the paper and that, as the result, they may not map onto the two roles identified by the authors (hypothesis or heuristic tool). It seems to me that a specific risk stems from a possible conflation of the epistemology of the TOL and its ontology. This point is clearly identified by the authors, yet only in the second section of the paper, and I wish this distinction were made earlier. Indeed, when presenting the different construals of the TOL in the first main section, the authors mention "trees of genes as trees of species" and "trees of genomes as trees of cells". Yet these expressions tend to conflate different possible meanings associated with the TOL: Is the TOL a tree of genes or a tree of species? What does the "as" imply? Is it rather a tree of genomes or a tree of cells? If it is a tree of cells, how does it differ from a tree of species?
Authors' response: This comment points to a dimension of discussion we largely sidestepped and yet which is of enormous importance to TOL debates. We now mention earlier in the manuscript how we think ontological issues have been conflated with epistemological ones, and we also announce there that we try to separate the two as best we can. The questions Malaterre asks in this part of the review lie at the heart of ontological clarification of the TOL, and as far as we are concerned, they are unresolved. What we are doing with the "as", therefore, is signalling that we are agnostic on the exact nature of the relationships between the two interpretations of the TOL. We think it unlikely that there is an identity relationship (in which "as" would mean "the same as"). We note that methods are being used that presume some sort of equivalence, and we then focus on those methodological choices. Laura Franklin-Hall has done some philosophical work on the implications of such relationships, but there is still more that could be done, as Malaterre points out. This is especially because in practice, TOL ontology and epistemology are not isolated from one another. And yes, it is likely that our two foci, hypothesis and heuristic, do not exhaust what can be done with the TOL. Indeed, Malaterre rightly emphasizes the fruitfulness of thinking about the TOL as theory, and the same could no doubt be said for the TOL as a model.
Maybe distinctions could be made between different types of TOL depending on the types of entities that they refer to. One might, for instance, distinguish three types of entities: (i) real source entities such as genes, core genomes, gene sets that are extracted from particular present-day organisms and whose data are used to generate a tree-like or network-like representational model; (ii) represented entities that would include the source entities (as end-points in the model) but also such entities as ancestral genes or gene sets (as additional nodes in the model); and (iii) interpreted entities such as organisms, species, past or present, once an interpretation of the model is given. Accordingly, the TOL might be understood as a represented entities TOL (a tree-like model that is built from the source entities using various computational tools, some of which might in addition include hierarchical branching assumptions), or as an interpreted entities TOL (an interpretation of the previous tree-like model in terms of organisms or species for instance). Furthermore, one may consider the existence of the real genealogy of the real organisms on Earth, and therefore postulate the existence of real entities phylogenies at different levels (genes, genomes, cells, organisms, species). It then seems that some of the controversies mentioned in the paper -- in particular when it comes to the falsifiability of the "TOL as hypothesis" -- could be understood as disagreements about how to answer three different questions: (1) Given a set of real source entities, is the inferred represented entities TOL true -- in the sense that if the corresponding real entities phylogeny were known, the two would match -- or is it false due, for instance, to lack of data or to wrong inferences made by our computational tools? (2) Given a represented entities TOL (for instance a gene tree), is the interpreted entities TOL (for instance a species tree) true -- in the sense that if the corresponding real entities phylogeny were known, the two would match -- or is it false due to a wrong interpretation? And (3), are the real entities phylogenies tree-like or not? And, while the third question is a question that concerns the structure or topology of phylogenies, the two first questions concern the more general problem of inference justification. These three types of questions might also help clarify the different epistemological levels at which the TOL might play a role as a hypothesis/theory, and more specific circumstances in which it might endorse a more heuristic role.
Authors' response: This is an interesting and potentially useful tripartite scheme for further analysis of debates about the TOL, and we believe such a framework of inquiry has never been suggested before. While it is not practical to rewrite the present article with this structure in mind, we would heartily endorse any attempt (from philosophical or life-science standpoints) to analyse TOL claims and research in light of this intriguing framework.
In any case, the conceptual distinctions that O'Malley and Koonin propose are most relevant to the debate: distinguishing between the TOL as a hypothesis (or a theory) and the TOL as a heuristic will help make discussions on the topic more precise and will improve the conceptual framing of some well-entrenched controversies.
Authors' response: We are most grateful to all three reviewers for the exceedingly thoughtful analyses they made of our paper, and the new routes of inquiry they have shared with us.