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Is It What We Know or Who We Know? Choice of Organism and Robustness of Inference in Ecology and Evolutionary Biology

2006; University of Chicago Press; Volume: 167; Issue: 3 Linguagem: Inglês

10.1086/501507

1537-5323

Joseph Travis,

Genetic diversity and population structure

Previous articleNext article FreeIs It What We Know or Who We Know? Choice of Organism and Robustness of Inference in Ecology and Evolutionary Biology (American Society of Naturalists Presidential Address)*Joseph TravisJoseph TravisDepartment of Biological Science, Florida State University, Tallahassee, Florida 32306‐4340†E‐mail: [email protected]. Search for more articles by this author Department of Biological Science, Florida State University, Tallahassee, Florida 32306‐4340PDFPDF PLUSFull Text Add to favoritesDownload CitationTrack CitationsPermissionsReprints Share onFacebookTwitterLinked InRedditEmailQR Code SectionsMoreEcology and evolutionary biology are amazing enterprises. Thousands of practitioners in hundreds of institutions around the world make idiosyncratic decisions about which questions to study, which organisms to use, and for how long, guided by a combination of individual predilection, inspiration from journals and books, and exchanges of progress reports and discussion at professional meetings. No synod of presbyters sets priorities, and no court of sagacious elders adjudicates disputes over which theory is the better explanation for a collection of data. From this swirling mix, principles form and a body of knowledge emerges. These are then collected into monographs and textbooks whose consistency might seem little short of miraculous, given the process. As in many academic disciplines, the epistemic basis of ecology and evolutionary biology, the set of principles and facts that we believe to be true, is the cumulative result of a remarkable self‐organizing process.Ecology and evolutionary biology are not focused on the uniform behavior of fundamental particles but on fundamental processes that unfold in a variety of contexts from a variety of histories. In that light, the most critical decision in the inquiry portion of our science is the match of question to organism (or system). That is, within this self‐organizing enterprise, how do we choose which organisms to employ to answer a question or, conversely, which questions to ask of a specific organism? If our epistemic basis is the cumulative result of these choices, then the principles and facts that emerge will be only as reliable as our choices have been wise.Here I explore how the decision to match organism to question influences what we believe to be so. In the first section, I take the pragmatic perspective of a working scientist and describe how we make the match. In the next section, I take a more formal perspective, following in part the work of Burian (1993), and describe how we should make the match; that is, I outline the criteria that ought to guide our decisions. In the final section, I explore how closely what we actually do approaches what we should do and discuss whether certain facets of our discipline warrant closer attention to the process by which we match organism to question and, thereby, derive what we believe to be so.How Do We Match Question and Organism?For many scientists, the organism leads to the question. This path is most likely when we observe some of nature's most striking phenomena, such as the synchronous mass flowering of south Asian bamboo (Keeley and Bond 1999) or the curious jugular location of the anus in pirate perch, Aphredoderus sayanus (Fletcher et al. 2004). We ask why something out of the ordinary has emerged; when we encounter mass flowering in bamboo, our first thought is not "I wonder what the specific leaf area of these plants might be," nor do we observe pirate perch and wonder immediately whether the population's superoxide dismutase gene shows extensive variation.Many of us work from organism to question in more routine contexts. That is, we make an observation that interests us and then direct our questions to it. Followed faithfully, this approach usually leads to research that crosses lines between subdisciplines and often leads to some striking discoveries about the organism. For example, the work that my colleagues, students, and I performed on sailfin mollies Poecilia latipinna began when Jim Farr and I noticed that molly populations varied widely in their body size distributions and that closely adjacent populations sometimes had extremely different distributions (fig. 1). We were not the first to notice this pattern, of course (see Kilby 1955; Hubbs 1964; Snelson 1985), but we were the most tenacious in our desire to explain it. Our subsequent studies embraced behavior (Farr et al. 1986; Farr and Travis 1986; Travis and Woodward 1989; Ptacek and Travis 1996), life history (Farr and Travis 1989; Travis et al. 1989; Trexler and Travis 1990; Trexler et al. 1990), demography (Trexler et al. 1992, 1994), population genetics (Trexler 1988), reproductive biology (Trexler 1985; Travis 1989), mating system (Travis et al. 1990; Sumner et al. 1994; Ptacek and Travis 1997; Trexler et al. 1997), and physiological ecology (McManus and Travis 1998). The work revealed several striking phenomena, including facultative matrotrophy (Trexler 1985), spontaneous ovarian cycling (Travis 1989), an olfactory cue for female receptivity (Sumner et al. 1994), and Y‐linked inheritance of male body size (Travis 1994).Figure 1: Some of the animals, plants, and places involved in my own research. Bottom left, Arisaema triphyllum, Giles County, Virginia; top left, Pseudacris ornata, Leon County, Florida; top right, Joel Trexler and James T. Cronin placing fish in field enclosures in a salt marsh, St. Marks National Wildlife Refuge, Wakulla County, Florida; middle right, libellulid dragonfly nymph, Jefferson County, Florida; bottom right, Acris gryllus, Scotland County, North Carolina; bottom center, Poecilia latipinna in the laboratory, collected from Franklin County, Florida; center, Zigadenus muscaetoxicus (Amianthium muscaetoxicum), Giles County, Virginia.View Large ImageDownload PowerPointGood organism‐inspired research is not agnostic to theory. Hypotheses for even the most striking observations are usually guided by theory; Janzen's 1976 essay is a masterful application of existing life‐history theory to the mass flowering of bamboo. In fact, organism‐inspired research often leads to new theory; with the passage of time, mass flowering turned out to be but one example of a broader phenomenon of synchronous reproduction, and theory aimed at that phenomenon followed accordingly (review in Ims 1990). In our molly work, although the initial question might appear agnostic to theory except in its broadest sense, the theory of local adaptation, many of the individual investigations relied heavily on existing mathematical theory for developing specific, testable hypotheses (Reznick and Travis 2001).Alternatively, the question can lead to the organism, in any of three ways. First, we may choose to employ a model system, such as Drosophila melanogaster, Caenorhabditis elegans, Zea mays, or Arabidopsis thaliana, to study a problem. Model systems may be the only practical choice for problems such as mutation accumulation (Mukai et al. 1972; Fry et al. 1999; Shaw et al. 2000; Baer et al. 2005), and they are often a convenient choice for a novel approach to a conceptual question (Travisano et al. 1995; Joshi et al. 2003). Model systems offer a faster and more forgiving path for an intricate study of a general problem that can be addressed in any of many systems—at least in principle—but can be addressed more quickly or more extensively with the model system. Several excellent programs have taken this path; among them are Mueller's studies of evolution in response to density (Mueller et al. 2000), the scrutiny of the genetic response to selection on a quantitative trait conducted by Mackay and colleagues (Mackay 2001), and the exploration of adaptation to thermal regimes led by Lenski and Bennett (Cullum et al. 2001).Model systems reveal what can happen in nature but not necessarily what does happen. In this light, studies with model systems guide those of us who work with natural populations to consider what might have happened in nature and what the alternative happenings might have been. Studies with model systems have also facilitated the development of methods and techniques that can be applied to natural populations so that we can better understand what does happen in nature. This "technology transfer" has been especially fruitful for large‐scale evolutionary studies with Drosophila that have helped us learn not just from model systems but also about them. Examples include the scrutiny of variation in life history (Coyne and Beecham 1987), morphology (Mezey and Houle 2005), physiology (David and Bocquet 1975; Gilchrist and Huey 2004), biochemistry (Oakeshott et al. 1982), host‐pathogen relationships (Jaenike and Perlman 2002), convergent evolution (Balanyà et al. 2003), isolating mechanisms (Coyne and Orr 1997; Noor 1997), and genetic responses to global climate change (Etges and Levitan 2004; Umina et al. 2005).The second path from question to organism emerges when a sound test of theory requires a system whose features match important theoretical assumptions and a scientist with a strong natural‐history background recognizes the propriety of a particular organism or system. The work of Wilbur (1972) and Morin (1983, 1986) with amphibians on the interaction of predation and resource competition in community ecology is a clear example. Their deep knowledge of natural history is implicit in this work and was vital to its success; not only did they recognize the propriety of the systems, but they were adept at creating realistic experimental conditions in which the organisms could grow and develop as they do in nature.The third way in which the question leads to the organism occurs when a particular theory unifies seemingly disparate phenomena and, in effect, tells us to look more widely for patterns that we would not otherwise have sought. Charnov's work on the evolution of sex allocation (synthesized in Charnov 1982) is an excellent example. Charnov offered a general theory that applied to sex ratios in gonochoristic animals, the circumstances under which hermaphrodites could displace gonochores, the allocation to male and female function in simultaneous hermaphrodites, and the way optimal allocation to gender function in sequential hermaphrodites should vary with age or size. This work helped inspire a host of empirical studies in a diversity of systems (e.g., Ashman and Baker 1992; Peterson and Fischer 1996; Roy et al. 2003), and sex allocation theory remains a vibrant topic (see, e.g., Pen and Weissing 1999; Sakai 2000; Cadet et al. 2004).Finally, as individual careers progress, some of us change the questions we ask of the organisms we study, and some of us change the organisms we use to address a particular question. We do so, as Burian (1993) describes, when our curiosity about an organism leads us to new questions or when we approach the limits to an organism's utility for a particular question. Bradshaw's work on pitcher‐plant mosquitoes Wyeomyia smithii traces an arc from his early studies of mutualism between arthropods and pitcher plants (Bradshaw and Creelman 1984) through studies of life history (Bradshaw 1986) to his recent work on hourglass timers and the regulation of circadian and annual rhythms (Bradshaw et al. 2003). Conversely, Huey's work on thermal ecology and the evolution of thermal response moved from a focus on lizards (Huey and Bennett 1987) to the employment of a model system, Drosophila melanogaster (Gilchrist et al. 1997), to a scrutiny of thermal effects on adaptation in natural populations of Drosophila subobscura (Gilchrist and Huey 2004).In rare cases, some of us take the opportunity late in our careers to return to particular questions about specific organisms on which we focused years before, in order to resolve the outstanding issues. Sometimes this return is facilitated by new technology or methods and sometimes by altered personal circumstances. Perhaps the best example is Hairston's remarkable studies of how competition and predation affect the distribution and abundance of plethodontid salamanders; the experimental studies in the latter part of his career (Hairston 1980a, 1980b, 1983, 1986) were separated from the observational studies of his early years (Hairston 1949, 1951) by a rich vein of diverse ecological work (Hairston 1958, 1959, 1967, 1969; Hairston et al. 1960; Hairston and Kellerman 1964, 1965; among many others).How Should We Match Question to Organism?Two general considerations ought to dictate how we choose our organisms, that is, how we match question to organism. First, we should choose on the basis of "suitability," which describes the quality of the reciprocal match of question and organism (Burian 1993). Second, we should take into account that, to borrow again from Burian (1993), the fundamental epistemology of ecology and evolutionary biology is comparative. That is, we can discover what is general only from a broad set of comparisons, and we can often understand the special case only through its relationship to the general pattern. I explore each of these considerations in turn.SuitabilityFollowing Burian (1993), we claim that a specific organism or study system is suitable for a particular question if it fulfills two requirements. First, the organism or system must be tractable for the question; that is, we must be able actually to find it and work with it. This requirement is familiar to every practicing ecologist or evolutionary biologist, and we often take great pains to assure reviewers of grant proposals that indeed we can work with a particular organism. Model systems are created when an extremely tractable organism is discovered to have peculiar but interesting properties; many organisms are easy to raise in the laboratory, but the ability to identify and delineate cell lineages made C. elegans the nematode of choice.The second requirement is that the question actually be relevant for the organism. Burian (1993, p. 353) states it slightly differently, asking "whether the model [here the organism or system] is faithful in relevant ways to that for which it is supposed to serve as a model." In the simplest case, we can ask whether the organism or system meets the assumptions of the theory or concept under consideration; for example, Morin (1983, 1986) selected his anuran prey and their predators because they exhibited the properties that the theory under scrutiny took as fundamental assumptions, so his system was suitable for his purpose. In a deeper case, we can ask directly whether the question itself applies to the organism. For example, the interpretation of an experimental study of the adaptive significance of cannibalism in an animal is open to question if no evidence suggests that the animal engages in cannibalism in nature. We could raise this question in many other contexts, from mate copying (Is the mating system such that copying is possible?) to predator functional responses (Do predators or parasitoids show density‐dependent attack rates in the natural range of densities?); Gunzburger and Travis (2005) have questioned the interpretation of many reports of unpalatability of tadpoles because the tadpoles were offered to predators that rarely, if ever, encounter them in nature.In a subtle variation, we can ask whether the experimental treatments employed to test a concept create a misleading result; that is, the question may apply, but the design and execution of the experiment may create artificial conditions that can bias the outcome in a particular direction. Expressed yet another way, the question applies but the experiment does not. For example, Jaeger and Walls (1989) criticized experimental studies of anuran populations and communities conducted in enclosures or mesocosms (large tanks set up as artificial ponds) because, among other reasons, the experiments up to that time had employed densities far higher than were measured in nature. The concern was that such experiments could not help but implicate an important role for biotic interactions in this system, a role that may not be fulfilled at lower, presumably more natural densities. Subsequent experiments at much lower densities (e.g., Warner et al. 1991, 1993; Gascon and Travis 1992) revealed the same effects seen in the earlier studies but found, indeed, that the strength of the biotic effects had previously been overestimated.Suitability of an organism has two important features. First, suitability can be specific to a particular context (Zallen 1993). Sailfin mollies in north Florida have proved suitable for studies of sexual selection and mating‐system variation but not for numerical dynamics; the effects of tidal fluctuations in salt marshes and the physical structure of these habitats precluded reliable sampling for population densities. Working in the Everglades, however, Trexler and his colleagues have found sailfin mollies quite suitable subjects for studying numerical dynamics, among other topics (Trexler et al. 2002).Second, the suitability of a system for a question may change as other questions are addressed and answered in the system. For example, the genetic control of pattern variation in Papilio dardanus offers important insights into the origin of mimicry, but the full utility of this system became apparent only after Nijhout's work on the developmental biology of lepidopteran wings (Nijhout 2002, 2003). The value of protein variation within many fish species for studying the genetic basis of adaptive variation improved dramatically when sophisticated methods for determining protein structure at a very fine scale were developed, along with the ability to determine the detailed sequence and structure of the genes involved (see Hochachka and Somero 2002). Suitability need not always improve; the discovery of reciprocal chromosome translocations in Oenothera lamarckiana compromised its suitability as a system for illustrating the constraints on the response to selection on quantitative traits (Provine 1971).Recognizing the Comparative Nature of Our EpistemologyThe comparative nature of our epistemology dictates three principles that ought to guide our collective choice of organisms.A well‐sampled spectrum is necessary for understanding diversity and defining generalities. To be specific, a well‐sampled spectrum serves to define the most common patterns and processes and identify the circumstances through which less common patterns and outcomes emerge. Of course, morphologists have known and applied this principle for centuries; understanding peculiar anatomical variations such as the fangs of venomous snakes or the toothless gape of egg‐eating specialist snakes requires appreciating a spectrum of ophidian skull morphology (Gans 1974). The principle is becoming well appreciated in "molecular morphology" as well; the spectrum of variation in the structure of the antifreeze glycoproteins in fish, when combined with genomic information in a phylogenetic context, reveals an astounding story of convergence and idiosyncrasy in adaptation (Fletcher et al. 2001).New discoveries can change tentative generalities. Although the scientific process stimulates a continuous refinement of our epistemic basis, from time to time new discoveries overturn a paradigm completely. Not all cases are historical; a recent example is the change in our view of life‐history evolution in the desmognathine salamanders. The traditional view was that direct development, the loss of the aquatic larval stage, was a recently derived life history, a sensible view in light of how few directly developing desmognathines were known and how extremely limited were their geographic and habitat distributions. However, the discovery in the 1960s of the directly developing species Phaeognathus hubrichti, a more complete understanding of species' distributions and ecology, and the employment of sophisticated molecular methods for testing phylogenetic hypotheses have combined to indicate that direct development is the ancestral condition (Chippindale et al. 2004; Mueller et al. 2004).We can identify other recent examples in which new discoveries, empirical or theoretical, called existing paradigms into question. Polis's (1991) detailed description of omnivory in a desert food web, following Paine's (1988) critique of food web theory, helped redirect that theory. Reznick et al.'s (1997) documentation of rapid evolution of guppy life histories helped usher in a new perspective on the likelihood of very rapid evolution (Kinnison and Hendry 2001; Reznick and Ghalambor 2001; Frankham and Kingsolver 2004). Spichtig and Kawecki's (2004) examination of multilocus soft selection in a subdivided population revealed that, in general, such soft selection does not protect extensive genetic variation; the impression to the contrary has been cultivated by generalization from the earliest single‐locus models of the process, and the generalization appears to have been misleading.Robust inference requires horizontal comparisons and vertical integration. Our modern emphasis on process biology puts high value on horizontal comparisons, the examination of the same question at the same level in a variety of systems. Horizontal comparisons have revealed general processes, such as the reciprocal‐yield and 3/2 thinning laws in plants (Harper 1977), trophic cascades (Carpenter and Kitchell 1993), and the preference of females for male signals associated with size or vigor (MacLaren et al. 2004). When horizontal comparisons are synthesized quantitatively, larger generalities often emerge; the patterns of biogeography are an excellent example (Brown 1984; Harte et al. 1999; Hubbell 2001).A truly robust epistemic basis for ecology and evolutionary biology also requires vertical integration, the study of many ecological and evolutionary processes as they unfold in a single species or system. Indeed, one might argue that the great challenge of biology in this century will be to connect our understanding across different levels of organization. Many of us are devoting more effort toward such integration; indeed, a number of species and systems have emerged as "natural models" for the study of an integrated ecology and evolutionary biology, including animals such as Poecilia reticulata and Gasterosteus aculeatus and plants such as Silene latifolia and Trifolium repens. A sampling of recent literature devoted to S. latifolia includes studies of genetic population structure (Giraud 2004; Ingvarsson 2004; Tellier et al. 2005), molecular evolution (Sugiyama et al. 2003; Ingvarsson 2004; Lengerova et al. 2004; Filatov 2005), floral genetics (Delph et al. 2004a; Meagher et al. 2005) and development (Ageez et al. 2003; Delph et al. 2004b; Matsunaga et al. 2004), nectar production and composition (Gehring et al. 2004; Dotterl et al. 2005), and invasion biology (Wolfe et al. 2004). The value of integrated knowledge is aptly illustrated in the studies by Brakefield and his colleagues on the evolution and ecology of the tropical butterfly Bicyclus anynana (Fischer et al. 2003, 2004; Molleman et al. 2004; Zijlstra et al. 2004; Frankino et al. 2005; Saccheri et al. 2005; Steigenga et al. 2005; van't Hof et al. 2005).Does Our Self‐Organizing System Enforce Suitability and Encourage a Comparative Epistemology?Without doubt, our system encourages one aspect of suitability, that the organism be tractable for the question. Proposals to funding agencies rarely trumpet that the proposed study organism is sparsely distributed, occurs in low numbers, is difficult to find and impossible to maintain, has critical features that cannot be measured, or is otherwise intractable for careful observation or deployment in powerful experiments. One cannot imagine a phylogenetics proposal that points out that the group to be studied has no informative characters or that the only genes that can be sequenced evolve at rates that cannot resolve the relationships among the member taxa.Whether we give sufficient encouragement to considering whether the question applies to the organism is another issue. If the literature includes declarations of prey unpalatability diagnosed from predators that do not encounter the prey (Gunzburger and Travis 2005), then it probably holds many examples of inappropriately directed questions that are less easily recognized by readers without extensive familiarity with the organism. In these cases, the organisms are being used, in effect, as analog simulations of an interesting ecological or evolutionary process. If this is the real idea behind such work, genuine digital simulations would seem a much wiser choice (see, e.g., Yedid and Bell 2001; Chow et al. 2004).Our best‐known systems, both model systems and "natural models," are not random samples of their larger groups. Our model systems are, by and large, human commensals that have probably experienced rapid population growth in the last several thousand years. Although we can argue over which genetic or genomic properties might be biased by this history, expecting no bias would be naive. For example, the chiasma frequencies of domesticated mammals are not representative of those in mammals as a whole (Burt and Bell 1987). Many of our emerging "natural models" are cosmopolitan taxa usually found at high densities (Poecilia reticulata is an obvious exception to the cosmopolitan attribute). This is not to claim that these systems offer idiosyncratic results but to argue that we will not recognize which results are idiosyncratic without a wider foundation of comparative investigation.Whether the conclusions we draw from our horizontal comparisons are sufficiently robust depends on whether we have sampled taxonomic and character diversity properly. Although practitioners of meta‐analyses or comparative studies worry explicitly about their sampling of taxa or characters, we may not worry enough about the sampling of our examples when we attempt a synthesis or seek generalizations. We sometimes make premature generalizations or fail to appreciate fully that a particular generalization might not be robust because it emerges from a circumscribed sample of systems, a limited range of diversity, or a peculiar set of experiments. For example, the earliest studies of biochemical variation were motivated in part by the possibility that generalizations about the ubiquity of adaptive genetic variation might be overly influenced by their emergence from studies of visible polymorphisms (Lewontin 1974). In another arena, ecologists argue whether trophic cascades are a general or a circumscribed phenomenon, and one part of this argument seems, at least to me, to maintain that their apparent prominence was a premature generalization from marine and aquatic systems (Polis and Strong 1996; Oksanen and Oksanen 2000).Even less clear is that we wrestle with the sampling of taxonomic, character, and system diversity when we conceive and design our original empirical work. We often let the organism lead to the question or find the most tractable organism for a question rather than seeking an organism or system whose attributes place it in an especially critical position for understanding the broad issue at hand. Reznick's study of the life‐history diversity in female poeciliid fishes illustrates how, ideally, we would approach these problems (Reznick and Miles 1989; Reznick et al. 1992, 2002; Arias and Reznick 2000); his initial survey isolated critical questions and critical taxa, and his subsequent efforts have been focused accordingly. Of course, "ideal" is not always possible or practical, and most of the time the best we can do may be to build our generalities and principles gradually from the organisms and systems that are available and suitable.An emerging issue is whether we apply the criteria of suitability when we embark on meta‐analyses or other exploitations of preexisting data. Obviously, we employ the first criterion of suitability, which is tractability; the data are available, so we use them. Whether those data are faithful, in relevant ways, to the question for which they will be exploited, even though they were collected for another purpose, is the critical issue.This issue is central to an already large and still‐burgeoning literature in ecology and evolutionary biology that exploits preexisting data of one sort or another. For example, the ecomorphological community studies of Ricklefs and Travis (Ricklefs and Travis 1980; Travis and Ricklefs 1983) are based on measurements of museum specimens—one type of preexisting data—and their validity relies on the assumption that those specimens are representative samples of the morphological variation in those species in those areas. Museum or herbarium specimens have been used to approach a wide variety of topics in ecology and evolutionary biology (see recent articles by McGlynn [1999], Simberloff et al. [2000], and Knouft [2003]); some conclusions are more likely than others to be robust to collection biases.The use of tabulated and archived data in meta‐analyses and synthetic analyses carries its own risks of inadvertent bias. In some cases, such as studies of numerical dynamics, the data are being used for the same purpose for which they were collected (e.g., Kendall et al. 1998), but in others, data collected for one purpose are exploited for a different one, and in these cases the potential for bias is an important issue. For example, many early quantitative analyses of food webs exploited data that were collected as by‐products of other work (Cohen et al. 1993), and substantial biases were present (Paine 1988).The biases can arise in many ways. For example, Jeff Leips and I published a study of numerical dynamics in Heterandria formosa that included density estimates of many other species (Leips and Travis 1999). It would be tempt