A few years ago, in another life, I was listening to an M.Sc. student provide a progress report to her advisory committee. She was tackling the problem of whether there were two, or just one genetically distinct population of sea-run trout using a particular lake in British Columbia. The managers knew there were two runs of spawning fish, an early one and a later one; they needed to know if these needed to be managed as separate populations. Our student’s problem was that this was a small lake and the late run had relatively few fish. While she was only catching the fish for a fin clip and then releasing them, there was occasional mortality and she did not want to be responsible for further reducing a threatened population. I asked what I thought was a simple question, “Can you tell the fish apart?” She looked puzzled, and answered, “No, I haven’t run the DNA sequences yet.” I looked puzzled, and said, “No, I mean can you tell the fish apart?” She looked more puzzled, and her advisor, a population geneticist used to talking to ecologists, said, “Peter means, if you look at the fish carefully, can you see any differences among them?” “Oh”, she replied, “I don’t know; I haven’t looked.”
She was a good student, but she had not yet learned an important lesson – get to know your animals. It is a lesson that serves the biologist in good stead whenever the question being asked concerns the organism being used in the study. That is not ‘always’, because biology is a field of study with a split personality.
Biophils and Mechanophils
There are those biologists – I’ll call them biophils — who are concerned about ecosystems, populations, individuals; and who ask questions at molecular, organismal, population or ecosystem level that concern how those creatures do what they do when they do it, and how all that doing creates a cohesive whole. And there are biologists – I’ll call them mechanophils — who are concerned with biological processes that take place among molecules, within cells, or within and sometimes among individuals, that they believe are fundamental to life. Mechanophils use ‘model systems’, ‘preparations’, ‘tissue lines’, and sometimes ‘animals’, but they are not concerned with what those creatures do or how, when or why they do it. They are concerned with the specific process and how it functions in a living system. I’ve always had trouble understanding mechanophils, because the questions they spend their lives on always seemed to me fundamentally less interesting than why, how, when, or what creatures do in the course of their lives. I know many of them have trouble understanding biophils like me, who revel in the unexpected variety of life, never tire of just-so stories, but could never get excited about the intricacies of metabolic goings-on within five or six cells in the tail-end of a tiny worm of a single species that has lived in lab culture for generations. What about all the other worms? Fortunately, the biological world is rich enough to sustain a diversity of approaches. Population geneticists are one group of biologists who regularly find themselves on the interface, attempting to communicate across this mechanophil – biophil divide, and the better ones are worth their weight in gold, simply as translators.
Getting to know your animals (or plants, or ecosystem) takes time, and university education increasingly sees that as time not well spent. Far better to master a new technique for measuring the biological world more precisely, or for handling vast quantities of data, sifting through them hunting for patterns that might be worth pursuing. It’s especially better to spend time mastering use of a new, expensive gizmo so that your results will be somehow flashier than anyone else’s. Along the way, generations of students have missed the opportunity to explore the complexity which is the hallmark of life while getting to know their animals.
Biologists all suffer from physics envy, embarrassed that they work in a field that is never going to find the question that belongs with the answer “42”, and is certainly never going to develop a “theory of everything” that will consist of a line or two of arcane mathematical symbols, and will cause the whole world of science, for one brief moment, to exhale in unison a single sustained note of exaltation and awe. No E=MC2 for biologists.
Especially when you study biology at the population or ecosystem level, biology lacks explicit axioms, and reveals a bewildering diversity of answers to any question posed. Biologists should celebrate that diversity, but mostly we seek ways to minimize it. That’s one reason why the mechanophils amongst us narrow their attention to a single preparation or model system. And that is what helps drive reductionism in all branches of biology – strip away the unusual, reject the outliers, focus in on the modal result, and go ever deeper into what causes that modal result. If the modal result happens 1% of the time, knowing in detail how and why it happens is only a modest step forward. What about the 99% of the time?
There is no good reason for talented biologists to feel inferior to physicists, even if we are not able to develop succinct equations that describe biological complexity. Image © Ikcd.com
Physics envy is also why we long for instrumentation that can yield precise measurements quickly and easily, and why we reject fields of enquiry that necessarily require enormous amounts of time sorting through field samples, or data. Phytoplankton ecologists know that chlorophyll concentration, as measured by a satellite scanning the ocean surface, is only a very rough proxy for the rich and dynamic phytoplankton community that is present there. But they still devote considerable effort to studies in which the closest they get to phytoplankton is a measure of chlorophyll concentration. Getting to know your phytoplankton takes far longer than downloading the chlorophyll data. Yet, what do we miss when we reduce an entire community of creatures to the intensity of the green color they carry in their organelles?
Our physics envy also drives our desire for simple explanations, even when investigating things as complex as ecosystems. We hope to find clearly defined causes for observed responses or patterns. We believe that a simple explanation is necessarily a sign of ‘better’ science, but if life is not simple, why should simple explanations, simple hypotheses, simple rules be the expected outcome of investigating that life? I am not suggesting that biologists throw away Occam’s razor, the maxim that when a simple and a more complicated hypothesis explain the observations equally well, the simpler hypothesis is the preferred choice. But I am suggesting that we should not expect simple hypotheses to be sufficient explanations for reality in most cases. We should be more skeptical of simple explanations than we sometimes are – if they seem too pat, they probably are.
It’s true that simple hypotheses make it possible to construct simple stories that serve to explain the living world. But does that make those stories superior to more complicated stories built out of more complex hypotheses? Simple stories can be too simple to be useful, but in a sound bite world, we seem to be forgetting this. What is the likelihood of explaining a complex world when our simple explanations have been generated from data generated after stripping away the complexity that is always there in raw nature. Biologists need to encourage their students to celebrate complexity, and be aware that simple stories will be rare when we study life.
The resilience of coral reefs
And so I ramble back to ecology of coral reefs, and two interesting papers. The first, by Joe Pawlik of UNC Wilmington, Deron Burkepile of UC Santa Barbara, and Rebecca Thurber of Oregon State University, was published online April 27th in Bioscience. The second, by George Roff and Pete Mumby of University of Queensland, appeared in Trends in Ecology and Evolution in 2012. They both concern the factors determining the ecological structure of coral reefs and the resilience to disturbance possessed by reef systems.
The physical structure of a coral reef is generated by calcifying organisms, chiefly corals. They are called coral reefs because corals are so conspicuous as members of the benthic community and because coral-derived carbonate rock is a major portion of the rocky structure itself. In recent years, for a variety of reasons, many coral reefs around the world have become degraded. The abundance of coral, usually measured as percent cover of the substratum, has been reduced, and foliose algae, along with other sessile invertebrates, have taken over much or all of the space formerly occupied by coral. In some cases, it is known that the rate of accretion of carbonate rock, or ‘reef growth’, has fallen or ceased because of the loss of living coral. The change through time is so profound that it is common to speak of a phase shift from a coral-dominated to an algae-dominated reef system.
Does this look like an ecosystem that could be modelled as three boxes: coral, fish, algae? The complexity of a coral reef is amazing even when you have visited thousands of them.
Photo © Vladimir Levantovsky.
A prominent hypothesis to explain this rather dramatic replacement of corals hinges on ecosystem resilience, the presumed competition for living space among the corals, algae and other sessile invertebrates, and the possible role of herbivory in keeping algae in check. This hypothesis (I’ll call it herbivore-mediated coral dominance) states that on a healthy (i.e. coral dominated) reef, herbivory by fish, sea urchins and other small invertebrates, curtails the growth of algae. When coral abundance is reduced in such places, whether by storms, bleaching, diseases or pollution, corals reproduce and regenerate and recovery is achieved – such systems are resilient to disturbances to the coral community. In contrast, on degraded reefs, subject to overfishing (and associated impacts due to human activity and poor reef management), if coral abundance is reduced by storms or other factors, the growth of algae is sufficient to rapidly take over the vacated space, impeding recruitment of corals, and the system shifts into an algal-dominated state that is then resistant to shifting back to one in which corals are abundant. The degraded reef has proved less resilient to loss of coral and has not been able to recover, largely because grazing on its algae was not sufficient to keep their growth in check.
There are places in the Caribbean for which the evidence largely supports this hypothesis, but the Caribbean itself is not uniform, and when we look outside the Caribbean, evidence to support this hypothesis is far less prevalent. Roff and Mumby review many ways in which Indo-Pacific and Caribbean reefs differ, and note in particular that coral recovery following disturbance was far more prevalent in the Indo-Pacific. Based on 41 separate multi-year studies of Pacific sites, and 74 studies of Caribbean sites, spread over the period from 1965 to the present, they found that 46% of Pacific studies but none of the Caribbean studies showed ‘recovery’. (They defined recovery as a loss of at least 33% of initial coral cover followed by recovery of at least 50% of the amount lost.)
Clearly, reality is more complex than the simple hypothesis of herbivore-mediated dominance of corals suggests, and Pacific reality seems to have very little to do with this hypothesis. Roff and Mumby offer six separate, though not mutually exclusive, hypotheses that might account for the differences in resilience, and in coral and algal abundances among reefs. The first notes the very different growth rates among corals; species of Acropora, in particular, are fast-growing, while many other coral genera grow quite slowly. While Pacific reefs support over 30 species of fast-growing Acropora, only two species of this genus occur in the Caribbean, and both have been substantially reduced in abundance since the early 1980s, chiefly through disease. This first hypothesis suggests that herbivory on algae can only facilitate recovery of coral abundances following a disturbance if fast-growing coral species are available to rapidly occupy vacant space. Otherwise, despite herbivory, algae will still occupy the space before slow-growing coral species are able to fill it. Under this ‘Acropora loss’ hypothesis, the difference in resilience between Pacific and Caribbean reef systems is due to the relative lack of fast-growing corals in the Caribbean.
Their second ‘functional redundancy’ hypothesis begins with the much greater diversity of herbivores in the Pacific. Among herbivorous fish, Caribbean reefs support only 4 species of one genus of surgeonfish, 15 species of four genera of parrotfish, and no rabbitfishes, while Pacific reefs support 84 species of 6 genera of surgeonfish, 83 species of 9 genera of parrotfish and 23 species of rabbitfish. This hypothesis states that a richer herbivore group will do a more effective job of curtailing algal growth because each of the different species does different parts of the job best, but they all work together. Thus, even when overfishing has suppressed numbers of herbivores, the richer Pacific groupings are still able to keep algae in check, while the depauperate Caribbean groupings are less able to do that.
Their next three hypotheses proposed all concern the possibility that algal growth is faster in the Caribbean. Perhaps there is faster recruitment of algal propagules onto bare reef rock in the Caribbean (hypothesis #3), or there are more nutrients available in Caribbean waters, favoring faster algal growth (hypothesis #4), or trace elements such as iron that can limit plant growth are more available in Caribbean waters (hypothesis #5). Any one of these three possibilities would result in more rapid occupancy of reef space vacated by dying corals on Caribbean reefs, regardless of levels of herbivory. Finally, as their 6th hypothesis, Roff and Mumby suggest that the differences in composition and abundance of fish communities in the Pacific and Caribbean are such that there is a higher absolute rate of grazing on Pacific reefs, such that algal have difficulty supplanting corals even when disturbances briefly knock back coral populations.
Roff and Mumby discuss the evidence in favor of or against each of these hypotheses and end by advocating the need for experimental work to discriminate among them. And there the matter has seemed to sit since 2012.
In the 2016 paper, Pawlik and colleagues begin by summarizing the results of Roff and Mumby. They then provide several examples of sites in the Caribbean where algal growth has proved largely independent of abundance of herbivorous fishes, or may even be enhanced when fish are abundant, likely because fish excrete nutrients that facilitate algal growth. Then, they introduce us to sponges.
One of the large barrel sponges, Xestospongia muta, on a Bahamian reef. Photo © J.R. Pawlik
Sponges are typically more abundant on Caribbean reefs than on Pacific reefs, and are mostly heterotrophic, while Pacific sponges are primarily phototrophic, possessing algal symbionts much as corals do. Sponges filter feed taking particulate matter – both plankton and POC (particulate organic carbon, also called organic detritus) – from the water column, but can also absorb DOC (dissolved organic carbon). Recent research has shown that the role of DOC in sponge metabolism is as, or more important than the role of POC. In fact, sponge biologists talk of a “sponge loop” in which sponges feed on DOC while exuding POC in the form of cellular detritus which is ingested by corals and various detritus-feeding invertebrates on the reef. Meanwhile corals and algae are exuding DOC back to the water column.
The “sponge loop” is analogous to the “microbial loop” that cycles DOC through plankton, and it is about here that I have to struggle to understand because I spent a reasonably successful career maintaining that one could be quite successful studying coral reef ecology without paying attention to anything too small to see. I maintained that if it was so small you could not see it with the naked eye, it could not be important in the ecology of fishes, and for many years, my lab was a microscope-free zone. In retrospect, I am sure I had blinkers on.
Diagrams showing the difference between Caribbean and Pacific reef systems. In the Caribbean (top) there is an abundant inflow of DOC (red), plus nutrients from dust (green), and a number of trophic pathways among sponges, corals, algae, plankton and fish. On Pacific reefs, there is less influx of DOC, fewer (and mostly phototrophic) sponges, and relatively weaker trophic pathways among corals, algae, plankton and fish. Figure © J. Pawlik and Bioscience.
Anyhow, Pawlik and colleagues go on to point out that unlike plankton, sponges are able to metabolize refractory DOC as well as the (much less abundant) labile DOC used by other organisms. Refractory DOC is common in river water, and the Caribbean basin is the destination of at least three major rivers, the Amazon, Orinoco, and Mississippi, which carry 30.7, 4.3, and 2.3 teragrams carbon per year (TgCyr-1) respectively. Most of this large amount of carbon is refractory DOC. They also refer to the abundance of African dust which deposits important trace nutrients, such as iron, in the Caribbean. Putting everything together, they suggest that a major, neglected difference between Caribbean and Pacific reefs, is that the Caribbean reefs exist in a relatively small basin with an abundant supply of refractory DOC, and the reefs support lots of sponges that feed on this material. By feeding on the flux of DOC, and then shedding detritus as POC, the sponges are serving as a mechanism for importing organic carbon to the reef system, thereby enhancing possible metabolic rates of various organisms there.
Why have Caribbean reefs failed to prove resilient and recover coral abundance following disturbances such as diseases that reduced coral cover? Pawlik and colleagues suggest that the Caribbean is much more trophically dynamic than the Pacific, because of the sponges, and algae are capable of growing more rapidly as a result. They can often overwhelm grazing by fish and rapidly capture space lost to corals. This is especially the case if fish abundances have been reduced by overfishing. In the much more nutrient-limited Pacific, algae cannot grow as aggressively, even when herbivory is reduced through overfishing.
Putting the two papers together, I see a number of plausible hypotheses to explain the differences between the Pacific and the Caribbean in the interactions of corals, herbivorous fishes, algae and sponges. The hypotheses are not all mutually exclusive (several of the mechanisms could be acting together), and sorting amongst them will be challenging. But science is always more fun when it is challenging, and reality is likely hidden among these hypotheses. The simple herbivore-mediated model of coral dominance (remove parrot fishes and algae out-compete corals) is nice and tidy, but clearly does not cover the complexity of reality. It is time to do some careful, experimental research to understand the resilience of coral reef systems.
The need for hypothesis-testing research
Hypotheses are just ‘what if’ statements. They offer plausible explanations of observations about the way the real world works. But hypotheses cry out to be tested. Indeed, they are just the stuff of a beer-fed conversation until they are tested. Most will be proved wrong, and that is how science makes progress – by proposing all sorts of plausible hypotheses, rigorously testing and rejecting them one by one, until one or more prove difficult to reject. In my view, we reef ecologists are not spending enough time testing hypotheses in the real world, and our understanding of the systems we study is not advancing as rapidly as it could. (And before anyone jumps up and down and puts out a fatwa on me, let me add that I am NOT suggesting that reef ecology has a weaker record than other fields of ecology or of biology. That this field of ecology is strong justifies me in demanding it get stronger.)
The fact is, hypothesis-testing is difficult and it takes time. Even the generation of hypotheses is difficult, and hypothesis-generation requires that you know your animals, or ecosystems. Too many students today learned all they are ever likely to learn about sponges in half a lecture in an introductory course in invertebrate biology – if they even got such a course, now termed ‘survey’ courses to indicate how trivial, old-fashioned, and irrelevant such courses are. (I think the situation has deteriorated, but the fact I was able to get through 65% of my career operating my lab as a microscope-free zone, shows that even in the Dark Ages it was possible to avoid vast areas of important science in the course of becoming ‘educated’.) I learned a number of new things (for me) about sponges by reading the Pawlik paper – I guess it’s never too late!
Testing ecological hypotheses is difficult because you mostly cannot bring ecosystems into the controlled conditions of a lab. Field experiments require considerable ingenuity, take time to set up, and often take long periods of time before results are obtained. Ecological processes mostly do not operate on timescales of hours or days.
Often there are no realistically possible manipulative experiments that could be done to test a particular hypothesis, and thus ecologists look for ‘natural experiments’ or use simulation models as alternative approaches. Neither is as powerful in rejecting hypotheses as a real experiment, and tests using models, while they produce beautiful results in minutes or hours, are only as powerful as the models themselves. If you do not know about sponges, you’d probably model the resilience of a Caribbean reef with only fish, corals and algae present. No model can reveal the importance of particular processes, or organisms, if those processes or creatures are not included in the model! I know we can use a combination of models, natural experiments and real experiments to test ecological hypotheses for coral reef systems – it’s been done before – but we absolutely have to know our reefs to design those tests. Too few of us know our reefs.
Field experiments come in many shapes and sizes. MIT students sampling sponges were working from the underwater habitat, Aquarius, off the Florida Keys, as was the Georgia Tech student checking herbivore cages. In the center, University of Queensland scientists monitor an ocean acidification experiment on the reef flat at Heron Island, GBR.
Photos L to R © MIT, MBARI, Georgia Tech
And so I plead for spending more time in the field learning about the ecological systems we want to study. More field time for undergraduates, far more field time for graduate students and post-docs, and reasonable amounts of field time even for established researchers. Not field time to run experiments, or carry out sampling programs that were dreamed up months ago, high and dry, while writing an imaginative research proposal, but time to tinker, to poke and prod, to watch and think about the system being studied.
I suspect I am swimming against the tide. Gone are the days when graduate students got set free on a coral reef. Now every hour of field time costs money and every dive requires an approved dive plan, multiple extra people to ensure safety, and sufficient pre-dive planning of the science to be done to ensure that every minute is productive. Looking around, wondering, and even trying a few things out just for fun is frowned upon – we must operate more like armies marching into battle than as the curious, enquiring scientists we are supposed to be. And yet, if reef science is going to provide new tools for more effective management, we need to be solving the critical questions. To do this, we need to know our chosen ecosystem.
Bleaching of the Great Barrier Reef
The recent GBR bleaching has proven to be quite severe. That it impacted the remote northern third of the region so severely does not portend well for the global future of coral reefs. Yet I have hope that some good may come of it because of the effort made by the Australian marine science community to document it, and to follow up with longer-term study of what happens after the bleaching is over. That it was scientist-driven, and knowing a number of the scientists involved, gives me hope that something more is going to result than a precise description of just where, when and how much reef was lost. Such information can be useful, but we need to get beyond simple monitoring of the collapse of coral reefs. I hope that there will be plenty of effort during subsequent months and years to document the recovery, and to test competing hypotheses for what is happening and why. Only in this way are we likely to generate a sufficient understanding of how reefs respond to a warming climate that we will be able to generate realistic approaches to mitigate damage or to assist reefs to recover. There are going to be more bleaching episodes on coral reefs, and our future looks increasingly likely to be one without coral reefs. Even if that dismal possibility is the eventual outcome of our current enthusiasm for fossil fuels, it would be nice to know that the reef science community did all it could to understand what was happening and seek remedies.
Overall, I hope to be pleasantly surprised by the quality of coral reef science that will be on display at the 13th International Coral Reef Symposium in Honolulu in just four short weeks from now. I dream of being proved completely wrong about the extent to which our current crop of reef researchers know their animals and ecosystems. Maybe coral reef science is far more robust than I give it credit for. But if so, shouldn’t somebody be busily testing that multiplicity of hypotheses that Roff and Pawlik and their colleagues have presented? And shouldn’t there be wider recognition that the simple herbivore-mediated model of coral dominance is way too simple? And shouldn’t we be making a major effort to understand the consequences of a global pattern of enhanced frequency of bleaching events? And shouldn’t we all know that there is lots we do not know about this amazingly complex ecosystem, and be trying to learn more?
If we only manage to monitor the progressive decline of coral reefs as successive bleaching events occur, we will simply be monitoring one important aspect of the sixth extinction. A detailed documentation of the step by step, species by species, set of extinctions that form the sixth extinction could be a mammoth undertaking that would take many scientist-hours, but it would also be of little real value after it is all over. I’ll have my fingers crossed for Honolulu.
There are more things in heaven and earth, Horatio, than are dreamt of in your philosophy. Incredible image of a pygmy seahorse. Photo © Alexander Franz.