Tag Archives: progress in ecology

Is Ecology Becoming a Correlation Science?

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One of the first lessons in Logic 101 is classically called “Post hoc, ergo propter hoc” or in plain English, “After that, therefore because of that”. The simplest example of many you can see in the newspapers might be: “The ocean is warming up, salmon populations are going down, it must be another effect of climate change. There is a great deal of literature on the problems associated with these kinds of simple inferences, going back to classics like Romesburg (1981), Cox and Wermuth (2004), Sugihara et al. (2012), and Nichols et al. (2019). My purpose here is only to remind you to examine cause and effect when you make ecological conclusions.

My concern is partly related to news articles on ecological problems. A recent example is the collapse of the snow crab fishery in the Gulf of Alaska which in the last 5 years has gone from a very large and profitable fishery interacting with a very large crab population to, at present, a closed fishery with very few snow crabs. What has happened? Where did the snow crabs go? No one really knows but there are perhaps half a dozen ideas put forward to explain what has happened. Meanwhile the fishery and the local economy are in chaos. Without very many critical data on this oceanic ecosystem we can list several factors that might be involved – climate change warming of the Bering Sea, predators, overfishing, diseases, habitat disturbances because of bottom trawl fishing, natural cycles, and then recognizing that we have no simple way for deciding cause and effect and therefore making management choices.

The simplest solution is to say that many interacting factors are involved and many papers indicate the complexity of populations, communities and ecosystems (e,g, Lidicker 1991, Holmes 1995, Howarth et al. 2014). Everyone would agree with this general idea, “the world is complex”, but the arguments have always been “how do we proceed to investigate ecological processes and solve ecological problems given this complexity?” The search for generality has led mostly into replications in which ‘identical’ populations or communities behave very differently. How can we resolve this problem? A simple answer to all this is to go back to the correlation coefficient and avoid complexity.

Having some idea of what is driving changes in ecological systems is certainly better than having no idea, but it is a problem when only one explanation is pushed without a careful consideration of alternative possibilities. The media and particularly the social media are encumbered with oversimplified views of the causes of ecological problems which receive wide approbation with little detailed consideration of alternative views. Perhaps we will always be exposed to these oversimplified views of complex problems but as scientists we should not follow in these footsteps without hard data.

What kind of data do we need in science? We must embrace the rules of causal inference, and a good start might be the books of Popper (1963) and Pearl and Mackenzie (2018) and for ecologists in particular the review of the use of surrogate variables in ecology by Barton et al. (2015). Ecologists are not going to win public respect for their science until they can avoid weak inference, minimize hand waving, and follow the accepted rules of causal inference. We cannot build a science on the simple hypothesis that the world is complicated or by listing multiple possible causes for changes. Correlation coefficients can be a start to unravelling complexity but only a weak one. We need better methods for resolving complex issues in ecology.

Barton, P.S., Pierson, J.C., Westgate, M.J., Lane, P.W. & Lindenmayer, D.B. (2015) Learning from clinical medicine to improve the use of surrogates in ecology. Oikos, 124, 391-398.doi: 10.1111/oik.02007.

Cox, D.R. and Wermuth, N. (2004). Causality: a statistical view. International Statistical Reviews 72: 285-305.

Holmes, J.C. (1995) Population regulation: a dynamic complex of interactions. Wildlife Research, 22, 11-19.

Howarth, L.M., Roberts, C.M., Thurstan, R.H. & Stewart, B.D. (2014) The unintended consequences of simplifying the sea: making the case for complexity. Fish and Fisheries, 15, 690-711.doi: 10.1111/faf.12041

Lidicker, W.Z., Jr. (1991) In defense of a multifactor perspective in population ecology. Journal of Mammalogy, 72, 631-635.

Nichols, J.D., Kendall, W.L. & Boomer, G.S. (2019) Accumulating evidence in ecology: Once is not enough. Ecology and Evolution, 9, 13991-14004.doi: 10.1002/ece3.5836.

Pearl, J., and Mackenzie, D. 2018. The Book of Why. The New Science of Cause and Effect. Penguin, London, U.K. 432 pp. ISBN: 978-1541698963

Popper, K.R. 1963. Conjectures and Refutations: The Growth of Scientific Knowledge. Routledge and Kegan Paul, London. 608 pp. ISBN: 978-1541698963

Romesburg, H.C. (1981) Wildlife science: gaining reliable knowledge. Journal of Wildlife Management, 45, 293-313.

Sugihara, G., et al. (2012) Detecting causality in complex ecosystems. Science, 338, 496-500.doi: 10.1126/science.1227079.

Five Stages of Ecological Research

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Ecological research falls into five broad classes or stages. Each stage has its strengths and its limitations, and it is important to recognize these since no one stage is more or less important than any other. I suggest a classification of these five stages as follows:

  1. Natural History
  2. Behavioural Ecology
  3. Applied Ecology
  4. Conservation Ecology
  5. Ecosystem Ecology

The Natural History stage is the most popular with the public and in some sense the simplest type of ecological research while at the same time the critical foundation of all subsequent research. Both Bartholomew (1986) and Dayton (2003) made impassioned pleas for the study of natural history as a basis of understanding all the biological sciences. In some sense this stage of biological science has now come into its own in popularity, partly because of influential TV shows like those of David Attenborough but also because of the ability of talented wildlife photographers to capture amazing moments of animals in the natural world. Many scientists still look upon natural history as “stamp-collecting” unworthy of a serious ecologist, but this stage is the foundational element of all ecological research.

Behavioural ecology became popular as one of the early outcomes of natural history observations within the broad framework of asking questions about how individuals in a population behave, and what the ecological and evolutionary consequences of these behaviours are to adaptation and possible future evolution. One great advantage of studying behavioural ecology has been that it is quick, perfectly suited to asking simple questions, devising experimental tests, and then being able to write a report, or a thesis on these results (Davies et al. 2012). Behavioural ecology is one of the strongest research areas of ecological science and provides entertainment for students of natural history and excellent science to understand individual behaviour and how it fits into population studies. It is perhaps the strongest of the ecological approaches for drawing the public into an interest in biodiversity.

Applied ecology is one of the oldest fields of ecology since it arose more than 100 years ago from local problems of how organisms affected human livelihoods. It has subdivided into three important sub-fields – pest management, wildlife management, and fisheries management. Applied ecology relies heavily on the principles of population ecology, one level above the individual studies of behavioural and natural history research. These fields are concerned with population changes, whether to reduce populations to stop damage to crops, or to understand why some species populations become pests. All applied ecology heavily interreacts with human usage of the environment and the economics of farming, fisheries, and wildlife harvesting. In a general sense applied ecology is a step more difficult than behavioural ecology because answering the applied problems or management has a longer time frame than the typical three-year thesis project. Applied ecology has a broad interface with evolutionary ecology because human actions can disrupt natural selection and pest evolution can complicate every management problem.

Conservation ecology is the new kid on the block. It was part of wildlife and fisheries management until about 1985 when it was clear to all that some populations were endangered by human changes to the ecosystems of fisheries, forestry, and agriculture. The essential problems of conservation ecology were described elegantly by Caughley (1994). Conservation issues are the most visible of all issues in population and community ecology, and they are often the most difficult to resolve when science dictates one conservation solution that interferes with the dominant economic view of human society. If species of interest are rare the problem is further confounded by the difficulty of studying rare species in the field. What will become of the earth’s ecosystems in the future depends in large part as to how these conservation conflicts can be resolved.

Ecosystem ecology and community ecology are the important focus at present but are hampered by a lack of a clear vision of what needs to be done and what can be done. The problem is partly that there is much poor theory, coupled with much poor data. The critical questions in ecosystem ecology are currently too vague to be studied in a realistic time period of less than 50 years. Climate change is impacting all our current ideas about community stability and resilience, and what predictions we can make for whole ecosystems in the light of a poor database. Ironically experimental manipulations are being done by companies with an economic focus such as forestry but there are few funds to make use of these large-scale landscape changes. In the long term, ecosystem ecology is the most significant aspect of ecology for humans, but it is the weakest in terms of understanding ecosystem processes. We can all see the negative effects of human changes on landscapes, but we have little in the way of scientific guidance to predict the long-term consequences of these changes and how they can be successfully ameliorated.

All of this is distressing to practical ecologists who wish to make a difference and be able to counteract undesirable changes in populations and ecosystems. It is important for all of us not to give up on reversing negative trends in conservation and land management and we need to do all we can to influence the public in general and politicians in particular to change negative trends to positive ones in our world. An array of good books points this out very forcefully (e.g., Monbiot 2018, Klein 2021). It is the job of every ecologist to gather the data and present ecological science to the community at large so we can contribute to decision making about the future of the Earth.

Bartholomew, G. A. (1986). The role of natural history in contemporary biology. BioScience 36, 324-329. doi: 10.2307/1310237

Caughley, G. (1994). Directions in conservation biology. Journal of Animal Ecology 63, 215-244. doi: 10.2307/5542

Davies, N.B., Krebs, J.R., and West, S.A. (2012) ‘An Introduction to Behavioural Ecology.‘ 4th edn. (Wiley-Blackwell: Oxford.). 520 pp.

Dayton, P.K. (2003). The importance of the natural sciences to conservation. American Naturalist 162, 1-13. doi: 10.1086/376572

Klein, Naomi (2021) ‘How to Change Everything: The Young Human’s Guide to Protecting the Planet and Each Other ‘ (Simon and Schuster: New York.) 336 pp. ISBN: 978-1534474529

Monbiot, George. (2018) ‘Out of the Wreckage: A New Politics for an Age of Crisis.’ (Verso.). 224 pp. ISBN: 1786632896

What is the Ratio of Thought to Action in Biodiversity Conservation?

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Many ecologists who peruse the conservation literature will come away with a general concern about the amount of effort that goes into thoughts about how conservation should be done and how much action is currently being carried out to achieve these goals in the field. My premise here is that currently the person-power given to thought greatly exceeds the person-power devoted to actually achieving the broad conservation goal of protecting biodiversity. Let me illustrate this with one dilemma in conservation: should we be concerned predominately with the loss of threatened and endangered species, or should we concentrate on the major dominant species in our ecosystems? Of course, this is not a black-or-white dichotomy, and the first answer is that we should do both. But the economist would suggest that resources are limited, and you cannot do both, so the question should be reworded as to what fraction of resources should go to one or the other of these two activities.

Consider the example of threatened and endangered species. Many of these species are rare numerically at present. In the past they may have been abundant but that is not always the case. The ecologist will know as a universal constant that most species in ecosystems are rare, and because they are rare, they are most difficult to study to answer the simple question why are they rare? Pick your favourite rare species and try to answer this question. For some species under persecution by humans the answer is simple; for most it is not, and ecologists fall back on explanations like the resources they require are not abundant, or their niche is specialized, meaningless statements that can be called panchrestons unless we have infinite time and funds to find out exactly what the limiting resources are, or why their niche is specialized. Now let us make a simple thought experiment that asks: what would happen if all these rare and endangered species disappeared from the world’s ecosystems? The first response would be total outrage that anyone would ask such a terrible question, so it is best not to talk about it. The second would be that we would be outraged if our favorite bird or frog disappeared like the passenger pigeon. The third might be that we should consider this question seriously.

Some community and ecosystem ecologists might wager that nothing would happen to ecosystem dynamics if all the rare and endangered species disappeared. No one of course would admit to such a point of view since it would end their career. At the moment we are in the unenviable state of doing the opposite experiment on the world’s coral reefs which are suffering in an ocean that is acidifying and heating up, pollution that is increasing, and overfishing that is common (Fraser et al. 2019, Lebrec et al. 2019, Romero-Torres et al. 2020). Coral reefs are an extreme example of human impacts on areas of high conservation and economic value such that the entire ecosystem will have to reconstruct itself with corals of greater tolerance to current and future conditions, a future with no clear guess of what positive effects will transpire.

Perhaps the message of both coral reef conservation and terrestrial ecosystem conservation is that you cannot destroy the major species without major consequences. Australia provides a good example of the consequences of altering predator abundance in an ecosystem. The dingo (Canis familaris) has been persecuted because of predation on sheep, and at the same time domestic cats (Felis catus) and red foxes (Vulpes vulpes) have been introduced to the continent. The ecological question is whether the reintroduction of the dingo to places where it has been exterminated will reduce the abundance of cats and foxes, and thus save naïve prey species from local extinction (Newsome et al. 2015). The answer to this question is far from clear (Morgan et al. 2017, Hunter and Letnic 2022) and may differ in different ecosystems within Australia.  

The bottom line is that our original question about rare species cannot be answered. There is much literature on introduced predators affecting food webs, following from Estes et al. (2011) important paper. and now there is much research effort on the roles of apex predators and consumers on ecosystem dynamics (Serrouya et al. 2021). Much of this effort concentrates on the common animals rather than the rare ones with which we began this discussion. Much more action in the field is needed on all conservation fronts since in my opinion the amount of thought we have available now will last field workers for the rest of the century.

Estes, J.A., Terborgh, J., Brashares, J.S., Power, M.E., Berger, J., et al. (2011). Trophic downgrading of Planet Earth. Science 333, 301-306. doi: 10.1126/science.1205106.

Fraser, K.A., Adams, V.M., Pressey, R.L., and Pandolfi, J.M. (2019). Impact evaluation and conservation outcomes in marine protected areas: A case study of the Great Barrier Reef Marine Park. Biological Conservation 238, 108185. doi: 10.1016/j.biocon.2019.07.030

Hunter, D.O. and Letnic, M. (2022). Dingoes have greater suppressive effect on fox populations than poisoning campaigns. Australian Mammalogy 44. doi: 10.1071/AM21036.

Lebrec, M., Stefanski, S., Gates, R., Acar, S., Golbuu, Y., Claudel-Rusin, A., Kurihara, H., Rehdanz, K., Paugam-Baudoin, D., Tsunoda, T., and Swarzenski, P.W. (2019). Ocean acidification impacts in select Pacific Basin coral reef ecosystems. Regional Studies in Marine Science 28, 100584. doi: 10.1016/j.rsma.2019.100584.

Morgan, H.R., Hunter, J.T., Ballard, G., Reid, N.C.H., and Fleming, P.J.S. (2017). Trophic cascades and dingoes in Australia: Does the Yellowstone wolf–elk–willow model apply? Food Webs 12, 76-87. doi: 10.1016/j.fooweb.2016.09.003.

Newsome, TM., Ballard, G.-A., Crowther, M.S., Dellinger, J.A., Fleming, P.J.S., et al. (2015). Resolving the value of the dingo in ecological restoration. Restoration Ecology 23, 201-208.  doi: 10.1111/rec.12186.

Romero-Torres, M., Acosta, A., Palacio-Castro, A.M., Treml, E.A., Zapata, F.A., Paz-García, D.A., and Porter, J.W. (2020). Coral reef resilience to thermal stress in the Eastern Tropical Pacific. Global Change Biology 26, 3880-3890. doi: 10.1111/gcb.15126

Serrouya, R., Dickie, M., Lamb, C., Oort, H. van, Kelly, A.P., DeMars, C., et al. (2021). Trophic consequences of terrestrial eutrophication for a threatened ungulate. Proceedings of the Royal Society B: Biological Sciences 288, 20202811. doi: 10.1098/rspb.2020.2811.

How Do We Decide Controversial Issues in Conservation?

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While almost everyone favours conservation of plants and animals around the globe, it is far from clear how this broad goal can be disarticulated into smaller issues. Once we have done this the solution of the conservation problem should be simple. But it is not (Sutherland et al, 2021). Take an example of the koala in Australia, cute mid-size marsupials that live in trees and eat leaves. If koalas are to be protected, you must protect forests, but if you protect forests the companies that survive by logging on both private and crown land will be adversely affected. We have an immediate conflict, so how do we decide what to do. One response which we can label have-your-cake-and-eat-it-too suggests that we use some of our forests for logging and protect some forests for ecological reserves. Everyone is now happy, but things unravel. As the human population grows, we need more wood, so over time we would have to log more and more of the forested areas that could support koalas. Conflict now, jobs for loggers vs. conservation of koalas. The simplest solution is to decide all this in economic terms. Logging produces much money; conservation is largely a drain on the taxpayers. To propose that conservation should win, ecologists will pull out David Attenborough to show all the beauties of the forest and to point out that the forest contains many other animals and plants and not just trees for lumber. Stalemate, and social and economic goals begin to override the ecological issue until some compromise is suggested and accepted.

While this kind of oversimplified scenario is common, the whole issue of conservation decision making is fraught with problems and who is going to decide these issues (Christie et al. 2022)? In a democracy in the good old days, you took a vote or a poll and decided to win/lose at >50% of the vote. But this cannot work for critical problems. We have a good example of this problem now with Covid vaccination requirements, and a vocal minority opposed to vaccinations. This now spills over into the issue of whether to wear a face mask or not. In all these kinds of scenarios science delivers a simple decision about the consequences of decision A vs decision B, but the problem is that society can refuse to recognize the scientific results or just prefer decision B with little visible justification. Science is not always perfect, adding further complications. And in the case of the covid virus, the virus can mutate in unexpected ways, complicating prognoses. In the case of protected conservation areas, we can suffer fires, floods, insect outbreaks and any number of events that affect the balance of decision making.

There is a large literature on decision making in conservation (e.g., Bower et al. 2018) and even good advice from the field of psychology about this problem of making decisions (Papworth 2017). The best systematic decision tree I have found is that in Sutherland et al. 2021). Sutherland et al. (2021) compiled a framework that can be used profitably in deciding on the level of evidence assessment (see Table 1 and Figure 1 below from their paper).

Table 1 and Figure 1 from Sutherland et al. (2021)

The Strategic Evidence Assessment Framework. Seven levels of evidence assessment, how to apply them.

Assessment LevelApproach UsedGeneral Database ApplicationApproximate Time to reflect on the evidence
1 No consideration of evidenceContinue with existing practice or make decisions without considering scientific evidencenone
2 Assertion but no independent consideration of evidenceConsultation with others (including experts) that affect decision but are not verified e.g. “we normally do this”, “accepted best practice is to do this”minutes
3Papers reviewed, looking at: Read the title and/or summary points to determine whether action described in the paper is likely to be effective or not. Review effectiveness category e.g. “likely to be beneficial” on action page to decide whether action is likely to be effective or notminutes
4 Read abstract to assess the evidence described in the paper in relation to the local problemTens of minutes- hours
5  Read abstract, key results and conclusion assessing each paper in relation to the decision being madeHours
6 Read the full underlying paper/s. This is likely to affect decisions on study quality, relevance and modificationsHours to days
7Comprehensive assessmentA systematic review of all available literature. Assessed papers summarised as part of new reviewMonths to a year

Figure 1. A framework for considering the appropriate level of effort in decision making. Numbers refer to assessment level (Table 1). For a given decision about an action identify the column with the relevant level of consequence, start at the lowest level (1) and decide whether it would benefit from examining higher levels of evidence. Keep moving up until either the uncertainty in the effectiveness of the action is resolved from examining the evidence (from any platform) or the arrows end. This final number is the level at which the evidence assessment should occur. (From Sutherland et al. 2021 with permission).

Clearly conservation ecologists cannot use the highest assessment level for all issues that arise and must result to triage in many cases (Hayward and Castley 2018). But triage and assessment levels 1 and 2 should be rare in making judgement on what program to adopt. We need to get the science right for all conservation problems.

But this is not enough to get thoughtful political decisions. Some native species can be pests, yet nothing is done to reduce their damage (e.g. horses in North America and Australia, camels and goats in Australia, feral pigs in North America) and the list goes on. Nothing is done because of budget limitations or political concerns about “cute species”. The science of conservation is difficult enough, the social science of conservation is too often out of our control.

Bower, S.D., Brownscombe, J.W., Birnie-Gauvin, K. Ford, M.I. et al. (2018). Making Tough Choices: Picking the appropriate conservation decision-making tool. Conservation Letters 11, e12418. doi: 10.1111/conl.12418.

Christie, A.P., Downey, H., Bretagnolle, V., Brick, C., Bulman, C.R., et al. (2022). Principles for the production of evidence-based guidance for conservation actions. Conservation Science and Practice 4, e579. doi: 10.1111/csp2.12663.

Hayward, M.W. and Castley, J.G. (2018). Triage in Conservation. Frontiers in Ecology and Evolution 5, 168. doi: 10.3389/fevo.2017.00168.

Papworth, Sarah (2017). Decision-making psychology can bolster conservation. Nature Ecology & Evolution 1, 1217-1218. doi: 10.1038/s41559-017-0281-9.

Sutherland, W.J., Downey, H., Frick, W.F., Tinsley-Marshall, P., and McPherson, T. (2021). Planning practical evidence-based decision making in conservation within time constraints: the Strategic Evidence Assessment Framework. Journal for Nature Conservation 60, 125975. doi: 10.1016/j.jnc.2021.125975.

On Rewilding and Conservation

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Rewilding is the latest rage in conservation biology, and it is useful to have a discussion of how it might work and what might go wrong. I am reminded of a comment made many years ago by Buzz Holling at UBC in which he said, “do not take any action that cannot be undone”. The examples are classic – do not introduce rabbits to Australia if you can not reverse the process, do not introduce weasels and stoats to New Zealand if you cannot remove them later if they become pests, do not introduce cheatgrass to western USA grasslands and allow it to become an extremely invasive species. There are too many examples that you can find for every country on Earth. But now we approach the converse problem of re-introducing animals and plants that have gone extinct back into their original geographic range, the original notion of rewilding (Schulte to Bühne et al. 2022).

The first question could be to determine what ‘rewilding’ means, since it is a concept used in so many ways. As a general concept it can be thought of as repairing the Earth from the ravages imposed by humans over the last thousands of years. It appeals to our general belief that things were better in the ‘good old days’ with respect to conservation, and that all we have seen are losses of iconic species and the introduction of pests to new locations. But we need to approach rewilding with the principle that “the devil is in the details”, and the problems are triply difficult because they must engage support from ecologists over the science and the public over policies that affect different social groups like farmers and hunters. Rewilding may range from initiatives that range from “full rewilding” to ‘minimal rewilding’ (Pedersen et al. 2020). Rewilding has been focused to a large extent on large-bodied animals and particularly those species of herbivores and predators that are high in the food chain, typified by the reintroduction of wood bison back into the Yukon after they went extinct about 800 years ago (Boonstra et al. 2018). So the first problem is that the term “rewilding” can mean many different things.

Two major issues must be considered by conservation ecologists before a rewilding project is initiated. First, there should be a comprehensive understanding of the food web of the ecosystem that is to be changed. This is a non-trivial matter in that our understanding of the food webs of what we describe as our best-known ecosystems are woefully incomplete. At best we can do a boxes and arrows diagram without understanding the strength of the connections and the essential nature of many of the known linkages. The second major issue is how rewilding will deal with climate change (Bakker and Svenning, 2018). There is now an extensive literature on paleoecology, particularly in Europe and North America. The changes in climate and species distributions that flowed from the retreat of the glaciers some 10,000 years ago are documented as a reminder to all ecologists that ecosystems and communities are not permanent in time. Rewilding at the present has a time frame with less than necessary thought to future changes in climate. We make the gigantic assumption that we can recreate an ecosystem that existed sometime in the past, and without being very specific about how we might measure success or failure in restoring ecological integrity. 

Pedersen et al. (2020) recognize 5 levels of rewilding of which the simplest is called “minimal rewilding” and the measure of success at this level is the “Potential of animal species to advance self-regulating biodiverse ecosystems” which I suggest to you is an impossible task to achieve in any feasible time frame less than 50-100 years, which is exactly the time scale the IPCC suggests for maximum climatic emergencies. We do not know what a ‘biodiverse ecosystem’ is since we do not know the boundaries of ecosystems under climate change, and we cannot measure what “natural population dynamics” is because we have so few long-term studies. Finally, at the best level for rewilding we cannot measure “natural species interaction networks” without much arm waving.

Where does this leave the empirical conservation ecologist (Hayward et al. 2019)? Rewilding appears to be more a public relations science than an empirical one. Conservation issues are immediate, and a full effort is needed to protect species and diagnose conservation problems of the day. Goshawks are declining in a large part of the boreal forest of North America, and no one knows exactly why. Caribou are a conservation issue of the first order in Canada, and they continue to decline despite good ecological understanding of the causes. The remedy of some conservation dilemmas like the caribou are clear, but the political and economic forces deny their implementation. As conservation biologists we are ever limited by public and governmental policies that favour exploitation of the land and jobs and money as the only things that matter. Simple rewilding on a small scale may be useful, but the losses we face are a whole Earth issue, and we need to address these more with traditional conservation actions and an increase in research to find out why many elements in our natural communities are declining with little or no understanding of the cause.

Bakker, E.S. and Svenning, J.-C. (2018). Trophic rewilding: impact on ecosystems under global change. Philosophical Transaction of the Royal Society B 373, 20170432. doi: 10.1098/rstb.2017.0432.

Boonstra, R., et al. (2018). Impact of rewilding, species introductions and climate change on the structure and function of the Yukon boreal forest ecosystem. Integrative Zoology 13, 123-138. doi: 10.1111/1749-4877.12288.

Hayward, M.W., et al. (2019). Reintroducing rewilding to restoration – Rejecting the search for novelty. Biological Conservation 233, 255-259. doi: 10.1016/j.biocon.2019.03.011.

Pedersen, P.B.M., Ejrnæs, R., Sandel, B., and Svenning, J.-C. (2020). Trophic rewilding advancement in Anthropogenically Impacted Landscapes (TRAAIL): A framework to link conventional conservation management and rewilding. Ambio 49, 231-244. doi: 10.1007/s13280-019-01192-z.

Schulte to Bühne, H., Pettorelli, N., and Hoffmann, M. (2022). The policy consequences of defining rewilding. Ambio 51, 93-102. doi: 10.1007/s13280-021-01560-8.

On Administration and Scientific Progress

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After talking and listening to my colleagues and friends who are still employed, I have the urge to try to quantify the utility of administrative meetings to scientific progress. I begin with a very simple model of what this relationship might look like.

The Neutral Model suggests that scientific progress is independent from the number of meetings that are focused on the scientific problem at hand. This is most likely the preferred model of administrators. The Optimistic Model suggests that scientific progress is positively related to the number of administrative meetings, possibly because the coordination among the members of the scientific team is enhanced. The Pessimistic Model suggests that the reverse is true, and if you as a scientific director wish to slow the progress of your scientific team, you should schedule many meetings all the time, presumably with a long agenda.

It is far from clear which model is appropriate for an ecological scientific team and more research is needed on this topic. Many scientists struggling with measurements and data collection are possibly attracted to the Pessimistic Model because time is the limiting element in their lives and both data and results are what limit progress. On the other hand, scientific administrators are possibly drawn to the Optimistic Model if they believe that meetings are the most important point of scientific progress and time is not the limiting factor, or perhaps they are drawn to the Neutral Model if they assume their scientists will work diligently and achieve the same goals no matter how many meetings are scheduled.

I hesitate to present this model given that the underlying mathematics are relatively simple, plus there are probably more business textbooks that make a detailed analysis of this issue than there are words in this blog. In a more realistic framework, we may have a peaked curve that indicate many meetings early in a project and fewer meetings once things are moving forward smoothly. There is going to be no magic numbers here, and the only purpose of this brief discussion is to think about how much you need to meet to define and deliver a set of objectives for a scientific question.

All my speculations above arose from an old paper (Moss 1978) illustrating these same general principles. Parkinson (1958) framed the law that “Work Expands To Fill The Time Available For Its Completion” and showed one consequence of this was that the fraction of administrators within a public organisation tends to increase irrespective of the amount of external scientific work done by that organisation. Moss (1978) produced these data to illustrate this law for British science data from 1976-77, illustrated in this graph:

Moss (1980) further elaborated on how Parkinson’s Law applied to scientific research organizations and noted that it may apply to many other research organizations. Although it is an old ‘law’ it may still be worth some discussion and consideration today.

Moss, R. (1978). An empirical test of Parkinson’s Law. Nature 273, 184. doi: 10.1038/273184a0.

Moss, R. (1980). Expanding on Parkinson’s Law. Nature 285, 9. doi: 10.1038/285009a0.

On How Genomics will not solve Ecological Problems

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I am responding to this statement in an article in the Conversation by Anne Murgai on April 19, 2022 (https://phys.org/news/2022-04-african-scientists-genes-species.html#google_vignette) : The opening sentence of her article on genomics encapsulates one of the problems of conservation biology today:

“DNA is the blueprint of life. All the information that an organism needs to survive, reproduce, adapt to environments or survive a disease is in its DNA. That is why genomics is so important.”

If this is literally correct, almost all of ecological science should disappear, and our efforts to analyse changes in geographic distributions, abundance, survival and reproductive rates, competition with other organisms, wildlife diseases, conservation of rare species and all things that we discuss in our ecology journals are epiphenomena, and thus our slow progress in sorting out these ecological issues is solely because we have not yet sequenced all our species to find the answers to everything in their DNA.

This is of course not correct, and the statement quoted above is a great exaggeration. But, if it is believed to be correct, it has some important consequences for scientific funding. I will confine my remarks to the fields of conservation and ecology. The first and most important is that belief in this view of genetic determinism is having large effects on where conservation funding is going. Genomics has been a rising star in biological science for the past 2 decades because of technological advances in sequencing DNA. As such, given a fixed budget, it is taking money away from the more traditional approaches to conservation such as setting up protected areas and understanding the demography of declining populations. Hausdorf (2021) explores these conflicting problems in an excellent review, and he concludes that often more cost-effective methods of conservation should be prioritized over genomic analyses. Examples abound of conservation problems that are immediate and typically underfunded (e.g., Turner et al. 2021, Silva et al, 2021).   

What is the resolution of these issues? I can recommend only that those in charge of dispensing funding for conservation science examine the hypotheses being tested and avoid endless funding for descriptive genomics that claim to have a potential and immediate outcome that will forward the main objectives of conservation. Certainly, some genomic projects will fit into this desirable science category, but many will not, and the money should be directed elsewhere.  

The Genomics Paradigm listed above is used in the literature on medicine and social science, and a good critique of this view from a human perspective is given in a review by Feldman and Riskin (2022). Scientists dealing with human breast cancer or schizophrenia show the partial but limited importance of DNA in determining the cause or onset of these complex conditions (e.g., Hilker et al 2018, Manobharathi et al. 2021). Conservation problems are equally complex, and in the climate emergency have a short time frame for action. I suspect that genomics for all its strengths will have only a minor part to play in the resolution of ecological problems and conservation crises in the coming years.

Feldman, Marcus W. and Riskin, Jessica (2022). Why Biology is not Destiny. The New York Review of Books 69 (April 21, 2022), 43-46.

Hausdorf, Bernhard (2021). A holistic perspective on species conservation. Biological Conservation 264, 109375. doi: 10.1016/j.biocon.2021.109375.

Hilker, R., Helenius, D., Fagerlund, B., Skytthe, A., Christensen, K., Werge, T.M., Nordentoft, M., and Glenthøj, B. (2018). Heritability of Schizophrenia and Schizophrenia Spectrum based on the Nationwide Danish Twin Register. Biological Psychiatry 83, 492-498. doi: 10.1016/j.biopsych.2017.08.017.

Manobharathi, V., Kalaiyarasi, D., and Mirunalini, S. (2021). A concise critique on breast cancer: A historical and scientific perspective. Research Journal of Biotechnology 16, 220-230.

Samuel, G. N. and Farsides, B. (2018). Public trust and ‘ethics review’ as a commodity: the case of Genomics England Limited and the UK’s 100,000 genomes project. Medicine, Health Care, and Philosophy 21, 159-168. doi: 10.1007/s11019-017-9810-1.

Silva, F., Kalapothakis, E., Silva, L., and Pelicice, F. (2021). The sum of multiple human stressors and weak management as a threat for migratory fish. Biological Conservation 264, 109392. doi: 10.1016/j.biocon.2021.109392.

Turner, A., Wassens, S., and Heard, G. (2021). Chytrid infection dynamics in frog populations from climatically disparate regions. Biological Conservation 264, 109391. doi: 10.1016/j.biocon.2021.109391.

On Assumptions in Ecology Papers

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What can we do as ecologists to improve the publishing standards of ecology papers? I suggest one simple but bold request. We should require at the end of every published paper a annotated list of the assumptions made in providing the analysis reported in the paper. A tabular format could be devised with columns for the assumption, the perceived support of and tests for the assumption, and references for this support or lack thereof. I can hear the screaming already, so this table could be put in the Supplementary Material which most people do not read. We could add to each paper in the final material where there are statements of who did the writing, who provided the money, and add a reference to this assumptions table in the Supplementary Material or a statement that no assumptions about anything were made to reach these conclusions.

The first response I can detect to this recommendation is that many ecologists will differ in what they state are assumptions to their analysis and conclusions. As an example, in wildlife studies, we commonly make the assumption that an individual animal having a radio collar will behave and survive just like another animal with no collar. In analyses of avian population dynamics, we might commonly assume that our visiting nests does not affect their survival probability. We make many such assumptions about random or non-random sampling. My question then is whether or not there is any value in listing these kinds of assumptions. My response is that this approach of listing what the authors think they are assuming should alert the reviewers to the elephants in the room that have not been listed.

My attention was called to this general issue by the recent paper of Ginzburg and Damuth (2022) in which they contrasted the assumptions of two general theories of functional responses of predators to prey – “prey dependence” versus “ratio dependence”. We have in ecology many such either-or discussions that never seem to end. Consider the long-standing discussion of whether populations can be regulated by factors that are “density dependent” or “density independent”, a much-debated issue that is still with us even though it was incisively analyzed many years ago.  

Experimental ecology is not exempt from assumptions, as outlined in Kimmel et al. (2021) who provide an incisive review of cause and effect in ecological experiments. Pringle and Hutchinson (2020) discuss the failure of assumptions in food web analysis and how these might be resolved with new techniques of analysis. Drake et al. (2021) consider the role of connectivity in arriving at conservation evaluations of patch dynamics, and the importance of demographic contributions to connectivity via dispersal. The key point is that, as ecology progresses, the role of assumptions must be continually questioned in relation to our conclusions about population and community dynamics in relation to conservation and landscape management.

Long ago Peters (1991) wrote an extended critique of how ecology should operate to avoid some of these issues, but his 1991 book is not easily available to students (currently available on Amazon for about $90). To encourage more discussion of these questions from the older to the more current literature, I have copied Peters Chapter 4 to the bottom of my web page at https://www.zoology.ubc.ca/~krebs/books.html for students to download if they wish to discuss these issues in more detail.

Perhaps a possible message in all this has been that ecology has always wished to be “physics-in-miniature” with grand generalizations like the laws we teach in the physical sciences. Over the last 60 years the battle in the ecology literature has been between this model of physics and the view that every population and community differ, and everything is continuing to change under the climate emergency so that we can have little general theory in ecology. There are certainly many current generalizations, but they are relatively useless for a transition from the general to the particular for the development of a predictive science. The consequence is that we now bounce from individual study to individual study, typically starting from different assumptions, with very limited predictability that is empirically testable. And the central issue for ecological science is how can we move from the present fragmentation in our knowledge to a more unified science. Perhaps starting to examine the assumptions of our current publications would be a start in this direction.  

Drake, J., Lambin, X., and Sutherland, C. (2021). The value of considering demographic contributions to connectivity: a review. Ecography 44, 1-18. doi: 10.1111/ecog.05552.

Ginzburg, L.R. and Damuth, J. (2022). The Issue Isn’t Which Model of Consumer Interference Is Right, but Which One Is Least Wrong. Frontiers in Ecology and Evolution 10, 860542. doi: 10.3389/fevo.2022.860542.

Kimmel, K., Dee, L.E., Avolio, M.L., and Ferraro, P.J. (2021). Causal assumptions and causal inference in ecological experiments. Trends in Ecology & Evolution 36, 1141-1152. doi: 10.1016/j.tree.2021.08.008.

Peters, R.H. (1991) ‘A Critique for Ecology.’ (Cambridge University Press: Cambridge, England.) ISBN:0521400171 (Chapter 4 pdf available at https://www.zoology.ubc.ca/~krebs/books.html)

Pringle, R.M. and Hutchinson, M.C. (2020). Resolving Food-Web Structure. Annual Review of Ecology, Evolution, and Systematics 51, 55-80. doi: 10.1146/annurev-ecolsys-110218-024908.

On Replication in Ecology

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All statistics books recommend replication in scientific studies. I suggest that this recommendation has been carried to extreme in current ecological studies. In approximately 50% of ecological papers I read in our best journals (a biased sample to be sure) the results of the study are not new and have been replicated many times in the past, often in papers not cited in ‘new’ papers. There is no harm in this happening, but it does not lead to progress in our understanding of populations, communities or ecosystems or lead to new ecological theory. We do need replication examining the major ideas in ecology, and this is good. On the other hand, we do not need more and more studies of what we might call ecological truths. An analogy would be to test in 2022 the Flat Earth Hypothesis to examine its predictions. It is time to move on.

There is an extensive literature on hypothesis testing which can be crudely summarized by “Observations of X” which can be explained by hypothesis A, B, or C each of which have unique predictions associated with them. A series of experiments are carried out to test these predictions and the most strongly supported hypothesis, call it B*, is accepted as current knowledge. Explanation B* is useful scientifically only if it leads to a new set of predictions D, E, and F which are then tested. This chain of explanation is never simple. There can be much disagreement which may mean sharpening the hypotheses following from Explanation B*. At the same time there will be some scientists who despite all the accumulated data still accept the Flat Earth Hypothesis. If you think this is nonsense, you have not been reading the news about the Covid epidemic.

Further complications arise from two streams of thought. The first is that the way forward is via simple mathematical models to represent the system. There is much literature on modelling in ecology which is most useful when it is based on good field data, but for too many ecological problems the model is believed more than the data, and the assumptions of the models are not stated or tested. If you think that models lead directly to progress, examine again the Covid modelling situation in the past 2 years. The second stream of thought that complicates ecological science is that of descriptive ecology. Many of the papers in the current literature describe a current set of data or events with no hypothesis in mind. The major offenders are the biodiversity scientists and the ‘measure everything’ scientists. The basis of this approach seems to be that all our data will be of major use in 50, 100 or whatever years, so we must collect major archives of ecological data. Biodiversity is the bandwagon of the present time, and it is a most useful endeavour to classify and categorise species. As such it leads to much natural history that is interesting and important for many non-scientists. And almost everyone would agree that we should protect biodiversity. But while biodiversity studies are a necessary background to ecological studies, they do not lead to progress in the scientific understanding of the ecosphere.

Conservation biology is closely associated with biodiversity science, but it suffers even more from the problems outlined above. Conservation is important for everyone, but the current cascade of papers in conservation biology are too often of little use. We do not need opinion pieces; we need clear thinking and concrete data to solve conservation issues. This is not easy since once a species is endangered there are typically too few of them to study properly. And like the rest of ecological science, funding is so poor that reliable data cannot be achieved, and we are left with more unvalidated indices or opinions on species changes. Climate change puts an enormous kink in any conservation recommendations, but on the other hand serves as a panchrestron, a universal explanation for every possible change that occurs in ecosystems and thus can be used to justify every research agenda, good or poor with spurious correlations.

We could advance our ecological understanding more rapidly by demanding a coherent theoretical framework for all proposed programs of research. Grace (2019) argues that plant ecology has made much progress during the last 80 years, in contrast to the less positive overview of Peters (1991) or my observations outlined above. Prosser (2020) provides a critique for microbial ecology that echoes what Peters argued in 1991. All these divergences of opinion would be worthy of a graduate seminar discussion.

If you think all my observations are nonsense, then you should read the perceptive book by Peters (1991) written 30 years ago on the state of ecological science as well as the insightful evaluation of this book by Grace (2019) and the excellent overview of these questions in Currie (2019).  I suggest that many of the issues Peters (1991) raised are with us in 2022, and his general conclusion that ecology is a weak science rather than a strong one still stands. We should celebrate the increases in ecological understanding that have been achieved, but we could advance the science more rapidly by demanding more rigor in what we publish.

Currie, D.J. (2019). Where Newton might have taken ecology. Global Ecology and Biogeography 28, 18-27. doi: 10.1111/geb.12842.

Grace, John (2019). Has ecology grown up? Plant Ecology & Diversity 12, 387-405. doi: 10.1080/17550874.2019.1638464.

Peters, R.H. (1991) ‘A Critique for Ecology.’ (Cambridge University Press: Cambridge, England.). 366 pages. ISBN: 0521400171

Prosser, J.I. (2020). Putting science back into microbial ecology: a question of approach. Philosophical Transactions of the Royal Society. Biological sciences 375, 20190240. doi: 10.1098/rstb.2019.0240.

On the Canadian Biodiversity Observation Network (CAN BON)

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I have been reading the report of an exploratory workshop from July 2021 on designing a biodiversity monitoring network across Canada to address priority monitoring gaps and engage Indigenous people across Canada. The 34 pages of their workshop report can be accessed here, and I recommend you might read it before reading my comments on the report:

https://www.nserc-crsng.gc.ca/Media-Media/NewsDetail-DetailNouvelles_eng.asp?ID=1310

I have a few comments on this report that are my opinion only. I think the Report on this workshop outlines a plan so grand and misguided that it could not be achieved in this century, even with a military budget. The report is a statement of wisdom put together with platitudes. Why is this and what are the details that I believe to be unachievable?

The major goal of the proposed network is to bring together everyone to improve biodiversity monitoring and address the highest priority gaps to support biodiversity conservation. I think most of the people of Canada would support these objectives, but what does it mean? Let us do a thought experiment. Suppose at this instant in time we knew the distribution and the exact abundance of every species in Canada. What would we know, what could we manage, what good would all these data be except as a list taking up terabytes of data? If we had these data for several years and the numbers or biomass were changing, what could we do? Is all well in our ecosystems or not? What are we trying to maximize when we have no idea of the mechanisms of change? Contrast these concerns about biodiversity with the energy and resources applied in medicine to the mortality of humans infected with Covid viruses in the last 3 years. A monumental effort to examine the mechanisms of infection and ways of preventing illness, with a clear goal and clear measures of progress toward that goal.

There is no difficulty in putting out “dream” reports, and biologists as well as physicists and astronomers, and social scientists have been doing this for years. But in my opinion this report is a dream too far and I give you a few reasons why.

First, we have no clear definition of biodiversity except that it includes everything living, so if we are going to monitor biodiversity what exactly should we do? For some of us monitoring caribou and wolves would be a sufficient program, or whales in the arctic, or plant species in peat bogs. So, to begin with we have to say what operationally we would define as the biodiversity we wish to monitor. We could put all our energy into a single group of species like birds and claim that these are the signal species to monitor for ecosystem integrity. Or should we consider only the COSEWIC list of Threatened or Endangered Species in Canada as our major monitoring concern? So, the first job of CAN BON must be to make a list of what the observation network is supposed to observe (Lindenmayer 2018). There is absolutely no agreement on that simple question within Canada now, and without it we cannot move forward to make an effective network.

The second issue that I take with the existing report is that the emphasis is on observations, and then the question is what problems will be solved by observation alone. The advance of ecological science has been based on observation and experiment directed to specific questions either of ecological interest or of economic interest. In the Pacific salmon fishery for example the objective of observation is to predict escapement and thus allowable harvest quotas. Despite years of high-quality observations and experiments, we are still a long way from understanding the ecosystem dynamics that drive Pacific salmon reproduction and survival.

Contrast the salmon problem with the caribou problem. We have a reasonably good understanding of why caribou populations are declining or not, based on many studies of predator-prey dynamics, harvesting, and habitat management. At present the southern populations of caribou are disappearing because of a loss of habitat because of land use for forestry and mining, and the interacting nexus of factors is well understood. What we do not do as a society is put these ideas into practice for conservation; for example, forestry must have priority over land use for economic reasons and the caribou populations at risk suffer. Once ecological knowledge is well defined, it does not lead automatically to action that biodiversity scientists would like. Climate change is the elephant in the room for many of our ecological problems but it is simultaneously easy to blame and yet uneven in its effects.

The third problem is funding, and this overwhelms the objectives of the Network. Ecological funding in general in Canada is a disgrace, yet we achieve much with little money. If this ever changes it will require major public input and changed governmental objectives, neither is under our immediate control. One way to press this objective forward is to produce a list of the most serious biodiversity problems facing Canada now along with suggestions for their resolution. There is no simple way to develop this list. A by-product of the current funding system in Canada is the shelling out of peanuts in funding to a wide range of investigators whose main job becomes how to jockey for the limited funds by overpromising results. Coordination is rare partly because funding is low. So (for example) I can work only on the tree ecology of the boreal forest because I am not able to expand my studies to include the shrubs, the ground vegetation, the herbivores, and the insect pests, not to mention the moose and the caribou.  

For these reasons and many more that could be addressed from the CAN BON report, I would suggest that to proceed further here is a plan:

  1. Make a list of the 10 or 15 most important questions for biodiversity science in Canada. This alone would be a major achievement.
  2. Establish subgroups organized around each of these questions who can then self-organize to discuss plans for observations and experiments designed to answer the question. Vague objectives are not sufficient. An established measure of progress is essential.
  3. Request a realistic budget and a time frame for achieving these goals from each group.  Find out what the physicists, astronomers, and medical programs deem to be suitable budgets for achieving their goals.
  4. Organize a second CAN BON conference of a small number of scientists to discuss these specific proposals. Any subgroup can participate at this level, but some decisions must be made for the overall objectives of biodiversity conservation in Canada.

These general ideas are not particularly new (Likens 1989, Lindenmayer et al. 2018). They have evolved from the setting up of the LTER Program in the USA (Hobbie 2003), and they are standard operating procedures for astronomers who need to come together with big ideas asking for big money. None of this will be easy to achieve for biodiversity conservation because it requires the wisdom of Solomon and the determination of Vladimir Putin.

Hobbie, J.E., Carpenter, S.R., Grimm, N.B., Gosz, J.R., and Seastedt, T.R. (2003). The US Long Term Ecological Research Program. BioScience 53, 21-32. doi: 10.1016/j.oneear.2021.12.008

Likens, G. E. (Ed.) (1989). ‘Long-term Studies in Ecology: Approaches and Alternatives.’ (Springer Verlag: New York.) ISBN: 0387967435

Lindenmayer, D. (2018). Why is long-term ecological research and monitoring so hard to do? (And what can be done about it). Australian Zoologist 39, 576-580. doi: 10.7882/az.2017.018.

Lindenmayer, D.B., Likens, G.E., and Franklin, J.F. (2018). Earth Observation Networks (EONs): Finding the Right Balance. Trends in Ecology & Evolution 33, 1-3. doi: 10.1016/j.tree.2017.10.008.