Category Archives: Conservation Biology

On Ecological Climate Change Research

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The media world is awash in climate change articles and warnings. When your town is faced with the fourth one-in-100-year-flood or your favourite highway has been washed away, you should perhaps become aware that something is changing rapidly. Ecologists are aware of the problems that climate change is producing, and the question I want to raise here is what kind of research is needed to outline current and future problems and suggest possible solutions. This fact of current climate change means that each of us has something important to do at the individual level to reduce the impacts of climate change, like taking the bus or bicycling. But that is another whole set of social issues that I cannot cover here.

The first thing most scientific organizations want to do when faced with a big problem is to have endless meetings about the problem. This unfortunately eats up much money and produces little understanding except that the problem is complicated and multidimensional. Ecological research on climate change must begin with the axiom that climate change is happening rapidly, and that we as ecological scientists can do nothing about this at the level of climate physics. Given this, what are we to do? The first approach we could take is to ignore climate change and carry on with normal research agendas. This works very well for short term problems on the time scale of 20-30 years. Since this is the research lifespan of most ecological scientists, it is not an unreasonable approach. But it does not help solve the earth’s future problems, and this is not a desirable path to take in science.

There are three broad problems that accompany climate change for ecological science. First, geographical ranges of species will shift. We have from paleoecology much information on some of these changes since the last Ice Age. Data from palaeontology is less useful to planning, given that we have enough problems trying to forecast the next 100 years of change. So, we have major ecological question #1 – what limits the geographical distributions of species? This relatively simple question is greatly confounded by human activities. If we send oil and other chemical pollution out onto a coastal coral reef, we should not be surprised if the local distribution of sea life is affected. For ecologists this class of problems of distribution changes caused by human activities is a very important focus of research. If you doubt this, read about Covid viruses. But there is also a large area of research needed to estimate the possible changes in geographic distributions of organisms that are not immediately affected by human activities. How fast will tree species colonize up-slope in mountains around the globe, and how will this affect the bird and mammals that depend on trees or the vegetation types the trees displace? These changes are local and complex, and we can begin by describing them, but to understand the limiting factors involved in changes in geographical distributions is not easy.

Population ecology addresses the second central question of ecology: what causes changes in the abundance of particular species? While we need answers to this simple question for our conservation and management issues, population ecology is an even bigger minefield for research on the effects of climate change. There is no doubt that climate in general can affect the abundance and changes in abundance of organisms, but the complications lie in determining the detailed mechanisms of explaining these changes in abundance. Large scale climate indicators like ENSO sometimes correlate positively with animal population increases, sometimes negatively, and sometimes not at all in different populations (Wan et al. 2022). Consequently, a changing climate may not have a universal effect on biodiversity. This means we must dive into details of how climate affects our specific population, is it via maximum temperatures?, minimum temperatures?, dry season rainfall?, wet season rainfall? etc., and each of these aspects of weather have many subcomponents – March temperatures, April temperatures, etc. and the search for an explanation can thus become infinite. The problem is that the number of possible explanatory variables in weather dwarfs the number of years of observations of our study species (c.f. Ginzburg and Jensen 4004, Loken and Gelman 2017). The result is that some of the strongest papers with conclusions about the impact of climatic change on animals can be in error (Daskalova. Phillimore, and Myers-Smith 2021). The statistical pitfalls have been discussed for many years (e.g., Underwood and Chapman 2003) but are still commonly seen in the ecological literature today.

A third central question is that each population is embedded in a community of other species which may interact so that we must analyse the changes occurring community and ecosystem dynamics. Changes in biological communities and ecosystems are subject to complications arising from climate change and more because of species interactions which are not easy to measure. These difficulties do not mean that we should stop trying to explain population and community changes that might be related to climate change. What it does mean is that we should not jump to strong conclusions without considering all the alternate possible agents that are changing the earth’s biomes. The irony is that the human caused shifts are easy to diagnose but difficult to fix because of economics, while the pure climate caused shifts in ecosystems are difficult to diagnose and to validate the exact mechanisms involved. We need both strong involvement in diagnosing the major ecological problems associated with climate change, but this must be coupled with modesty in our suggested conclusions and explanations. There is much to be done.

Daskalova, Gergana N., Phillimore, Albert B., and Myers-Smith, Isla H. (2021). Accounting for year effects and sampling error in temporal analyses of invertebrate population and biodiversity change: a comment on Seibold et al. 2019. Insect Conservation and Diversity 14, 149-154. doi: 10.1111/icad.12468.

Ginzburg, L. R. and Jensen, C. X. J. (2004). Rules of thumb for judging ecological theories. Trends in Ecology and Evolution 19, 121-126. doi: 10.1016/j.tree.2003.11.004.

Loken, Eric and Gelman, Andrew (2017). Measurement error and the replication crisis. Science 355, 584. doi: 10.1126/science.aal3618.

Underwood, A. J. and Chapman, M. G. (2003). Power, precaution, Type II error and sampling design in assessment of environmental impacts. Journal of Experimental Marine Biology and Ecology 296, 49-70. doi: 10.1016/s0022-0981(03)00304-6.

Wan, Xinru, Holyoak, Marcel, Yan, Chuan, Maho, Yvon Le, Dirzo, Rodolfo, et al. (2022). Broad-scale climate variation drives the dynamics of animal populations: A global multi-taxa analysis. Biological Reviews 97. (in press).

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.

Our World View and Conservation

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Recent events have large implications for conservation science. Behind these events – Covid, climate change, wars – lies a fundamental dichotomy of views about humanity’s place in the world today. At the most basic level there are those who view humans as the end-all-and-be-all of importance so that the remainder of the environment and all other species are far down the list of importance when it comes to decision making. The other view is that humans are the custodians of the Earth and all its ecosystems, so that humans are an important part of our policy decisions but not the only part or even the most important part. Between these extreme views there is not a normal distribution but a strongly bimodal one. We see this very clearly with respect to the climate emergency. If you explain the greenhouse dilemma to anyone, you can see the first reaction is that this does not apply to me, so I can do whatever I want versus the reaction of others that I should do something to reduce this problem now. It is the me-here-and-now view of our lives in contrast to the concern we should have about future generations.

Our hope lies in the expectation that things are improving, strongly in young people, more slowly in older people, and negligibly in our politicians. We must achieve sustainability professed by the Greta Thunberg’s of the world, and yet recognize that the action needed is promised by our policy makers only for 2050 or 2100. There is hope that the captains of industry will move toward sustainability goals, but this will be achieved only by rising public and economic pressure. We are beset by wars that make achieving any sustainability goals more difficult. In Western countries blessed with superabundant wealth we can be easily blinded by promises of the future like electricity from nuclear fusion at little cost, or carbon-capture to remove greenhouse gases from the atmosphere. If things get impossibly bad, we are told we can all go to Mars. Or at least the selected elite can.

Conservation gets lost in this current world, and pleas to set aside 30% or 40% of the Earth for biosphere conservation are rarely even heard about on the evening news. The requests for funds for conservation projects are continually cut when there are more important goals for economic growth. Even research funding through our first-class universities and government laboratories is falling, and I would wager without the data that less than 20% of funding for basic research goes to investigating environmental problems or conservation priorities. In my province in Canada a large section of this year’s budget labelled “Addressing Climate Change” is to be spent on repairing the highways from last year’s floods and trying to restore the large areas affected by fires in the previous dry summer.  

What is the solution to this rather depressing situation? Two things must happen soon. First, we the public must hold the government to account for sustainability. Funding oil companies, building pipelines, building highways through Class A farmland, and waging wars will not bring us closer to having a sustainable earth for our grandchildren. Second, we must encourage private industries and wealthy philanthropists to invest in sustainability research. Conservation cannot ever be achieved without setting aside large, protected areas. The list of species that are in decline around the Earth is growing, yet for the vast number of these we have no clear idea why they are declining or what can be done about it. We need funding for science and action, both in short supply in the world today. And some wisdom thrown in.   

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 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.

More on Old Growth Forests and Conservation

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This is a short blog to alert you to a well written plea for saving old growth forests in British Columbia by Karen Price. Karen works with Dave Daust and Rachel Holt, three of our ecological heroes pushing the provincial government to recognize the value of old growth forests. This problem is world-wide but the scientific data alone will not capture the general public as much as this article might.

https://northernbeat.ca/opinion/old-growth-complexity-in-a-sound-bite/

These ecologists have reported their detailed analysis in a report that you can access through the Sierra Club of BC if you want more information on the struggle here in Canada (https://sierraclub.bc.ca/laststand/ ). At present there is nothing but denial from the government and from the industry that there is a problem – the forestry industry is not overharvesting or if it is, we need the jobs. As one person told me, it is not a problem “because we plant one tree seedling for every thousand-year-old tree that we log”.

So please keep up the pressure on governments around the world. Scientists have pushed a strong agenda on sustainable logging for many years with success now looking possible because ordinary citizens demand a change, understanding that forests are more than wood. We must continue the push for sustainable forestry and old growth forest protection.

Lindenmayer, D.B., Kooyman, R.M., Taylor, C., Ward, M., and Watson, J.E.M. (2020). Recent Australian wildfires made worse by logging and associated forest management. Nature Ecology & Evolution 4, 898-900. doi: 10.1038/s41559-020-1195-5.

Price, Karen, Holt, Rachel F., and Daust, Dave (2021). Conflicting portrayals of remaining old growth: the British Columbia case. Canadian Journal of Forest Research 51, 1-11. doi: 10.1139/cjfr-2020-0453.

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.