Category Archives: Climate Emergency

On Ignoring Evidence

Alas Biodiversity

One would have to be on another planet not to have heard of the current COP 15 meeting in Montreal, the Convention on Biological Diversity. Negotiators have recently finalised an agreement on what the signatory nations will do in the next 5 years or so. I do not wish to challenge the view that these large meetings achieve much discussion and suggestions for action on conservation of biodiversity. I do wish to address, from a scientific viewpoint, issues around the “loss of biodiversity” and in particular some of the claims that are being made about this problem.

The first elephant in the room which must not be ignored is human population growth. At a best guess there are perhaps three times as many people now on earth as the earth can support. So the background for all biodiversity action is human population size and the accompanying resource demands. Too few wish to discuss this elephant.

The second elephant is the vagueness of the concept of biodiversity. If we take its simple meaning to be ‘all life on Earth’, we must face the fact that we are not even close to having a complete catalogue of life on earth. To be sure we know most of the species of birds and mammals, a lot of the fish and the reptiles, so we have made a start. But look at the insects and you will find guesses of several million species that are undescribed. And we have hardly begun to look at the bacteria, fungi, and viruses.

The consequence of this is loose speech. When we say we wish to ‘protect biodiversity’ what exactly do we wish to protect? Only the birds but not all of them, only the ones we like? Or only the large mammals like the polar bears, the African lion, and the panda? Typically, conservation of biodiversity focuses on one charismatic species and hopes for spill over to others, applying the well-known principles of population ecology to the immediate threat. But ecologists talk about ecological communities and ecosystems, so this raises another issue of how to define these entities and how protecting biodiversity can be applied to them.

Now the third elephant comes into play, climate change. To appreciate this, we need to talk to paleoecologists. If you were fortunate to live in central Alaska or the Yukon 30,000 years ago and you formed a society for the conservation of biodiversity, you would face a vegetation community that was destined to disappear or change dramatically, not to mention species like the mammoths and saber-toothed tigers that no longer exist but we love to see in museums. So there is a time scale as well as a spatial scale to biodiversity that is easily forgotten. Small national parks and reserves may not be a solution to the issue.

So whither biodiversity science? If we are serious about biodiversity change, we must lay out more specific questions as a start. Exactly what species are we measuring and for how long and with what precision? We need to concentrate on areas that are protected from human exploitation, one of the main reasons for biodiversity losses, the loss of habitat due to agriculture, mining, forestry, human housing, roads, invasive pests, the list goes on. We need groups of ecologists to concentrate on the key areas we define, on the key threats affecting each area, how we might mitigate these effects, and once these questions are decided we need to direct funding to these groups. Biodiversity funding is all over the map and often wasted on trivial problems. Biodiversity issues are at their core problems in community and ecosystem ecology, and yet we typically treat them as single species problems. We need to study communities and ecosystems. To say that we as ecologists do not know how to study community and ecosystem ecology would be a start. Studying one fish species extensively will not protect the community and ecosystem it requires for survival. If you need a concrete example, consider Pacific salmon on the west coast of North America and the ecosystems they inhabit. This is not a single species problem. In some river systems stocks are doing well, while in other rivers salmon are disappearing. Why? If we know that at least part of the answer to this question lies in ecosystem management and yet no action is undertaken, is this because it costs too much or what? Why can we spend a billion dollars going to the moon and not spend this money on serious ecological problems subject to biodiversity increases or declines? Perhaps part of the problem is that to get to the moon we do not give money to 10 different agencies that do not talk or coordinate with one another. Part of the answer is that governments do not see biodiversity loss or gain as an important problem, and it is easier to talk vaguely about it and do little in the hope that Nature will rectify the problems.

So, we continue in the Era of Biodiversity without knowing what this means and too often without having any plan to see if biodiversity is increasing or declining in any particular habitat or region, and then devising a plan to ameliorate the situation as required. This is not a 5 year or a 10-year plan, so it requires a long-term commitment of public support, scientific expertise, and government agencies to address. For the moment we get an A+ grade for talking and an F- grade for action.

Dupont-Doaré, C. & Alagador, D. (2021) Overlooked effects of temporal resolution choice on climate-proof spatial conservation plans for biodiversity. Biological Conservation, 263, 109330.doi: 10.1016/j.biocon.2021.109330.

Fitzgerald, N., Binny, R.N., Innes, J., Pech, R., James, A., Price, R., Gillies, C. & Byrom, A.E. (2021) Long-Term Biodiversity Benefits from Invasive Mammalian Pest Control in Ecological Restorations. Bulletin of the Ecological Society of America, 102, e01843.doi: 10.1002/bes2.1843.

Moussy, C., Burfield, I.J., Stephenson, P.J., Newton, A.F.E., Butchart, S.H.M., Sutherland, W.J., Gregory, R.D., McRae, L., Bubb, P., Roesler, I., Ursino, C., Wu, Y., Retief, E.F., Udin, J.S., Urazaliyev, R., Sánchez-Clavijo, L.M., Lartey, E. & Donald, P.F. (2022) A quantitative global review of species population monitoring. Conservation Biology, 36, e13721.doi. 10.1111/cobi.13721.

Price, K., Holt, R.F. & Daust, D. (2021) Conflicting portrayals of remaining old growth: the British Columbia case. Canadian Journal of Forest Research, 51, 1-11.doi: 10.1139/cjfr-2020-04530.

Shutt, J.D. & Lees, A.C. (2021) Killing with kindness: Does widespread generalised provisioning of wildlife help or hinder biodiversity conservation efforts? Biological Conservation, 261, 109295.doi: 10.1016/j.biocon.2021.109295.

In Honour of David Suzuki at his Retirement

David Suzuki is retiring from his media work this year at age 86. If you wish to have a model for a lifetime of work, he should be high on your list – scientist, environmentalist, broadcaster, writer. He has been a colleague of mine at the Department of Zoology, UBC from the time when I first came there in 1970. He was a geneticist doing imaginative and innovative research with his students on the humble fruit fly Drosophila melanogaster. The Department at that time was a beehive of research and teaching, and David was a geneticist breathing fire at the undergraduates taking the genetics course. Many a doctor would probably tell you now that Suzuki’s genetics course was the most challenging in their undergraduate education.

The hierarchy in the Department of Zoology was very clear in the 1970s. First came the physiologists, top of the pack and excellent scientists who turned the spotlight on the Department nationally and internationally. Second came the geneticists, with the DNA revolution full on. At the bottom of the pile were the ecologists causing nothing but trouble about fisheries and wildlife management problems, pointing out a rising tide of environmental problems including climate change. Contrary to what you might conclude from the media, environmental problems and climate change issues were very alive even in the 1970s. But somehow these problems did not get through to governments, and David has been a key person turning this around. In 1979 he began a natural history and science program on the CBC entitled “The Nature of Things” which he then hosted for 43 years. In doing so he began to fill an empty niche in Canadian news affairs between the environmental scientists who had data on what was going on in the environment and what needed attention. Environmental scientists were severely ignored both by industry and the governments of the day who operated on two premises – first, that the most critical issues for Canada were economics and economic growth, and second that environmental issues could largely be ignored or could be solved by promises but no action. Alas we are still inundated with the news that “growth is good”, and “more growth is better”.

I had relatively little involvement in David’s increasing interest in environmental issues by 1979, but I had written 3 ecology textbooks by then, pushing some of the environmental issues that are still with us, and I became a friend of David’s in the Department. We ecologists could only admire his ability to speak so clearly on the environmental issues of our day and connect these issues with the many travesties of how First Nations people had been sidelined. He pointed out very forcefully the astonishing failure of governments to address these issues. The public which was much less aware of environmental issues in the 1980s is now highly mobilized thanks in great part to all the work David and his colleagues have done in the last 50 years. He has many friends now but still strong enemies who continue to think of the environment as a large garbage can for economic growth. And he, still in his retirement, having achieved so much from his environmental work, bemoans the slow pace of government actions on environmental problems, as does every ecologist I know. His Foundation continues to press for action on many conservation fronts. So, thank you David for all your work and your wisdom over all these many years. You have engineered a strong environmental movement among old and young and I thank you for all that.

https://davidsuzuki.org/

On Ecological Climate Change Research

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

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:

Natural History
Behavioural Ecology
Applied Ecology
Conservation Ecology
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 Can You Do About the Climate Emergency?

It is very easy to do little in the climate emergency because it is a long-term problem, and many of us will be gone by 2050 when Shell Oil and our government promise Net Zero emissions. Possibly the first thing you should do is find out what “net zero” really means. “Net zero emissions” refers to achieving an overall balance between greenhouse gas emissions produced by us and greenhouse gas emissions taken out of the atmosphere. So clearly it does not mean zero emissions so pollution will still be with us, and all it promises is equality between what goes in and what comes out. If you believe that net-zero will happen, you are living in la-la land, but consider it a scientific hypothesis and if you are young and live to 2050, check the numbers. It means that all the greenhouse gases that are here today will remain and all the problems on our doorstep today will continue – floods, fires, drought, sea level rise, agricultural changes, temperature increases – and if you think none of this will bother you, you can probably buy an inexpensive house in New Mexico and avoid shopping for groceries.

But do not throw your hands up since there are many small things all of us can do to minimize these problems. Here is a partial list:

Drive less, fly less, walk more, get an electric car if you can. Try a bicycle.
Avoid coal, gasoline, and natural gas implements. Sit in the sun, not under a propane heater on the deck.
Put solar panels on your roof if you can. In addition to your windmill generating power.
Put your retirement funds into renewable energy funds, not into oil companies.
Educate yourself and ignore all the dangerous nonsense about climate change that is provided in advertisements, radio, TV, and social media.
Protest against climate nonsense by writing letters, using social media, phoning the stations that allow nonsense to be perpetrated. Your one letter may have minimal effect, but if a million people do the same, someone might listen.
Demand that politicians actually answer questions about climate change action plans. And as they say in Chicago, vote early and vote often.
Nominate Greta Thunberg again for the Nobel Prize. If she does not receive it, request that the Nobel Committee be disbanded and replaced by young people.
Relax and enjoy your life while keeping a lid on your carbon budget.

The climate emergency is not difficult to comprehend. Help the world survive it for your grandchildren.

Our World View and Conservation

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

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 Replication in Ecology

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)

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:

Make a list of the 10 or 15 most important questions for biodiversity science in Canada. This alone would be a major achievement.
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.
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.
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.

Ecological Rants

Ecological opinions of Charley Krebs and Judy Myers