Tag Archives: long-term problems

Should Empirical Ecology be all Long-term?

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The majority of empirical ecology research published in our journals is short-term with the time span dictated by the need for 1–2-year Master’s degree studies and 3-4-year PhD research. This has been an excellent model when there was little of a framework for researching the critical questions ecologists ought to answer. Much of ecology in the good old days was based on equilibrium models of populations, communities, and ecosystems, an assumption we know to be irrelevant to a world with a changing climate. Perhaps we should have listened to the paleoecologists who kept reminding us that there was monumental change going on in the eras of glaciation and much earlier in the time of continental drift (Birks 2019). All of this argues that we need to change direction from short-term studies to long-term studies and long-term thinking.

There are many short-term ecological studies that are useful and should be done. It is necessary for management agencies to know if the spraying of forest insect pests this year reduces damage next year, and many similar problems exist that can be used for student projects. But the big issues of our day are long term problems, defined in the first place by longer than the research lifespan of the average ecologist, about 40 years. These big issues are insufficiently studied for two reasons. First, there is little funding for long term research. We can find a few exemptions to this statement, but they are few and many of them are flawed. Second, we as research scientists want to do something new that no one has done before. This approach leads to individual fame and sometimes fortune and is the social model behind many of the research prizes that we hear about in the media, the Nobel Prize, the MacArthur Awards, the National Medal of Science, the Kyoto Prize and many more. The point here is not that we should stop giving these awards (because they are socially useful), but that we should take a broader perspective on how research really works. Many have recognized that scientific advances are made by groups of scientists standing on the shoulders of an earlier generation. Perhaps some of the awards in medicine recognize this more frequently than other areas of science. My point is that large problems in ecology require a group effort by scientists that is too often unrecognized in favour of the individual fame model of science prizes.

A few examples may exemplify the need in ecology to support group studies of long-term problems. The simplest cases are in the media every day. The overharvesting of trees continues with little research into the long-term recovery of the harvested area and exactly how the forest community changes as it recovers. We mine areas for minerals and drill and mine tar sands for oil and gas with little long-term view of the recovery path which may stretch to hundreds or thousands of years while our current research program is long-term if it goes for 10 years. Canada has enough of these disturbance problems to fill the leger. The Giant Gold Mine in the Northwest Territories of Canada mined 220,000 kg of gold from 1948 to 2004 when it closed. It left 237 tonnes of arsenic trioxide dust, a by-product for extracting gold. The long-term ecosystem problems from this toxic compound will last for centuries but you might expect it will be much sooner forgotten than subjected to long-term study.

So where are we ecologists with respect to these large problems? We bewail biodiversity loss and when you look at the available data and the long-term studies you would expect to measure biodiversity and, if possible, manage this biodiversity loss. But you will find only piecemeal short-term studies of populations, communities, and ecosystems that are affected. We tolerate this unsatisfactory scientific situation even for ecosystems as iconic as the Great Barrier Reef of eastern Australia where we have a small number of scientists monitoring the collapse of the reef from climate change. The only justification we can give is that “Mother Nature will heal itself” or in the scientific lingo, “the organisms involved will adapt to environmental change”. All the earth’s ecosystems have been filtered through a million years of geological change, so we should not worry, and all will be well for the future, or so the story goes.

I think few ecologists would agree with such nonsense as the statements above, but what can we do about it? My main emphasis here is long-term monitoring. No matter what you do, this should be part of your research program. If possible, do not count birds on a plot for 3 years and then stop. Do not live trap mice for one season and think you are done. If you have any control over funding recommendations, think continuity of monitoring. Long-term monitoring is a necessary but not a sufficient condition for managing biodiversity change.

There are many obstacles interfering with achieving this goal. Money is clearly one. If your research council requests innovation in all research proposals, they are probably driven by Apple iPhone producers who want a new model every year. For the past 50 years we have been able to fund monitoring in our Yukon studies without ever using the forbidden word monitor because it was not considered science by the government granting agencies. In one sense it is not whether you consider science = innovation or not, but part of the discussion about long term studies might be shifted to consider the model of weather stations, and to discuss why we continue to report temperatures and CO2 levels daily when we have so much past data. No one would dream of shutting down weather monitoring now after the near fiasco around whether or not to measure CO2 in the atmosphere (Harris, 2010, Marx et al. 2017).

Another obstacle has been the destruction of research sites by human developments. Anyone with a long history of doing field research can tell you of past study areas that have been destroyed by fire or are now parking lots, or roads, or suburbia. This problem could be partly alleviated by the current proposals to maintain 30% of the landscape in protected areas. We should however avoid designating areas like the toxic waste site of the Giant Gold Mine as a “protected area” for ecological research.

Where does this all lead? Consider long-term monitoring if you can do the research as part of your overall program. Read the recent contributions of Hjeljord, and Loe (2022) and Wegge et al. (2022) as indicators of the direction in which we need to move, and if you need more inspiration about monitoring read Lindenmayer (2018).

Birks, H.J.B. (2019) Contributions of Quaternary botany to modern ecology and biogeography. Plant Ecology & Diversity, 12, 189-385.doi: 10.1080/17550874.2019.1646831.

Harris, D.C. (2010) Charles David Keeling and the story of atmospheric CO2 measurements. Analytical Chemistry, 82, 7865-7870.doi: 10.1021/ac1001492.

Hjeljord, O. & Loe, L.E. (2022) The roles of climate and alternative prey in explaining 142 years of declining willow ptarmigan hunting yield. Wildlife Biology, 2022, e01058.doi: 10.1002/wlb3.01058.

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.

Marx, W., Haunschild, R., French, B. & Bornmann, L. (2017) Slow reception and under-citedness in climate change research: A case study of Charles David Keeling, discoverer of the risk of global warming. Scientometrics, 112, 1079-1092.doi: 10.1007/s11192-017-2405-z.

Wegge, P., Moss, R. & Rolstad, J. (2022) Annual variation in breeding success in boreal forest grouse: Four decades of monitoring reveals bottom-up drivers to be more important than predation. Ecology and Evolution.12, e9327. doi: 10.1002/ece3.9327.

Alas Biodiversity

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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.

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 Can You Do About the Climate Emergency?

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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:

  1. Drive less, fly less, walk more, get an electric car if you can. Try a bicycle.
  2. Avoid coal, gasoline, and natural gas implements. Sit in the sun, not under a propane heater on the deck.
  3. Put solar panels on your roof if you can. In addition to your windmill generating power.
  4. Put your retirement funds into renewable energy funds, not into oil companies.
  5. Educate yourself and ignore all the dangerous nonsense about climate change that is provided in advertisements, radio, TV, and social media.
  6. 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.
  7. Demand that politicians actually answer questions about climate change action plans. And as they say in Chicago, vote early and vote often.
  8. 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.
  9. 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.

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 the Canadian Biodiversity Observation Network (CAN BON)

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Ecology for Now or the Future

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With the general belief that the climate is changing and that these changes must continue for at least 100 years due to the atmospheric physics of greenhouse gases, ecologists of all stripes face a difficult decision. The optimist says to continue with current studies, with due analysis of data from the past getting published, with the assumption that the future will be like the past. We know that the future will not be like the past so our belief in the future is a projection not a prediction. Does this mean that ecologists today should really be in the History Department of the Faculty of Arts?

Well, no one would allow this to happen, since we are scientists not the connivers of untestable stories of past events that masquerade as history, a caricature of the scientific method. The general problem is applicable to all the sciences. The physical sciences of physics and chemistry are fixed for all eternity, so physicists do not have to worry. The geological sciences are a mix of history and applied physics with hypotheses that are partly testable in the current time but with an overall view of future predictions that have a time scale of hundreds to thousands of years. One way to look at this problem is to imagine what a textbook of Physics would look like in 100 years, compared to a textbook of Geology or Biology or Ecology.

Ecological science is burdened by the assumption of equilibrium systems which we all know to be false since we have the long-term evidence of evolution staring at us as well as the short-term evidence of climate change. Ecologists have only two options under these constraints: assume equilibrium conditions over short time-frames or model the system to provide future projections of change. First, assume we are dealing with equilibrium systems within a defined time frame so that we can define clear hypotheses and test them on a short time scale of 10 to perhaps 20 years so we reach a 10–20-year time scale understanding of ecological processes. This is how most of our ecological work is currently carried out. If we wish to study the pollination of a particular set of plants or a crop, we work now to find out which species pollinate, and then hopefully in a short time frame try to monitor if these species are increasing or declining over our 10–20-year time span. But we do this research with the knowledge that the time frame of our ecological information is at most 100 years and mostly much less. So, we panic with bird declines over a 48 year time span (Rosenberg et al. 2019) with an analysis based on unreliable population data, and we fail to ask what the pattern might look like if we had data for the last 100 years or what it might look like in the next 100 years. We have the same problem with insect declines (Wagner et al. 2021, Warren et al. 2021).

If we wish to improve these studies we need much better monitoring programs, and with some notable exceptions there is little sign yet that this is happening (Lindenmayer et al. 2018, 2020). But the real question must come back to the time frame and how we can make future projections. We cannot do this with a 3-year funding cycle. If most of our conservation problems can be traced to human alterations of the biosphere then we must document these carefully with the usual scientific methods. At present I would hazard a guess that 95% of all endangered species are due directly to human meddling, even if we remove the effect of climate change.  

One way to make future projections is to model the population or community under study. A great deal of modelling is being done and has been done but there is little follow-through of how accurate the model predictions have been and little plan to test these projections. We may be successful with models that predict next year’s population or community dynamics, given much background data but that is only a tiny step to estimating what will be there in even 20 or 30 years. We need testable models more than panic calls about declining species with no efforts to discover if and why.

Where does that leave us? We must continue to analyse the ecological state of our current populations and communities and beware of the assumption that they are equilibrium systems. While physics for the future is rather well settled, ecological questions are not.

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.

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.

Rosenberg, K.V., et al. (2019). Decline of the North American avifauna. Science 366, 120-124. doi: 10.1126/science.aaw1313.

Wagner, D.L., Grames, E.M., Forister, M.L., Berenbaum, M.R., and Stopak, D. (2021). Insect decline in the Anthropocene: Death by a thousand cuts. Proceedings of the National Academy of Sciences 118, e2023989118. doi: 10.1073/pnas.2023989118.

Warren, M.S., et al. (2021). The decline of butterflies in Europe: Problems, significance, and possible solutions. Proceedings of the National Academy of Sciences 118 (2), e2002551117. doi: 10.1073/pnas.2002551117.

A Poem on the State of Agriculture in 1935

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After listening to me rant about the state of modern agriculture in the Anthropocene, a colleague in Australia sent me this poem by C.J. Dennis (1876 – 1938) written long before most of us were born. I reprint it here as a reminder that many of our ecological problems are not new, that we have perhaps made progress on some but that in many areas Dennis’s poem about agriculture could have been published today. A powerful poem that in a classroom discussion might lead us to second thoughts that we now live in the best of all possible worlds. Vale C.J. Dennis.

C.J. Dennis in the Herald in 1935 in Australia
THE SPOILERS

“Because overstocking and continuous grazing have denuded the land of vegetation and removed all resistance to wind and flood, it has now been suddenly realised that erosion in the Western districts of N.S.W. has reduced thousands of acres to little better than desert. A descendant of the original black inhabitants of this country might regard this as just retribution.

Ye are the Great White People, masters and lords of the earth,
Spreading your stern dominion over the world’s wide girth.
Here, where my fathers hunted since Time’s primordial morn,
To our land’s sweet, fecund places, you came with your kine and corn.
Mouthing your creed of Culture to cover a baser creed,
Your talk was of White Man’s magic, but your secret god was Greed.
And now that your generations to the second, the third have run,
White Man, what of my country?  Answer, what have you done?

Now the God of my Simple People was a simple, kindly God,
Meting his treasure wisely that sprang from this generous sod,
With never a beast too many and never a beast too few,
Thro’ the lean years and the fruitful, he held the balance true.
Then the White Lords came in their glory; and their cry was: “More!  Yet more!”
And to make them rich for a season they filched Earth’s age-old store,
And they hunted my Simple People — hunters of yester-year —
And they drove us into the desert — while they wrought fresh deserts here.

They ravaged the verdant uplands and spoiled wealth ages old,
Laid waste with their pumps and sluices for a gunny-bag of gold;
They raided the primal forests and the kind, rain-bringing trees
That poured wealth over the lowlands thro’ countless centuries;
They fed their kine on the grasslands, crowding them over the land,
Till blade and root in the lean years gave place to hungry sand.
Then, warned too late of their folly, the White Lords grew afraid,
And they cried to their great god Science; but Science could not aid.

This have you done to our country, lords of the air and the seas,
This to the hoarded riches of countless centuries —
Life-yielding loam, uncovered, unsheltered in the drought,
In the floods your hand unbridled, to the age-old sea drifts out.
You have sold man’s one true birthright for a White Man’s holiday,
And the smothering sands drift over where once green fields turn grey —
Filched by the White Man’s folly to pamper the White Lords’ vice;
And leave to your sons a desert where you found a paradise.”

Herald, 6 December 1935, page 6

http://www.middlemiss.org/lit/authors/denniscj/newspapers/herald/1935/works/spoilers.html

Ecological Science: Monitoring vs. Stamp Collecting

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Ecology as a science is deeply divided by two views of the natural world. First is the view that we need to monitor changes in the distribution and abundance of the biota and try to explain why these changes are occurring through experiments. The second view is that we need to understand ecosystems as complex systems, and this can be done only by models with a tenuous link to data. It is worth discussing the strengths and weaknesses of each of these views of our science.

The first view could be described as the here-and-now approach, studies of how the populations, communities, and ecosystems are changing in all the biomes on Earth. It is clearly impossible to do this properly because of a lack of funding and person-power. Because of this impossibility we change our focus to short-term studies of populations, species, or communities and try to grasp what is happening in the time scale of our lifetime. This had led to a literature of confusing short-term studies of problems that are long-term. Experiments must be short term because of funding. Any long-term studies such of those highlighted in textbooks are woefully inadequate to support the conclusions reached. Why is this? It is the baffling complexity of even the simplest ecological community. The number of species involved is too large to study all of them, so we concentrate on the more abundant species, assuming all the rare species are of little consequence. This has led to a further division within the monitoring community between conservation ecologists who worry about the extinction of larger, dominant species and those that worry about the loss of rare species.

The first approach is further compromised by climate change and human exploitation of the Earth. You could invest in the study of a grassland ecosystem for 15 years only to find it turned into a subdivision of houses in year 16. We try to draw conclusions in this hypothetical case by the data of the 15 years of study. But if physiological ecologists and climate change models are even approximately correct, the structure of similar grassland ecosystems will change due to rainfall and temperature shifts associated with greenhouse gases. Our only recourse is to hope that evolution of physiological tolerances will change fast enough to rescue our species of interest. But there is no way to know this without further empirical studies that monitor climate and the details of physiological ecology. And we talk now about understanding only single species and are back to the complexity problem of species interactions in communities.

The second approach is to leap over all this complexity as stamp-collecting and concentrate on the larger issues. Are our ecological communities resilient to climate change and species invasions? Part of this approach comes from paleoecology and questions of what has happened during the last 10,000 or one million years. But the details that emerge from paleoecology are very large scale, very interesting but perhaps not a good guide to our future under climate change. If a forward-looking forestry company wishes to make sure it has 100-year-old trees to harvest in 100 years’ time, what species should they plant now in central Canada? Or if a desert community in Chile is to be protected in a national park, what should the management plan involve? These kinds of questions are much harder to answer than simpler ones like how many dingoes will we have in central Australia next year.

Long-term experiments could bridge the gap between these two approaches to ecological understanding, but this would mean proper funding and person-power support for numerous experiments that would have a lifetime of 25 to 100 years or more. This will never happen until we recognize that the Earth is more important than our GDP, and that economics is the king of the sciences.

Where does all this lead ecological scientists? Both approaches have been important to pursue in what has been the first 100 years of ecological studies and they will continue to be important as our ecological understanding improves. We need good experimental science on a small scale and good broad thinking on long time scales with extensive studies of everything from coral reefs to the Alaskan tundra. We need to make use of the insights of behavioural ecology and physiological ecology in reaching our tentative conclusions. And if anyone tells you what will happen in your lifetime in all our forests and all the biodiversity on Earth, you should be very careful to ask for strong evidence before you commit to a future scenario.

Beller, E.E., McClenachan, L., Zavaleta, E.S., and Larsen, L.G. (2020). Past forward: Recommendations from historical ecology for ecosystem management. Global Ecology and Conservation 21, e00836. doi: 10.1016/j.gecco.2019.e00836.

Bro-Jørgensen, J., Franks, D.W., and Meise, K. (2019). Linking behaviour to dynamics of populations and communities: application of novel approaches in behavioural ecology to conservation. Philosophical Transactions of the Royal Society, B.  Biological Sciences 374: 20190008.  doi: 10.1098/rstb.2019.0008.

Lidicker, W.Z. (2020). A Scientist’s Warning to humanity on human population growth. Global Ecology and Conservation 24, e01232. doi: 10.1016/j.gecco.2020.e01232.

McGowan, D. W., Goldstein, E. D., and Zador, S. (2020). Spatial and temporal dynamics of Pacific capelin Mallotus catervarius in the Gulf of Alaska: implications for ecosystem-based fisheries management. Marine Ecology. Progress Series 637, 117-140. doi: 10.3354/meps13211.

Tsujimoto, M., Kajikawa, Y., and Matsumoto, Y. (2018). A review of the ecosystem concept — Towards coherent ecosystem design. Technological Forecasting & Social Change 136, 49-58. doi: 10.1016/j.techfore.2017.06.032.

Wolfe, Kennedy, Kenyon, Tania M., and Mumby, Peter J. (2021). The biology and ecology of coral rubble and implications for the future of coral reefs. Coral Reefs 40, 1769-1806. doi: 10.1007/s00338-021-02185-9.

Yu, Zicheng, Loisel, J., Brosseau, D.P., Beilman, D.W., and Hunt, S.J. (2010). Global peatland dynamics since the Last Glacial Maximum. Geophysical Research Letters 37, L13402. doi: 10.1029/2010GL043584.