Tag Archives: ecosystem dynamics

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:

  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

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.

Ecology for Now or the Future

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.

On Biodiversity Science

With David Attenborough and all the amazing picture books on biodiversity there can be few people in the world who have not been alerted to the array of beautiful and interesting species on Earth. Until recently the subject of biodiversity, known to First Nations since long, long ago, had not entered the western world of automobiles, industry, farming, fishing, music, theatres, and movies. Biodiversity is now greatly appreciated by most people, but perhaps more as entertainment for western societies and more for subsistence food in less wealthy parts of our world.

There are many different measures of ‘biodiversity’ and when discussing how we should protect biodiversity we should be careful about exactly how this word is being used. The number of different species in an area is one simple measure of biodiversity. But often the types of organisms being considered are less well defined. Forest ecologists attempt to protect forest biodiversity, but logging companies are more concerned only with trees and tree size for commercial use. Bird watchers are concerned with birds and have developed much citizen science in counting birds. Mushroom connoisseurs may worry about what edible mushrooms will be available this summer. But in many cases biodiversity scientists recognize that the community of organisms and the ecosystem that contains them would be a more appropriate unit of analysis. But as the number of species in an ecosystem increases, the complexity of the ecosystem becomes unmanageable. A single ecosystem may have hundreds to thousands of species, and we are in the infant stage of trying to determine how to study these biological systems.

One result is that, given that there are perhaps 10 million species on Earth and only perhaps 10,000 biologists who study biodiversity, where do we begin? The first and most popular way to answer this question is to pick a single species and concentrate on understanding its ecology. This makes are researcher’s life fairly simple. If elephants in Africa are under threat, find out all about the ecology of elephants. If a particular butterfly in England is very rare, try to find out why and how to protect them. This kind of research is very valuable for conservation because it provides a detailed background for understanding the requirements of each species. But the single species approaches lead into at least two quagmires. First, all species exist in a web of other species and understanding this web greatly expands the problem. It is possible in many cases to decipher the effects other species have on our elephants or butterflies, but this requires many more scientists to assist in analysing the species’ food chain, its diseases, its predators and parasites, and that is only a start. The second quagmire is that one of the general rules of ecology is that most species on Earth are rare, and few are common. So that we must concentrate our person-power on the common species because they are easier to find and study. But it is often the rare species that are of conservation concern, and so we should focus on them rather than the common species. In particular, given that only about 10% of the species on Earth have been described scientifically, we may often be assigned a species that does not have any information on its food habits or habitat requirements, its distribution, and how its abundance might be changing over time, a lifetime research program.

The result of this general overview is that the mantra of our day – Protect Biodiversity – begins as a compelling slogan and ends in enormous scientific complexity. As such it falls into the category of slogans like ‘Reduce Poverty’ and ‘Peace on Earth’, something we can all agree on, but the devil is in the details of how to achieve that particular goal.

One way to avoid all these pitfalls has been to jump over the problems of individual species and analyse communities of species or entire ecosystems. The result of this approach is to boil down all the species in the community to a number that estimates “biodiversity” and then use that number in relating ‘biodiversity’ to community attributes like ‘productivity’ or ‘stability’. This approach leads to testing hypotheses like ‘Higher biodiversity leads to greater stability’. There are serious problems with this approach if it is used to test any such hypothesis. First, biodiversity in this example must be rigorously defined as well as stability. The fact that higher biodiversity of butterflies in a particular region is associated with a more stable abundance of these butterflies over time is worthy of note but not of generalization to global communities or ecosystems. And as in all ecological studies we do not know if this is a generalization applicable to all butterfly populations everywhere until many more studies have been done.

A second problem is that this community or ecosystem approach to address ecological questions about biodiversity is not very useful in promoting conservation which boils down to particular species in particular environments. It should force us back to looking at the population ecology of species that are of conservation concern. It is population ecologists who must push forward the main goals of the conservation of the Earth’s biota, as Caughley (1994) recognized long ago.

The practical goals of conservation have always been local, and this constraint is mostly ignored in papers that demand some global research priorities and global ecological rules. The broad problem is that the conservation of biodiversity is a gigantic scientific and political problem that is currently underfunded and in its scientific infancy. At the present too much biodiversity research is short-term and not structured in a comprehensive framework that identifies critical problems and concentrates research efforts on these problems (Nichols et al. 2019, Sutherland et al. 2018). One more important issue for a seminar discussion group. 

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

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

Sutherland, W.J., Butchart, Stuart H.M., Connor, B., Culshaw, C., Dicks, L.V., et al. (2018). A 2018 Horizon Scan of Emerging Issues for Global Conservation and Biological Diversity. Trends in Ecology & Evolution 33, 47-58. doi: 10.1016/j.tree.2017.11.006.

Ecological Science: Monitoring vs. Stamp Collecting

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.

On A Global Agenda for Ecology

Reading the ecology literature now I am excited by the papers that are filling in small gaps in our understanding of population and community ecology. Good work indeed. But I am concerned more about the big picture – what would we like ecological science to show to the world in 50 years as our achievements? There are two aspects of this question. At present the findings of ecological research are presented in the media mostly as what could be coarsely described as ecological trivia, light entertainment. We must continue to do this as it is an important part of keeping the public aware of environmental issues. The second aspect of our public face is the bigger issue of how we can make the future world a better place. This part is a global agenda for ecology that should be the background focus of all our research. So what should be our global agenda?

We could call it global change. Specifically, how will our ecological systems change as a joint consequence of climate change and human disturbances? So look out the window to any natural landscape where you live and ask how much we now know that will allow you to predict what that scene will be like in a century or so. We should be able to make this prediction more easily with human disturbed landscapes that with those driven by environmental change, but I am not sure everyone would agree with this hypothesis. We will probably know that if we continue to overgraze a grassland, we will end with a weed infested wasteland or even bare soil. Consequently, a rational management agency should be able to prevent this degradation. These kinds of change should be easy to manage yet we as a society continue to degrade ecosystems all over the globe. Is there an general index for degradation for the countries of the world, so we could add it to Greenhouse Gas Emissions, freshwater contamination, overharvesting of fish and timber, and a host of other environmental indicators that are useful to the public?

The consequences of climate change are the most difficult to understand and possibly manage. We have lived in a dream world of a stable environment, and the mathematical gurus focus on stability as a sine qua non. Change in a system that is well understood should be predictable both in the short term of 50 years and in the long term of 500 years. But we are not there yet. We work hard on the pieces – is the bird population of this particular national park going up or down?, how rapidly are peat bogs releasing CO2 under current changing climate? – but these details while important do not allow one to predict whole ecosystem shifts. more rapidly. What do we need to do as ecologists to achieve a broad consensus on global issues?

Sutherland et al. (2013, 2018) have made a heroic attempt both to recognize fundamental ecological questions and to identify emerging issues in a broader societal framework. This helps us to focus on both specific ecological issues as well as emerging global problems. One useful recommendation that could proceed from these reviews would be a specific journal that would review each year a small number of these questions or issues that would serve as a progress bar on increasing understanding of ecological unknowns.

A personal example might focus the problem. My colleagues, students, and I have been working in the Yukon boreal forest at Kluane for 46 years now, trying to understand community dynamics. The ecosystem moves slowly because of the cold climate, so in the short term of 50 years we cannot see there will be much significant change. But this is more of a guess than a solid prediction because a catastrophe – fire, insect attacks – could reset the system on a different pathway. The long term (500 year) trajectory for this ecosystem is much harder to predict, except to say that it will be driven largely by the climate-vegetation axis, and this is the link in ecosystem dynamics that we understand least. We cannot assume stability or equilibrium dynamics in boreal forests, and while paleo-ecologists have given us a good understanding of past changes in similar ecosystems, the past is not necessarily a good guide to future long-term changes. So I think a critic could well say that we have failed our attempt to understand our boreal forest ecosystem and be able to predict its trajectory, even though we have more than 300 papers describing how parts of this system interact.

My concern is that as we make progress with the pieces of the ecology puzzle we more and more lose sight of the final goals, and we are lost in the details of local ecosystems. Does this simply mean that we have an ecological ‘Red Queen’ that we will forever be chasing? Perhaps that is both the fundamental joy and the fundamental frustration of working on changing ecological systems. In the meantime, enjoy slaying the unknowns of local, specific ecosystems and on occasion look back to see how far we have come.

Sutherland, W.J.et al. (2013). Identification of 100 fundamental ecological questions. Journal of Ecology 101(1): 58-67. doi: 10.1111/1365-2745.12025.

Sutherland, W.J.et al. (2018). A 2018 Horizon Scan of Emerging Issues for Global Conservation and Biological Diversity. Trends in Ecology & Evolution 33(1): 47-58. doi: 10.1016/j.tree.2017.11.006.

 

On the Loss of Large Mammals

The loss of large mammals and birds in the Pleistocene was highlighted many years ago (Martin and Wright 1967, Grayson 1977, Guthrie 1984 and many other papers). Hypotheses about why these extinctions occurred were flying left and right for many years with no clear consensus (e.g. Choquenot and Bowman 1998). The museums of the world are filled with mastodons, moas, sabre-tooth tigers and many other skeletons of large mammals and birds long extinct. The topic has come up again in a discussion of these extinctions and a prognosis of future losses (Smith et al. 2018). I do not want to question the analysis in Smith et al. (2018) but I want to concentrate on this one quotation that has captured the essence of this paper in the media:

“Because megafauna have a disproportionate influence on ecosystem structure and function, past and present body size downgrading is reshaping Earth’s biosphere.”
(pg. 310).

What is the evidence for this very strong statement? The first thought that comes to mind is from my botanical colleagues who keep reminding me that plants make of 99% of the biomass of the Earth’s ecosystems. So, if this statement is correct, it must mean that large mammals have a very strong effect on plant ecosystem structure and function. And it must also imply that large mammals are virtually immune to predators, so no trophic cascade can occur to prevent plant overgrazing.

I appreciate that it is very difficult to test such a statement since evolution has been going on for a long time before humans arrived, and so there must have been a lot of other factors causing ecosystem changes in those early years. Humans have a disproportionate love for biodiversity that is larger than us. So, we revel in elephants, tigers, bears, and whales, while at the same time we pay little attention to the insects, small mammals, most fish, and plankton. Because of this size bias, we are greatly concerned with the conservation of large animals, as we should be, but much less concerned about what is happening to the small chaps.

What is the evidence that large mammals and birds have a disproportionate influence on ecosystem structure and function? In my experience, I would say there is very little evidence for strong ecosystem effects from the collapse of the megafauna. DeMaster et al. (2006) evaluated a proposed explanation for ecosystem collapse caused by whaling in the North Pacific Ocean and concluded that the evidence was weak for a sequential megafauna collapse caused by commercial whaling. Trites et al. (2007) and Wade et al. (2007) supported this conclusion. Citing paleo-ecological data for Australia, Johnson (2010) and Rule et al. (2012) argued in another evaluation of ecosystem changes that the human-driven extinction of the megafauna in Australia resulted in large changes in plant communities, potentially confounded by climate change and increases in fire frequency about 40K years ago. If we accept these controversies, we are left with trying to decide if the current losses of large mammals are of similar strength to those assigned to the Pleistocene megafauna, as suggested by Smith et al. (2018).

If we define ecosystem function as primary productivity and ecosystem structure as species diversity, I cannot think of a single case in recent studies where this idea has been clearly tested and supported. Perhaps this simply reflects my biased career working in arctic and subarctic ecosystems in which the vast majority of the energy flow in the system rotates through the smaller species rather than the larger ones. Take the Great Plains of North America with and without the bison herds. What aspect of ecosystem function has changed because of their loss? It is impossible to say because of human intervention in the fire cycle and agricultural pre-emption of much of the landscape. It is certainly correct that overgrazing impacts can be severe in human-managed landscapes with overstocking of cattle and sheep, and that is a tragedy brought on by economics, predator elimination programs, and human land use decisions. All the changes we can describe with paleo-ecological methods have potential explanations that are highly confounded.

I think the challenge is this: to demonstrate that the loss of large mammals at the present time creates a large change in ecosystem structure and function with data on energy flow and species diversity. The only place I can see it possible to do this experimentally today would be in arctic Canada where, at least in some areas, caribou come and go in large numbers and with relatively little human impact. I doubt that you could detect any large effect in this hypothetical experiment. It is the little chaps that matter to ecosystem function, not the big chaps that we all love so much. And I would worry if you could do this experiment, the argument would be that it is a special case of extreme environments not relevant to Africa or Australia.

No one should want the large mammals and birds to disappear, but the question of how this might play out in the coming 200 years in relation to ecosystem function requires more analysis. And unlike the current political inactivity over the looming crisis in climate change, we conservation biologists should certainly try to prevent the loss of megafauna.

Choquenot, D., and Bowman, D.M.J.S. 1998. Marsupial megafauna, Aborigines and the overkill hypothesis: application of predator-prey models to the question of Pleistocene extinction in Australia. Global Ecology and Biogeography Letters 7: 167-180.

DeMaster, D.P., Trites, A.W., Clapham, P., Mizroch, S., Wade, P., Small, R.J., and Hoef, J.V. 2006. The sequential megafaunal collapse hypothesis: testing with existing data. Progress in Oceanography 68(2-4): 329-342. doi:10.1016/j.pocean.2006.02.007

Grayson, D.K. 1977. Pleistocene avifaunas and the Overkill Hypothesis. Science 195: 691-693.

Guthrie, R.D. 1984. Mosaics, allelochemics and nutrients: An ecological theory of late Pleistocene megafaunal extinctions. In: Quaternary Extinctions: A Prehistoric Revolution ed by P.S. Martin and R.G. Klein. University of Arizona Press Tucson.

Johnson, C.N. 2010. Ecological consequences of Late Quaternary extinctions of megafauna. Proceeding of the Royal Society of London, Series B 276(1667): 2509-2519. doi: 10.1098/rspb.2008.1921.

Martin, P.S., and Wright, H.E. (eds). 1967. Pleistocene Extinctions; The Search for a Cause. Yale University Press, New Haven, Connecticut. 453 pp.

Rule, S., Brook, B.W., Haberle, S.G., Turney, C.S.M., Kershaw, A.P., and Johnson, C.N. 2012. The aftermath of megafaunal extinction: ecosystem transformation in Pleistocene Australia. Science 335(6075): 1483-1486. doi: 10.1126/science.1214261.

Smith, F.A., Elliott Smith, R.E., Lyons, S.K., and Payne, J.L. 2018. Body size downgrading of mammals over the late Quaternary. Science 360(6386): 310-313. doi: 10.1126/science.aao5987.

Trites, A.W., Deecke, V.B., Gregr, E.J., Ford, J.K.B., and Olesiuk, P.F. 2007. Killer whales, whaling, and sequential megafaunal collapse in the North Pacific: a comparative analysis of the dynamics of marine mammals in Alaska and British Columbia following commercial whaling. Marine Mammal Science 23(4): 751-765. doi: 10.1111/j.1748-7692.2006.00076.x.

Wade, P.R., et al. 2007. Killer whales and marine mammal trends in the North Pacific – a re-examination of evidence for sequential megafaunal collapse and the prey-switching hypothesis. Marine Mammal Science 23(4): 766-802. doi: 10.1111/j.1748-7692.2006.00093.x.

On Mauna Loa and Long-Term Studies

If there is one important element missing in many of our current ecological paradigms it is long-term studies. This observation boils down to the lack of proper controls for our observations. If we do not know the background of our data sets, we lack critical perspective on how to interpret short-term studies. We should have learned this from paleoecologists whose many studies of plant pollen profiles and other time series from the geological record show that models of stability which occupy most of the superstructure of ecological theory are not very useful for understanding what is happening in the real world today.

All of this got me wondering what it might have been like for Charles Keeling when he began to measure CO2 levels on Mauna Loa in Hawaii in 1958. Let us do a thought experiment and suggest that he was at that time a typical postgraduate students told by his professors to get his research done in 4 or at most 5 years and write his thesis. These would be the basic data he got if he was restricted to this framework:

Keeling would have had an interesting seasonal pattern of change that could be discussed and lead to the recommendation of having more CO2 monitoring stations around the world. And he might have thought that CO2 levels were increasing slightly but this trend would not be statistically significant, especially if he has been cut off after 4 years of work. In fact the US government closed the Mauna Loa observatory in 1964 to save money, but fortunately Keeling’s program was rescued after a few months of closure (Harris 2010).

Charles Keeling could in fact be a “patron saint” for aspiring ecology graduate students. In 1957 as a postdoc he worked on developing the best way to measure CO2 in the air by the use of an infrared gas analyzer, and in 1958 he had one of these instruments installed at the top of Mauna Loa in Hawaii (3394 m, 11,135 ft) to measure pristine air. By that time he had 3 published papers (Marx et al. 2017). By 1970 at age 42 his publication list had increased to a total of 22 papers and an accumulated total of about 50 citations to his research papers. It was not until 1995 that his citation rate began to exceed 100 citations per year, and after 1995 at age 67 his citation rate increased very much. So, if we can do a thought experiment, in the modern era he could never even apply for a postdoctoral fellowship, much less a permanent job. Marx et al. (2017) have an interesting discussion of why Keeling was undercited and unappreciated for so long on what is now considered one of the world’s most critical environmental issues.

What is the message for mere mortals? For postgraduate students, do not judge the importance of your research by its citation rate. Worry about your measurement methods. Do not conclude too much from short-term studies. For professors, let your bright students loose with guidance but without being a dictator. For granting committees and appointment committees, do not be fooled into thinking that citation rates are a sure metric of excellence. For theoretical ecologists, be concerned about the precision and accuracy of the data you build models about. And for everyone, be aware that good science was carried out before the year 2000.

And CO2 levels yesterday were 407 ppm while Nero is still fiddling.

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

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

Ecological Alternative Facts

It has become necessary to revise my recent ecological thinking about the principles of ecology along the lines now required in the New World Order. I list here the thirteen cardinal principles of the new ecology 2017:

  1. Population growth is unlimited and is no longer subject to regulation.
  2. Communities undergo succession to the final equilibrium state of the 1%.
  3. Communities and ecosystems are resilient to any and all disturbances and operate best when challenged most strongly, for example with oil spills.
  4. Resources are never limiting under any conditions for the 1% and heavy exploitation helps them to trickle down readily to assist the other 99%.
  5. Overexploiting populations is good for the global ecosystem because it gets rid of the species that are wimps.
  6. Mixing of faunas and floras have been shown over the last 300 years to contribute to the increasing ecological health of Earth.
  7. Recycling is unnecessary in view of recent advances in mining technology.
  8. Carbon dioxide is a valuable resource for plants and we must increase its contribution to atmospheric chemistry.
  9. Climate change is common and advantageous since it occurs from night to day, and has always been with us for many millions of years.
  10. Evolution maximizes wisdom and foresight, especially in mammals.
  11. Conservation of less fit species is an affront to alternative natural laws that were recognized during the 18th century and are now mathematically defined in the new synthetic theory of economic and ecological fitness.
  12. Scientific experiments are no longer necessary because we have computers and technological superiority.
  13. Truth in science is no longer necessary and must be balanced against equally valid post-truth beliefs.

The old ecology, now superseded, was illustrated in Krebs (2016), and is already out of date. Recommendations for other alternative ecological facts will be welcome. Please use the comments.

Krebs, C.J. (2016) Why Ecology Matters. University of Chicago Press, Chicago. 208 pp.