Author Archives: Charles Krebs

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.

Have we moved on from Hypotheses into the New Age of Ecology?

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For the last 60 years a group of Stone Age scientists like myself have preached to ecology students that one needs hypotheses to do proper science. Now it has always been clear that not all ecologists followed this precept, and a recent review hammers this point home (Betts et al. 2021). I have always asked my students to read the papers from the Stone Age about scientific progress – Popper (1959), Platt (1964), Peters (1991) and even back to the Pre-Stone Age, Chamberlin (1897). There has been much said about this issue, and the recent Betts et al. (2021) paper pulls much of it together by reviewing papers from 1991 to 2015. Their conclusion is dismal if you think ecological science should make progress in gathering evidence. No change from 1990 to 2015. Multiple alternative hypotheses = 6% of papers, Mechanistic hypotheses = 25% of papers, Descriptive hypotheses = 12%, No hypotheses = 75% of papers. Why should this be after years of recommending the gold standard of multiple alternative hypotheses? Can we call ecology a science with these kinds of scores? 

The simplest reason is that in the era of Big Data we do not need any hypotheses to understand populations, communities, and ecosystems. We have computers, that is enough. I think this is a rather silly view, but one would have to interview believers to find out what they view as progress from big data in the absence of hypotheses. The second excuse might be that we cannot be bothered with hypotheses until we have a complete description of life on earth, food webs, interaction webs, diets, competitors, etc. Once we achieve that we will be able to put together mechanistic hypotheses rapidly. An alternative statement of this view is that we need very much natural history to make any progress in ecology, and this is the era of descriptive natural history and that is why 75% of papers do not list the word hypothesis.

But this is all nonsense of course, and try this view on a medical scientist, a physicist, an aeronautical engineer, or a farmer. The fundamental principle of science is cause-and-effect or the simple view that we would like to see how things work and why often they do not work. Have your students read Romesburg (1981) for an easy introduction and then the much more analytical book by Pearl and Mackenzie (2018) to gain an understanding of the complexity of the simple view that there is a cause and it produces an effect. Hone et al. (2023) discuss these specific problems with respect to improving our approach to wildlife management

What can be done about the dismal situation described by Betts et al. (2021)? One useful recommendation for editors and reviewers would be to request for every submitted paper for a clear statement of the hypothesis they are testing, and hopefully for alternative hypotheses. There should be ecology journals specifically for natural history where the opposite gateway is set: no use of ‘hypothesis’ in this journal. This would not solve all the Betts et al. problems because some ecology papers are based on the experimental design of ‘do something’ and then later ‘try to invent some way to support a hypotheses’, after the fact science. One problem with this type of literature survey is, as Betts et al. recognized, is that papers could be testing hypotheses without using this exact word. So words like ‘proposition’, ‘thesis’, ‘conjectures’ could camouflage thinking about alternative explanations without the actual word ‘hypothesis’.

One other suggestion to deal with this situation might be for journal editors to disallow all papers with hypotheses that are completely untestable. This type of rejection could be instructive to authors to assist rewriting your paper to be more specific about alternative hypotheses. If you can make a clear causal set of predictions that a particular species will go extinct in 100 years, this could be described as a ‘possible future scenario’ that could be guided by some mechanisms that are specified. Or if you have a hypothesis that ‘climate change will affect species geographical ranges, you are providing  a very vague inference that is difficult to test without being more specific about mechanisms, particularly if the species involved is rare.

There is a general problem with null hypotheses which state there is “no effect”. In some few cases these null hypotheses are useful but for the most part they are very weak and should indicate that you have not thought enough about alternative hypotheses.

So read Platt (1964) or at least the first page of it, the first chapter of Popper (1959), and Betts et al. (2021) paper and in your research try to avoid the dilemmas they discuss, and thus help to move our science forward lest it become a repository of ‘stamp collecting’.

Betts, M.G., Hadley, A.S., Frey, D.W., Frey, S.J.K., Gannon, D., Harris, S.H., et al. (2021) When are hypotheses useful in ecology and evolution? Ecology and Evolution, 11, 5762-5776. doi: 10.1002/ece3.7365.

Chamberlin, T.C. (1897) The method of multiple working hypotheses. Journal of Geology, 5, 837-848 (reprinted in Science 148: 754-759 in 1965). doi. 10.1126/science.148.3671.754.

Hone, J., Drake, A. & Krebs, C.J. (2023) Evaluation options for wildlife management and strengthening of causal inference BioScience, 73, 48-58.doi: 10.1093/biosci/biac105.

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

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

Platt, J.R. (1964) Strong inference. Science, 146, 347-353.doi: 10.1126/science.146.3642.347.

Popper, K.R. (1959) The Logic of Scientific Discovery. Hutchinson & Co., London. ISBN: 978-041-5278-447.

Romesburg, H.C. (1981) Wildlife science: gaining reliable knowledge. Journal of Wildlife Management, 45, 293-313. doi:10.2307/3807913.

Management by Killing

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While reading a recent wildlife management magazine I became focused on the idea that the main topic of interest was killing in the same way that the news every day is now about who killed who yesterday. The management paradigm behind my concerns is this simple one:

  1. Decide who are the “good guys” and who are the “bad guys”.
  2. Kill all (or many) of the “bad guys”.

I know this sounds too simple but bear with me. In the papers this week are two current management issues. In Sweden they have decided they need only 400 wolves in the entire country, and they have several hundred too many, so they armed many hunters with very large guns to go out and kill every wolf they can find, using dogs and other tricks, until they reach the magic number of 400 left. In British Columbia there is concern that predators like sea lions and seals eat Pacific salmon so there are fewer salmon for the fishers to catch and sell. The answer again leaps to mind – kill the sea lions and seals and anything else that eats salmon, Fisheries Science 101.

If this approximates ‘management’, our main discussions must be to decide who are the “good guys”. This leads to conflicts with conservation at times, so we must develop a “killing for conservation” subroutine (Shutt and Lees 2021) which raises the cumbersome question of whether our conservation efforts are causing harm to other species.

One way to challenge the Management by Killing paradigm is to start with a food web of the species involved – what might be the consequences of taking one species out of a food web on any or all the other species in the web? Now the management problem expands because we must do good community ecology to answer these questions. Some of the simple food web consequences have already been well described. Study the coyotes in the grasslands and you will find out how complex its diet is (Lingle et al. 2022), so that killing coyotes will affect other species and you may get many more prairie dogs or ground squirrels, some of which may carry the plague bacterium and many of which predate on ground nesting birds. Or if you are a fan of penguins in Antarctica you will find that killer whales eat penguins (Pitman and Durban 2010) so do we kill killer whales to save penguins? King penguins are declining on Macquarie Island for reasons that are not clear, and predation by a suite of avian birds of prey is one possible component (Pascoe et al. 2022). Yet we are reluctant to kill bird predators. Barred owls kill the endangered spotted owl in western North America, so should we be killing barred owls in areas of overlap (Bodine and Capaldi 2017, Wiens et al. 2021)? So even if you have available detailed natural history information on a predator, you cannot easily estimate the effect of removing it without field experimentation.  

My main points are two. First, if you are able, educate your favourite newscaster about the complexities of the Management by Killing approach to conservation. Second, support more detailed research on food web dynamics to show that ecosystems cannot be managed by the two simple rules listed above.

It does not escape me that all this discussion could be applied to the human species, but I venture far out of my field of competence to address this political and social issue (Ein et al. 2022).

Bodine, E.N. & Capaldi, A. (2017) Can culling Barred Owls save a declining Northern Spotted Owl population? Natural Resource Modeling, 30, e12131.doi. 10.1111/nrm.12131.

Ein, N., Liu, J.J.W. Houle, S. Easterbrook, B. et al. (2022) The effects of child encounters during military deployments on the well-being of military personnel: a systematic review. European Journal of Psychotraumatology, 13(2): 2132598. doi. 10.1080/20008066.2022.2132598.

Lingle, S., Breiter, C.J., Schowalter, D.B. & Wilmshurst, J.F. (2022) Prairie dogs, cattle subsidies and alternative prey: seasonal and spatial variation in coyote diet in a temperate grassland. Wildlife Biology, 2022: 5.1doi. 10.1002/wlb3.01048.

Pascoe, P., Raymond, B. & McInnes, J. (2022) The current trajectory of king penguin (Aptenodytes patagonicus ) chick numbers on Macquarie Island in relation to environmental conditions. ICES Journal of Marine Science, 79, 2084-2092.doi.

Pitman, R.L. & Durban, J.W. (2010) Killer whale predation on penguins in Antarctica. Polar Biology, 33, 1589-1594.doi. 10.1007/s00300-010-0853-5.

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.

Wiens, J.D., Dugger, K.M., Higley, J.M., Lesmeister, D.B., Franklin, A.B., et al. (2021) Invader removal triggers competitive release in a threatened avian predator. Proceedings of the National Academy of Sciences, 118 (31), e2102859118.doi. 10.1073/pnas.2102859118.

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.

Is Ecology Becoming a Correlation Science?

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

In Honour of David Suzuki at his Retirement

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

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

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

https://davidsuzuki.org/

How to Destroy a Research Station

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I have had the ‘privilege’ over the last 60 years of watching three ecological field stations be destroyed. Admittedly this is a small sample, against which every ecologist can complain, but I wanted to present to you my list of how to achieve this kind of destruction should you ever be commanded to do so. I will not name names or specific places, since the aim is to develop a general theory rather than to name and pillory specific historical actions and people. I suggest that nine rules are needed to proceed smoothly in this matter if you are given this job.

  1.  Have a clear vision why you wish to destroy an existing station. Do not vacillate. The background may be money, or philosophy of science, or orders from those higher in the echelon, or a personal peeve. Remember you are an administrator, and no one can challenge your wisdom in making major changes or closing the station.  
  2. Speak to none of the current users of the research station. If the research station has a Users Committee, avoid talking to them until after all the decisions are made. A users committee is just an honorary appointment, and it helps if very few of the users are actually people who do research at the station. It is very important that your vision should not be clouded by personnel or research programs currently running at the station. And it is best if the scientists using the station have no information except gossip about the changes that are coming.
  3. Avoid loose talk around your office. If you or your group are paying a visit in the field to the research station before closing it or repositioning its purpose, give out no information to anyone on future courses of action.
  4. Communicate upwards in the hierarchy, never downwards. You must keep all the members of the higher echelons fully informed. Do not dwell on the details of your progress in destruction but emphasize the gains that will flow from this dismantling. Tell fibs as much as you like because no one will question your version of events.
  5. Never read anything about the history of the research station or read any of the papers and reports that have originated there. The key is that you as an administrator know what should be done, and the last consideration is history. Administrators must keep a clear mind, unconcerned with historical trivia.
  6. Let none of the destruction news reach the media lest the public in general might begin to see what is happening. Newspaper and media coverage are rarely flattering to bureaucrats. If possible, line up a sympathetic media person who can talk about the brilliant future of the research station and the wisdom of the decisions you have made.
  7. Take a strong business approach. Do not worry if you must fire people currently running the research station or eject scientists currently working there. Everyone must retire at some point and all business leaders have solid recipes for hiring contractors to take care of any problems with the buildings. No matter what the extra cost.
  8. Sell the research station if you possibly can in order to gain revenue for your yet to be revealed vision. You may talk complete nonsense to explain why you are making major changes or closing the research station because few of your possible critics will be in a position to distinguish nonsense statements from truth. ‘Alternative facts’ are very useful if your decisions are questioned.
  9. Realize that if you have made a mistake in destroying a research station, your employer will not know that for several years. By that time, you will have ascended in the hierarchy of your employment unit for having carried out such a definitive action. And if your co-workers know the poor job you are doing, they will write sterling letters of reference for you to move you to another position in a different department or agency so that the worse the job you have done, the stronger will be the reference letters to recommend you for another job.

There is almost no literature I can find on this topic of administering a field station. If you think field stations are eternal, it may be a sign that you are very young, or you are very fortunate in working for an agency where moving forward is correctly labeled as progress. I have always thought that long-term field research stations were considered sacred but clearly not everyone agrees. Administrators must have something to do to leave their mark on the world for better or worse. All we can do is watch and be alert for emerging symptoms of collapse.

Swanson, F.J. (2015). Confluence of arts, humanities, and science at sites of long-term ecological inquiry. Ecosphere 6 (8), Article 132. doi: 10.1890/ES15-00139.1.

On the Meaning of ‘Food Limitation’ in Population Ecology

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There are many different ecological constraints that are collected in the literature under the umbrella of ‘food limitation’ when ecologists try to explain the causes of population changes or conservation problems. ‘Sockeye salmon in British Columbia are declining in abundance because of food limitation in the ocean’. ’Jackrabbits in some states in the western US are increasing because climate change has increased plant growth and thus removed the limitation of their plant food supplies.’ ‘Moose numbers in western Canada are declining because their food plants have shifted their chemistry to cope with the changing climate and now suffer food limitation”. My suggestion here is that ecologists should be careful in defining the meaning of ‘limitation’ in discussing these kinds of population changes in both rare and abundant species.

Perhaps the first principle is that it is the definition of life that food is always limiting. One does not need to do an experiment to demonstrate this truism. So to start we must agree that modern agriculture is built on the foundation that food can be improved and that this form of ‘food limitation’ is not what ecologists who are interested in population changes in the real world are trying to test. The key to explain population differences must come from resource differences in the broad sense, not food alone but a host of other ecological causal factors that may produce changes in birth and death rates in populations.

‘Limitation’ can be used in a spatial or a temporal context. Population density of deer mice can differ in average density in 2 different forest types, and this spatial problem would have to be investigated as a search for the several possible mechanisms that could be behind this observation. Often this is passed off too easily by saying that “resources” are limiting in the poorer habitat, but this statement takes us no closer to understanding what the exact food resources are. If food resources carefully defined are limiting density in the ‘poorer’ habitat, this would be a good example of food limitation in a spatial sense. By contrast if a single population is increasing in one year and declining in the next year, this could be an example of food limitation in a temporal sense.

The more difficult issue now becomes what evidence you have that food is limiting in either time or space. Growth in body size in vertebrates is one clear indirect indicator but we need to know exactly what food resources are limiting. The temptation is to use feeding experiments to test for food limitation (reviewed in Boutin 1990). Feeding experiments in the lab are simple, in the field not simple. Feeding an open population can lead to immigration and if your response variable is population density, you have an indirect effect of feeding. If animals in the experimentally fed area grow faster or have a higher reproductive output, you have evidence of the positive effect of the feeding treatment. You can then claim ‘food limitation’ for these specific variables. If population density increases on your feeding area relative to unfed controls, you can also claim ‘food limitation of density’. The problems then come when you consider the temporal dimension due to seasonal or annual effects. If the population density falls and you are still feeding in season 2 or year 2, then food limitation of density is absent, and the change must have been produced by higher mortality in season 2 or higher emigration.

Food resources could be limiting because of predator avoidance (Brown and Kotler 2007). The ecology of fear from predation has blossomed into a very large literature that explores the non-consumptive effects of predators on prey foraging that can lead to food limitation without food resources being in short supply (e.g., Peers et al. 2018, Allen et al. 2022).

All of this seems to be terribly obvious but the key point is that if you examine the literature about “food limitation” look at the evidence and the experimental design. Ecologists like medical doctors at times have a long list of explanations designed to sooth the soul without providing good evidence of what exact mechanism is operating. Economists are near the top with this distinguished approach, exceeded only by politicians, who have an even greater art in explaining changes after the fact with limited evidence.

As a footnote to defining this problem of food limitation, you should read Boutin (1990). I have also raved on about this topic in Chapter 8 of my 2013 book on rodent populations if you wish more details.

Allen, M.C., Clinchy, M. & Zanette, L.Y. (2022) Fear of predators in free-living wildlife reduces population growth over generations. Proceedings of the National Academy of Sciences (PNAS), 119, e2112404119. doi: 10.1073/pnas.2112404119.

Boutin, S. (1990). Food supplementation experiments with terrestrial vertebrates: patterns, problems, and the future. Canadian Journal of Zoology 68(2): 203-220. doi: 10.1139/z90-031.

Brown, J.S. & Kotler, B.P. (2007) Foraging and the ecology of fear. Foraging: Behaviour and Ecology (eds. D.W. Stephens, J.S. Brown & R.C. Ydenberg), pp. 437-448.University of Chicago Press, Chicago. ISBN: 9780226772646

Krebs, C.J. (2013) Chapter 8, The Food Hypothesis. In Population Fluctuations in Rodents. University of Chicago Press, Chicago. ISBN: 978-0-226-01035-9

On Climate Change Research Funding

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I have grown weary of media and news statements that climate change research should be a priority. At the present time military spending, war, and oil and gas companies seem to be the priority spending of many governments. Climate change research seems to be more focused on the physical sciences in attempts to predict what changes in temperature, rainfall, and sea conditions can be expected if we continue at the present global rates of greenhouse gas emissions. This is all very good, and the IPCC reports are excellent. The people are listening and reacting to the bad news even if all the major western governments are close to ignoring the problem. So where does this leave ecological scientists?

Our first response is that we should mimic the climatologists in predicting what the ecological world will be like in 2050 or 2100. But there is a major problem with this centered around the fact that physics has a whole set of fixed laws that will not change in a thousand years, so that the physics of the atmosphere and the oceans is reasonably understood and by the application of the laws of physics, we can arrive at a reasonable prediction that should be constrained by physical laws. Ecological science is nowhere near that paradigm of predictability because it deals with organisms that can evolve and interactions that can change rapidly when an unexpected invasive species arrives on the scene or humans interfere with ecosystem services. Ecological changes are not driven solely by climate change, a fact it is easy to forget. One consequence of this limitation is that we cannot make any kind of reliable predictions about the state of our ecosystems and the state of the Earth’s biodiversity by 2050 or 2100. We can however, in contrast to the physical sciences, do something about ecological changes by finding the limiting factors for the species under concern, protecting these endangered species and setting aside natural areas protected from human depredation. While we can do this to some extent in rich countries, in poor countries, particularly tropical ones, we have a poor record of protecting the exploitation of national parks and reserves. Think Brazil or the Central African Republic.

But given this protection of areas and funding for threatened species, conservation ecologists still have some very difficult problems to face. First and foremost is the conservation of rare, endangered species. It is nearly impossible to study rare species to discover the limiting factors that are pushing them toward extinction. Second, if you have the information on limiting factors, it is difficult to reverse trends that are determined by climate change or by human disrespect for conservation values.

In spite of these problems, the ecological literature is full of papers claiming to solve these issues with various schemes that predict a brighter future sometime. But if we apply the same rigor to these papers as we do to other areas of ecology, we must treat them as a set of hypotheses that make specific predictions, and try to test them. If we have solutions that are feasible but will require 50 years to accomplish, we should be very clear that we are drawing a long bow. Some statement of goals for the next 5 years would be desirable so we can measure progress or lack of progress.

The screams of practitioners go up – we have no time to test hypotheses, we need action! If we have clear-cut a forest site, or bulldozed shrub habitats, we may have a good idea of how to proceed to restoration. But with a long term view, restoration itself in highly contestable. In particular with climate change we have even less ability to predict with knowledge based on the last 50 year or so. So if you are in a predictive mode about conservation issues, have multiple working hypotheses about what to do, rather than one certain view of what will solve the problem.

This is not a cry to give up on conservation, but rather to trim our certainty about future states of ecosystems. Trying to predict what will happen under climate change is important for the Earth but we must always keep in mind the other critical factors affecting biodiversity, from predators to parasites and diseases, and the potential for evolution. Human destruction of habitats is a key issue we do not control well enough, and yet it may be the most important short term threat to conservation.

All of this leads into the fact that to achieve anything we need resources –people and money. The problem at present is where can we get the money? Governments in general place a low value on conservation and the environment in general in the quest for money and economic growth. Rich philanthropists are useful but few, and perhaps too often they have a distorted view of what to invest in. Improving the human condition of the poor is vital; medical research is vital, but if the environment suffers losses as it is at present, we need to balance or reverse our priorities of where to put our money. I do not know how to accomplish this goal. The search for politicians who have even a grade 1 understanding of environmental problems is not going well. Read Boris Johnson and Vladimir Putin. What is being accomplished now is more to the credit of private philanthropy which has clear goals but may pull in diverse directions. I submit that to date we have not been successful in this pursuit of environmental harmony, but it is a goal we must keep pushing for. E.O. Wilson once said that there was more money spent in New York City on a Friday night on beer than was devoted to biodiversity conservation for the entire world for the year.  This should hardly be a good epitaph for our century.

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).