Category Archives: Conservation Biology

How Much Evidence is Enough?

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The scientific community in general considers a conclusion about a problem resolved if there is enough evidence. There are many excellent books and papers that discuss what “enough evidence” means in terms of sampling design, experimental design, and statistical methods (Platt 1964, Shadish et al. 2002, Johnson 2002, and many others) so I will skip over these technical issues and discuss the nature of evidence we typically see in ecology and management.

An overall judgement one can make is that there is a great diversity among the different sciences about how much evidence is enough. If replication is expensive, typically fewer experiments are deemed sufficient. If human health is involved, as we see with Covid-19, many controlled experiments with massive replication is usually required. For fisheries and wildlife management much less evidence is typically quoted as sufficient. For much of conservation biology the problem arises that no experimental design can be considered if the species or taxa are threatened or endangered. In these cases we have to rely on a general background of accepted principles to guide our management actions. It is these cases that I want to focus on here.

Two guiding lights in the absence of convincing experiments are the Precautionary Principle and the Hippocratic Oath. The simple prescription of the Hippocratic Oath for medical doctors has always been “Do no harm”. The Precautionary Principle has been spread more widely and has various interpretations, most simply “Look before you leap” (Akins et al. 2019). But if applied too strictly some would argue, this principle might stop “green” projects that are in themselves directed toward sustainability. Wind turbine tower effects on birds are one example (Coppes et al. 2020). The conservation of wild bees may impact current agricultural production positively (Drossart and Gerard 2020) or negatively depending on the details of the conservation practices. Trade offs are a killer for many conservation solutions, jobs vs. the environment.

Many decisions about conservation action and wildlife management rest on less than solid empirical evidence. This observation could be tested in any graduate seminar by dissecting a series of papers on explicit conservation problems. Typically, those cases involving declining large bodied species like caribou or northern spotted owls or tigers are affected by a host of interconnected problems involving human usurpation of habitats for forestry, agriculture, or cities, backed up by poaching or direct climate change due to air pollution, or diseases introduced by domestic animals or introduced species. In some fraction of cases the primary cause of decline is well documented but cannot be changed by conservation biologists (e.g. CO2 and coral bleaching). 

Nichols et al. (2019) recommend a model-based approach to answering conservation and management questions as a way to increase the rate of learning about which set of hypotheses best predict ecological changes. The only problem with their approach is the time scale of learning, which for immediate conservation issues may be limiting. But for problems that have a longer time scale for hypothesis testing and decision making they have laid out an important pathway to problem solutions.

In many ecological and conservation publications we are allowed to suggest weak hypotheses for the explanation of pest outbreaks or population declines, and in the worst cases rely on “correlation = causation” arguments. This will not be a problem if we explicitly recognize weak hypotheses and specify a clear path to more rigorous hypotheses and experimental tests. Climate change is the current panchrestron or universal explanation because it shows weak associations with many ecological changes. There is no problem with invoking climate change as an explanatory variable if there are clear biological mechanisms linking this cause to population or community changes.

All of this has been said many times in the conservation and wildlife management literature, but I think needs continual reinforcement. Ask yourself: Is this evidence strong enough to support this conclusion? Weak conclusions are perhaps useful at the start of an investigation but are not a good basis for conservation or wildlife management decision making. Ensuring that our scientific conclusions “Do no harm” is a good principle for ecology as well as medicine.

Akins, A., et al. (2019). The Precautionary Principle in the international arena. Sustainability 11 (8), 2357. doi: 10.3390/su11082357.

Coppes, J., et al. (2020). The impact of wind energy facilities on grouse: a systematic review. Journal of Ornithology 161, 1-15. doi: 10.1007/s10336-019-01696-1.

Drossart, M. and Gerard, M. (2020). Beyond the decline of wild bees: Optimizing conservation measures and bringing together the actors. Insects (Basel, Switzerland) 11, 649. doi: 10.3390/insects11090649.

Johnson, D.H. (2002). The importance of replication in wildlife research. Journal of Wildlife Management 66, 919-932.

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.

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

Shadish, W.R, Cook, T.D., and Campbell, D.T. (2002) ‘Experimental and Quasi-Experimental Designs for Generalized Causal Inference.‘ (Houghton Mifflin Company: New York.)

But It is Complicated in Ecology

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Consider two young ecologists both applying for the same position in a university or an NGO. To avoid a legal challenge, I will call one Ecologist C (as short for “conservative”), and the second candidate Ecologist L (as short for “liberal”). Both have just published reviews of conservation ecology. Person L has stated very clearly that the biological world is in rapid, catastrophic collapse with much unrecoverable extinction on the immediate calendar, and that this calls for emergency large-scale funding and action. Person C has reviewed similar parts of the biological world and concluded that some groups of animals and plants are of great concern, but that many other groups show no strong signals of collapse or that the existing data are inadequate to decide if populations are declining or not. Which person will get the job and why?

There is no answer to this hypothetical question, but it is worth pondering the potential reasons for these rather different perceptions of the conservation biology world. First, it is clear that candidate L’s catastrophic statements will be on the front page of the New York Times tomorrow, while much less publicity will accrue to candidate C’s statements. This is a natural response to the ‘This Is It!” approach so much admired by thrill seekers in contrast to the “Maybe Yes, Maybe No”, and “It Is Complicated” approach. But rather than get into a discussion of personality types, it may be useful to dig a bit deeper into what this question reveals about contemporary conservation ecology.

Good scientists attempting to answer this dichotomy of opinion in conservation ecology would seek data on several questions.
(1) Are there sufficient data available to reach a conclusion on this important topic?
(2) If there are not sufficient data, should we err on the side of being careful about our conclusion and risk “crying wolf”?
(3) Can we agree on what types of data are needed and admissible in this discussion?

On all these simple questions ecologists will argue very strongly. For question (1) we might assume that a 20-year study of a dominant species might be sufficient to determine trend (e.g. Plaza and Lambertucci 2020). Others will be happy with 5 years of data on several species. Can we substitute space for time? Can we simply use genetic data to answer all conservation questions (Hoffmann et al. 2017)? If the habitat we are studying contains 75 species of plants or invertebrates, on how many species must we have accurate data to support Ecologist L? Or do we need any data at all if we are convinced about climate change? Alfonzetti et al, (2020) and Wang et al. (2020) give two good examples of data problems with plants and butterflies with respect to conservation status. 

For question (2) there will be much more disagreement because this is not about the science involved but is a personal judgement about the future consequences of projected trends in species numbers. These judgements are typically based loosely on past observations of similar ecological populations or communities, some of which have declined in abundance and disappeared (the Passenger Pigeon Paradigm) or conversely those species that have recovered from minimal abundance to become common again (the Kirtland’s Warbler Paradigm). The problem revolves back to the question of what are ‘sufficient data’ to decide conservation policies.

Fortunately, most policy-oriented NGO conservation groups concentrate on the larger conservation issues of finding and protecting large areas of habitat from development and pushing strongly for policies that rein in climate change and reduce pollution produced by poor business and government practices.

In the current political and social climate, I suspect Ecologist L would get the job rather than Ecologist C. I can think of only one university hiring in my career that was sealed by a very assured candidate like person L who said to the departmental head and the search committee “Hire me and I will put this university on the MAP!”. We decided in this case we did not want to be on that particular MAP.

At present you can see all these questions are common in any science dealing with an urgent problem, as illustrated by the Covid-19 pandemic discussions, although much more money is being thrown at that disease issue than we ever expect to see for conservation or ecological science in general. It really is complicated in all science that is important to us.

Alfonzetti, M., et al. (2020). Shortfalls in extinction risk assessments for plants. Australian Journal of Botany 68, 466-471. doi: 10.1071/BT20106.

Hoffmann, A.A., Sgro, C.M., and Kristensen, T.N. (2017). Revisiting adaptive potential, population size, and conservation. Trends in Ecology & Evolution 32, 506-517. doi: 10.1016/j.tree.2017.03.012.

Plaza, P.I. and Lambertucci, S.A. (2020). Ecology and conservation of a rare species: What do we know and what may we do to preserve Andean condors? Biological Conservation 251, 108782. doi: 10.1016/j.biocon.2020.108782.

Wang, W.-L., Suman, D.O., Zhang, H.-H., Xu, Z.-B., Ma, F.-Z., and Hu, S.-J. (2020). Butterfly conservation in China: From science to action. Insects (Basel, Switzerland) 11, 661. doi: 10.3390/insects11100661.

How should biodiversity research be directed?

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There are many scientific papers and news reports currently that state that biodiversity is in rapid decline on Earth. No evidence is usually cited for this statement – it is considered to be self evident. What follows from that is typically a panic request for more work on declining populations, more money for conservation NGOs and national parks. Political ecology statements that request more money for ecological research are certainly on the right track if we are to understand how to achieve conservation of our biota. But the question I want to raise here is how to proceed on this broad issue in a logical manner. To do this I will not discuss political ecology or how to gain more donors for conservation agencies, valuable services to be sure. But behind all this advertising is a scientific agenda which needs careful consideration.    

Problem #1 is to determine if there is a problem. In some areas of conservation ecology there is much agreement on principles – we all agree that we are losing natural areas for urban and agricultural development, that we need more protected areas, that most protected areas are not large enough, that there are serious problems with poaching of wildlife and lumber in some protected areas, and that global pollution is affecting much of our biodiversity. In other areas of conservation ecology there is much controversy about details. Is global biodiversity in rapid decline (Vellend et al. 2017, Cardinale et al. 2018)? How can we best identify species at risk, and once we identify them, what can we do to prevent population collapse?

The answer to Problem #1 is that there are problems in some areas but not in others, in some taxonomic groups, but not in others, but overall the data are completely inadequate for a clear statement that overall biodiversity is in global decline (Dornelas et al. 2019). The problems of biodiversity conservation are local and group specific, which leads us to Problem #2.

Problem # 2 is to go back to the ecological details, concentrating on local and specific problems, exactly what should we do, and what can we do? The problems here relate almost entirely to ecological methods – how do we estimate species abundances particularly for rare species? How do we deal with year to year changes in communities? How long should a monitoring program continue until it has reliable conclusions about biodiversity change? None of these questions are simple to answer and require much discussion which is currently under way. How long is a long-term study? It might be something like 30 generations for vertebrate species or even longer, but what is it for earthworms or bark beetles? How can we best sample the variety of insects in an ecosystem in which they might be in decline (Habel et al. 2019)?

We need to scale our conservation studies for particular species, and this has led us into the Species-At-Risk dilemma. We can gather data for a specific geographical area like Canada on the species that we deem at risk. Typically, these are vertebrates, and we ignore the insects, microbes, and the rest of the community. We try to identify threatening processes for each species and write a detailed report (Bird and Hodges 2017). The action plan specified can rarely be carried out because it is multi-year and expensive, so the matter rests. For many of these species at risk and for almost all that are ignored the central problem is action – what could you do about a declining species-at-risk, given funds and person-power? We do what we can on a local scale on the principle that it is better to do something than nothing (Westwood et al. 2019). But too often even if we have a good ecological understanding of declines, for example in mountain caribou in Canada, little or nothing is done (Palm et al. 2020). Conservation collides with economics.

I will try to draw a few possible conclusions out of this general discussion.

  1. It is far from clear that global biodiversity is declining rapidly.
  2. On a local level we can do careful evaluations for some species at risk and take possible action if funding is available.
  3. Setting aside large areas of habitat is currently the best immediate conservation strategy. Managing land use is critical.
  4. Designing strong monitoring programs is essential to discover population and community trends so that, if action can be taken, it is not too late.
  5. Climate change will have profound biodiversity effects in the long run, and conservation scientists must work short-term but plan long-term.

As we take actions for conservation, we ought to keep in mind the central question: What will this ecosystem look like in 100 or 200 years? Perhaps that could be a t-shirt slogan.

Bird, S.C., and Hodges, K.E. (2017). Critical habitat designation for Canadian listed species: Slow, biased, and incomplete. Environmental Science & Policy 71, 1-8. doi: 10.1016/j.envsci.2017.01.007.

Cardinale, B.J., Gonzalez, A., Allington, G.R.H., and Loreau, M. (2018). Is local biodiversity declining or not? A summary of the debate over analysis of species richness time trends. Biological Conservation 219, 175-183. doi: 10.1016/j.biocon.2017.12.021.

Dornelas, M., Gotelli, N.J., Shimadzu, H., Moyes, F., Magurran, A.E., and McGill, B.J. (2019). A balance of winners and losers in the Anthropocene. Ecology Letters 22, 847-854. doi: 10.1111/ele.13242.

Habel, J.C., Samways, M.J., and Schmitt, T. (2019). Mitigating the precipitous decline of terrestrial European insects: Requirements for a new strategy. Biodiversity and Conservation 28, 1343-1360. doi: 10.1007/s10531-019-01741-8.

Palm, E.C., Fluker, S., Nesbitt, H.K., Jacob, A.L., and Hebblewhite, M. (2020). The long road to protecting critical habitat for species at risk: The case of southern mountain woodland caribou. Conservation Science and Practice 2 (7). doi: 10.1111/csp2.219.

Vellend, M., Dornelas, M., Baeten, L., Beauséjour, R., Brown, C.D., De Frenne, P., Elmendorf, S.C., et. al. (2017). Estimates of local biodiversity change over time stand up to scrutiny. Ecology 98, 583-590. doi: 10.1002/ecy.1660.

Westwood, A.R., Otto, S.P., Mooers, A., Darimont, C., Hodges, K.E., Johnson, C., Starzomski, B. et al. (2019). Protecting biodiversity in British Columbia: Recommendations for developing species at risk legislation. FACETS 4, 136-160. doi: 10.1139/facets-2018-0042.

How Should We Test Global Models in Ecology?

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There is an understandable desire to view ecological ideas on an exceptionally large or even global scale. Just as physicists, chemists, and engineers apply their scientific results as correct everywhere, biologists would like to have global hypotheses and global models of ecological principles. There is only one problem – that ecological principles or ‘laws’ are climate contingent. This simple fact has produced a minor mode of panic in the ecological literature. How reliable are our ecological principles? Must we change them as the climate changes? In principle not, since many chemical and physical laws are temperature dependent or moisture dependent, and we just recognize that these laws have a temperature or moisture parameter as part and parcel of how things like chemical reactions can change.

This kind of argument would suggest that if we build the physical-chemical universe into our ecological models we could approach the hard sciences in predictive precision. Alas as we know this is not to be. Why not? The first argument is that ecological systems are composed of many variables – all individuals in a population are not identical, communities and ecosystems contain many interacting species with different physical and chemical requirements. But this does not necessarily let ecologists off the hook because it can be interpreted to mean that we simply have a much harder job to do and it will take much longer but it is in principle achievable. The second argument is that evolution continues to occur and is in principle unpredictable, so that while we know where we are at present, we do not know the future (Ivory et al. 2019).

Let us take a global example of the decline in coral reefs as temperature in the ocean rises. We will ignore for the moment CO2 acidity changes to keep the discussion simple. We can define closely the thermal limits of different coral species, so that should give us good predictability. But we do not know if natural selection will change these thermal limits, or whether or not it can do so rapidly enough. For the most part we project that increasing ocean temperatures will destroy most of our coral reefs and turn them into algal communities. This prediction is partly based on observations of the last 40 years in different parts of the tropics and partly based on measurements in physiological ecology in the lab. But the elephant in the prediction room is evolution and what genetic variation now exists but has not been measured, as well as how far temperature and CO2 will increase (Frank 2019).  

So ecologists are caught in a dilemma – we can in principle define the current state of ecosystems and make short term predictions that we can test with further monitoring, but we cannot make the long term predictions everyone wants to have. As conservation biologists we can make warnings but few of them would stand up in court when push comes to shove. So the consequence is that we live in a world of make believe where, for example in British Columbia the government in its wisdom says yes we must protect old growth forests, and we will do all possible to achieve this goal, as long as new policies do not reduce the annual allowable cut to the forest industry.

We can look to paleoecology to get an overview of how life on Earth has changed in the past on any time scale you wish. If there is a general law coming out of all this research it is that when climate changes, ecological communities and ecosystems change. The simple message that is hard to get across is that, if you like current environmental conditions and desire only small changes in our present ecological communities, it is desirable to reduce the pollution that is causing rapid climate change. No clever and detailed global ecological model will help us overcome the tragedies unfolding with the business as usual models we currently use unless we control rapid climate change (van der Zande et al. 2020). A current popular example is the suggestion that if we plant trees around the world, we can reverse rising CO2 level. That sounds like a good achievable plan but in fact it is impossible (Friedlingstein et al. 2019).

So, my advice is two-fold. First, design and test global ecological models for short term understanding and predictions. Do not pretend they will provide accurate long-term predictions for ecological systems. In some cases, there is little predictability (Geary et al. 2020). Second, do much more long-term monitoring of communities and ecosystems to trace local and global changes quantitatively (Wagner 2020). Then at least we will know how big the ‘wolf’ is before we ‘cry wolf’. 

Frank, P. (2019). Propagation of error and the reliability of global air temperature projections. Frontiers in Earth Science 7, 223. doi: 10.3389/feart.2019.00223.

Friedlingstein, P., Allen, M., Canadell, J.G., Peters, G.P., and Seneviratne, S.I. (2019). Comment on “The global tree restoration potential”. Science 366, eaay8060. doi: 10.1126/science.aay8060.

Geary, W.L., Doherty, T.S., Nimmo, D.G., Tulloch, A.I.T., and Ritchie, E.G. (2020). Predator responses to fire: A global systematic review and meta-analysis. Journal of Animal Ecology 89, 955-971. doi: 10.1111/1365-2656.13153.

Ivory, S. J., Russell, J., Early, R., and Sax, D.F. (2019). Broader niches revealed by fossil data do not reduce estimates of range loss and fragmentation of African montane trees. Global Ecology and Biogeography 28, 992-1003. doi: 10.1111/geb.12909.

van der Zande, R.M., Achlatis, M., Bender-Champ, D., Kubicek, A., and Dove, S. (2020). Paradise lost: End-of-century warming and acidification under business-as-usual emissions have severe consequences for symbiotic corals. Global Change Biology 26, 2203-2219. doi: 10.1111/gcb.14998.

Wagner, D.L. (2020). Insect declines in the Anthropocene. Annual Review of Entomology 65, 457-480. doi: 10.1146/annurev-ento-011019-025151.

On Three Kinds of Ecology Papers

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There are many possible types of papers that discuss ecology, and in particular I want to deal only with empirical studies that deal with terrestrial and aquatic populations, communities, or ecosystems. I will not discuss here theoretical studies or modelling studies. I suggest it is possible to classify papers in ecological science journals that deal with field studies into three categories which I will call Descriptive Ecology, Explanatory Ecology, and Experimental Ecology. Papers in all these categories deal with a description of some aspects of the ecological world and how it works but they differ in their scientific impact.

Descriptive Ecology publications are essential to ecological science because they present some details of the natural history of an ecological population or community that is vital to our growing understanding of the biota of the Earth. There is much literature in this group, and ecologists all have piles of books on the local natural history of birds, moths, turtles, and large mammals, to mention only a few. Fauna and flora compilations pull much of this information together to guide beginning students and the interested public in increased knowledge of local fauna and flora. These publications are extremely valuable because they form the natural history basis of our science, and greatly outnumber the other two categories of papers. The importance of this information has been a continuous message of ecologists over many years (e.g. Bartholomew 1986; Dayton 2003; Travis 2020).

The scientific journals that professional ecologists read are mostly concerned with papers that can be classified as Explanatory Ecology and Experimental Ecology. In a broad sense these two categories can be described as providing a good story to tie together and thus explain the known facts of natural history or alternatively to define a set of hypotheses that provide alternative explanations for these facts and then to test these hypotheses experimentally. Rigorous ecology like all good science proceeds from the explanatory phase to the experimental phase. Good natural history provides several possible explanations for ecological events but does not stop there. If a particular bird population is declining, we need first to make a guess from natural history if this decline might be from disease, habitat loss, or predation. But to proceed to successful management of this conservation problem, we need studies that distinguish the cause(s) of our ecological problems, as recognized by Caughley (1994) and emphasized by Hone et al. (2018). Consequently the flow in all the sciences is from descriptive studies to explanatory ideas to experimental validation. Without experimental validation ‘ecological ideas’ can transform into ‘ecological opinions’ to the detriment of our science. This is not a new view of scientific method (Popper 1963) but it does need to be repeated (Betini et al. 2017). 

If I repeat this too much, I suggest you do a survey of how often ecological papers in your favorite journal are published without ever using the word ‘hypothesis’ or ‘experiment’. A historical survey of these or similar words would be a worthwhile endeavour for an honours or M.Sc. student in any one of the ecological subdisciplines. The favourite explanation offered in many current papers is climate change, a particularly difficult hypothesis to test because, if it is specified vaguely enough, it is impossible to test experimentally. Telling interesting stories should not be confused with rigorous experimental ecology.

Bartholomew, G. A. (1986). The role of natural history in comtemporary biology. BioScience 36, 324-329. doi: 10.2307/1310237

Betini, G.S., Avgar, T., and Fryxell, John M. (2017). Why are we not evaluating multiple competing hypotheses in ecology and evolution? Royal Society Open Science 4, 160756. doi: 10.1098/rsos.160756.

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

Dayton, P.K. (2003). The importance of the natural sciences to conservation. American Naturalist 162, 1-13. doi: 10.1086/376572

Hone, J., Drake, Alistair, and Krebs, C.J. (2018). Evaluating wildlife management by using principles of applied ecology: case studies and implications. Wildlife Research 45, 436-445. doi: 10.1071/WR18006.

Popper, K. R. (1963) ‘Conjectures and Refutations: The Growth of Scientific Knowledge.’ (Routledge and Kegan Paul: London.)

Travis, Joseph (2020). Where is natural history in ecological, evolutionary, and behavioral science? American Naturalist 196, 1-8. doi: 10.1086/708765.

On Ecological Models and the Coronavirus

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We are caught up now in a coronavirus pandemic with an unknown end point. There is a great deal now available about COVID-19, and I want to concentrate on the models of this pandemic that currently fill our media channels. In particular I want to use the current situation to reflect on the role of mathematical models in helping to solve ecological problems and make predictions of future trends. To oversimplify greatly, the scientific world is aligned along an axis from those supporting simple models to those tied up in complex multifactor models. To make this specific, the simple epidemic model approach provides us with a coronavirus model that has three classes of actors – susceptible, infected, and recovered individuals, and one key parameter, the relative infection rate of one person to another. If you as an infected person pass on the disease to more than one additional person, the pandemic will grow. If you pass the disease on to less than one person (on average), the pandemic will collapse. Social distancing will flip us into the favourable state of declining infections. There is a similar sort of model in ecology for predator-prey interactions, called the Lotka-Volterra model, in which one predator eating one prey species will change the population size of both depending on the rate of killing of the predator and the rate of reproduction of the prey.

So far so good. We can all have an intuitive understanding of such simple models, but of course the critics rise up in horror with the cry that “the devil is in the details”. And indeed this is also a universal truth. All humans are not equally affected by COVID-19. Older people do poorly, young children appear to be little bothered by the virus. All prey individuals in nature are also not equally susceptible to being caught by a predator. Young prey may not run as fast as adults, poorly fed prey in winter may run more slowly than well fed animals. The consequences of this ‘inequality’ is what leads to the need for an increasing investment in scientific research. We can pretend the world is simple and the virus will just “go away”, and a simple view of predation that “larger animals eat smaller animals” could fail to recognize that a small predator might drive a dinosaur species extinct if the small predator eats only the eggs of the prey and avoids the big adults. The world is complicated, and that is what makes it both interesting to many and infuriating to some who demand simplicity.

One of the purposes of a mathematical model is to allow predictions of coming events, and we hear much of this with the COVID-19 models currently in circulation. A simple principle is “all models are wrong’ but this must be matched with the corollary that in general “the simpler the model the more likely it is to provide poor forecasts. But there is a corollary that might be called the “Carl Walters’ Law” that there is some optimal level of complexity for a good result, and too much complexity is also a recipe for poor projections. The difficulty is that we can often only find this optimal point after the fact, so that we learn by doing. This does not sit well with politicians and business-people who demand “PRECISE PRECISION PROMPTLY!” 

These uncertainties reflect on to our current decision making in the coronavirus pandemic, in issues to fight climate change, and in the conservation of threatened species and ecosystems. Our models, our scientific understanding, and our decisions are never perfect or complete, and as we see so clearly with COVID-19 the science in particular can be pushed but cannot be rushed, even when money is not limiting. The combination of planning, judgement and knowledge that we call wisdom may come more slowly than we wish. Meanwhile there are many details that need investigation.  

Adam, D. (2020) Modelling the Pandemic: The simulations driving the world’s response to COVID-19. Nature, 580, 316-318. Doi: 10.1038/d41586-020-01003-6 

Neher, R.A., Dyrdak, R., Druelle, V., Hodcroft, E.B. & Albert, J. (2020) Potential impact of seasonal forcing on a SARS-CoV-2 pandemic. Swiss Medical Weekly 150, w20224. Doi: 10.4414/smw.2020.20224.

Xu, B., Cai, J., He, D., Chowell, G. & Xu, B. (2020) Mechanistic modelling of multiple waves in an influenza epidemic or pandemic. Journal of Theoretical Biology, 486, 110070. Doi: 10.1016/j.jtbi.2019.110070.

On Declining Bird Populations

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The conservation literature and the media are alive with cries of declining bird populations around the world (Rosenberg et al. 2019). Birds are well liked by people, and an important part of our environment so they garner a lot of attention when the cry goes out that all is not well. The problems from a scientific perspective is what evidence is required to “cry wolf’. There are many different opinions on what data provide reliable evidence. There is a splendid critique of the Rosenberg et al paper by Brian McGill that you should read::
https://dynamicecology.wordpress.com/2019/09/20/did-north-america-really-lose-3-billion-birds-what-does-it-mean/

My object here is to add a comment from the viewpoint of population ecology. It might be useful for bird ecologists to have a brief overview of what ecological evidence is required to decide that a bird population or a bird species or a whole group of birds is threatened or endangered. One simple way to make this decision is with a verbal flow chart and I offer here one example of how to proceed.

  1. Get accurate and precise data on the populations of interest. If you claim a population is declining or endangered, you need to define the population and know its abundance over a reasonable time period.

Note that this is already a nearly impossible demand. For birds that are continuously resident it is possible to census them well. Let me guess that continuous residency occurs in at most 5% or fewer of the birds of the world. The other birds we would like to protect are global or local migrants or move unpredictably in search of food resources, so it is difficult to define a population and determine if the population as a whole is rising or falling. Compounding all this are the truly rare bird species that are difficult to census like all rare species. Dorey and Walker (2018) examine these concerns for Canada.

The next problem is what is a reasonable time period for the census data. The Committee on the Status of Endangered Wildlife in Canada (COSEWIC) gives 10 years or 3 generations, whichever is longer (see web link below). So now we need to know the generation time of the species of concern. We can make a guess at generation time but let us stick with 10 years for the moment. For how many bird species in Canada do we have 10 years of accurate population estimates?

  • Next, we need to determine the causes of the decline if we wish to instigate management actions. Populations decline because of a falling reproductive rate, increasing death rate, or higher emigration rates. There are very few birds for which we have 10 years of diagnosis for the causes of changes in these vital rates. Strong conclusions should not rest on weak data.

The absence of much of these required data force conservation biologists to guess about what is driving numbers down, knowing only that population numbers are falling. Typically, many things are happening over the 10 years of assessment – climate is changing, habitats are being lost or gained, invasive species are spreading, new toxic chemical are being used for pest control, diseases are appearing, the list is long. We have little time or money to determine the critical limiting factors. We can only make a guess.

  • At this stage we must specify an action plan to recommend management actions for the recovery of the declining bird population. Management actions are limited. We cannot in the short term alter climate. Regulating toxic chemical use in agriculture takes years. In a few cases we can set aside more habitat as a generalized solution for all declining birds. We have difficulty controlling invasive species, and some invasive species might be native species expanding their geographic range (e.g. Bodine and Capaldi 2017, Thibault et al. 2018).

Conservation ecologists are now up against the wall because all management actions that are recommended will cost money and will face potential opposition from some people. Success is not guaranteed because most of the data available are inadequate. Medical doctors face the same problem with rare diseases and uncertain treatments when deciding how to treat patients with no certainty of success.

In my opinion the data on which the present concern over bird losses is too poor to justify the hyper-publicity about declining birds. I realize most conservation biologists will disagree but that is why I think we need to lift our game by having a more rigorous set of data rules for categories of concern in conservation. A more balanced tone of concern may be more useful in gathering public support for management efforts. Stanton et al. (2018) provide a good example for farmland birds. Overuse of the word ‘extinction’ is counterproductive in my opinion. Trying to provide better data is highly desirable so that conservation papers do not always end with the statement ‘but detailed mechanistic studies are lacking’. Pleas for declining populations ought to be balanced by recommendations for solutions to the problem. Local solutions are most useful, global solutions are critical in the long run but given current global governance are too much fairy tales.

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

Dorey, K. and Walker, T.R. (2018). Limitations of threatened species lists in Canada: A federal and provincial perspective. Biological Conservation 217, 259-268. doi: 10.1016/j.biocon.2017.11.018.

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

Stanton, R.L., Morrissey, C.A., and Clark, R.G. (2018). Analysis of trends and agricultural drivers of farmland bird declines in North America: A review. Agriculture, Ecosystems & Environment 254, 244-254. doi: 10.1016/j.agee.2017.11.028.

Thibault, M., et al. (2018). The invasive Red-vented bulbul (Pycnonotus cafer) outcompetes native birds in a tropical biodiversity hotspot. PLoS ONE 13, e0192249. doi: 10.1371/journal.pone.0192249.

http://cosewic.ca/index.php/en-ca/assessment-process/wildlife-species-assessment-process-categories-guidelines/quantitative-criteria

On Salmon Hatcheries as an Ecological Paradigm

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The West Coast of North America hosts 5 species of Pacific salmon that are an invaluable fishery resource and at least in theory a resource that is completely sustainable. The management of these fisheries provides a useful case study in how humans currently approach major resources, the mistakes they make, and how attempts to fix mistakes can lead to even further mistakes.

Salmon have been a major resource utilized by the First Nations of the Pacific Coast after the glaciers melted some 10-12,000 years ago. Salmon are anadromous fish, living in the ocean and spawning in fresh water. Their populations fluctuate from year to year but until the 1900s they were essentially considered an inexhaustible resource and thus became a target for exploitation. The buildup of salmon fisheries during the last 100 years coincided with an increase in environmental damage to freshwater spawning grounds. Dams on rivers cut migration routes to spawning grounds, pollution arising from mining, and erosion from forestry and agriculture all began to cut into spawning habitat and subsequently the available catch for the fishery. Salmon catches began to decline and in the late 1800s hatcheries began to be built both to restore fish stocks that were threatened and to increase the abundance of desirable fish like salmon (Naish et al 2007).

The simple model of salmon hatcheries was that the abundance of juvenile fish was the main factor limiting the adult population, so that adding more juveniles to wild juveniles moving out into the ocean would be profitable. This view of the world I call the “Farmer Paradigm” and if you are a dairy farmer with 4 cows that produce X milk, if you add 4 more cows to your farm, you now get 2X milk and thus more profit. But it became apparent with fish hatcheries that adding more juvenile fish did not necessarily increase the resulting fish catch. Some simple reasons might be that more juveniles were eaten by the predators waiting at the mouth of the river or stream, so that predation on juvenile fish was limiting. Alternatively, perhaps the ocean only had a given amount of food for juvenile growth, so that adding too many juveniles induced starvation deaths. Other explanations involving disease transmission could also be invoked.

Whatever the mechanism, it became clear that hatcheries for salmon sometimes worked and sometimes did not work to increase the productivity of the fishery. The Farmer Paradigm had to add a footnote to say “its complicated”. One complication noted early on was the possibility that natural selection in hatcheries was not equivalent to natural selection in wild populations. If hatchery fish were replacing wild fish in any population, the genetic changes involved could work in two directions by either making the entire population more fit or less fit, more productive or less. Much depends on what traits are selected for in hatcheries. In one example for sockeye salmon in Washington State, hatcheries appear to have selected for earlier spawning, so that wild sockeye in one river system return to spawn later than hatchery raised sockeye raised in the same river (Tillotson et al. 2019). Since in general juveniles from early spawners have poorer survival, climate change could favour earlier breeding and thereby reduce the overall productivity of the sockeye population in the river system. We are far from knowing the long-term selection that is occurring in hatcheries, and what it means for future populations of salmon (Cline et al. 2019, Stevenson et al. 2019).

Hatcheries are popular with the public because they indicate the government is doing something to assist fishers and hatcheries should increase and maintain fisheries production for species we love to eat. Consequently, there is a social signal that might be suppressed in data that might suggest a particular hatchery was in fact harming the fishery for a particular river or lake system. If someone wishes to do an economic analysis of the costs and benefits of a hatchery, one runs up against the standard simple belief that more juvenile fish equals higher fishery production. When Amoroso et al. (2017) tried to evaluate for pink salmon in Alaska whether hatcheries were an economic benefit or a loss, their best analysis suggested that recent increases in pink salmon productivity were higher in areas of Alaska with no hatcheries, compared with those with hatcheries. Since different river populations of pink salmon mix in their oceanic phase, it is difficult to obtain a clear experimental signal of hatchery success or failure. The immediate and the longer-term unintended consequences of hatcheries require further study. The assumption that every hatchery is an ecological and social good cannot be presumed.  

Salmon hatcheries are for me an ecological paradigm because they illustrate the management sequence: unlimited abundance → overharvesting → collapse of resource → find a technological fix → misdiagnosed problem → failure of technological fix → better diagnosis of the problem → competing socio-economic objectives → failure to act → collapse of the resource. This need not be the case, and we need to do better (Bendriem et al. 2019).

Amoroso, R.O. et al. (2017). Measuring the net biological impact of fisheries enhancement: Pink salmon hatcheries can increase yield, but with apparent costs to wild populations. Canadian Journal of Fisheries and Aquatic Sciences 74, 1233-1242. doi: 10.1139/cjfas-2016-0334.

Bendriem, N. et al. (2019). A review of the fate of southern British Columbia coho salmon over time. Fisheries Research 218, 10-21. doi: 10.1016/j.fishres.2019.04.002.

Cline, T.J. et al. (2019). Effects of warming climate and competition in the ocean for life-histories of Pacific salmon. Nature Ecology & Evolution 3, 935-942. doi: 10.1038/s41559-019-0901-7.

Naish, K.A. et al. (2007). An evaluation of the effects of conservation and fishery enhancement hatcheries on wild populations of salmon. Advances in Marine Biology 53, 61-194. doi: 10.1016/S0065-2881(07)53002-6.

Stevenson, C.F. et al. (2019). The influence of smolt age on freshwater and early marine behavior and survival of migrating juvenile sockeye salmon. Transactions of the American Fisheries Society 148, 636-651. doi: 10.1002/tafs.10156.

Tillotson, M.D. et al. (2019). Artificial selection on reproductive timing in hatchery salmon drives a phenological shift and potential maladaptation to climate change. Evolutionary Applications 12, 1344-1359. doi: 10.1111/eva.12730.

Do We Need Commissioners for the Environment?

Canada has just gone through an election, the USA will next year, and elections are a recurring news item everywhere. In our Canadian election we were spared any news on the state of the environment, and the dominant theme of the election was jobs, the economy, oil, gas, and a bit on climate change. The simplest theme was climate change, and yes, we are all in favour of stopping it so long as we do not need to do anything about it that would cost money or change our lifestyles. Meanwhile the fires of California and Australia and elsewhere carry on, generating another news cycle of crazy comments about the state of the environment.

Is there a better way? How can we get governments of the world to consider that the environment is worthy of some discussion? There is, and New Zealand has led the way in one direction. New Zealand has a Parliamentary Commissioner for the Environment, an independent Officer of Parliament, whose job it is to provide Members of Parliament with independent advice on matters that may have impacts on the environment. The Office is independent of the government of the day and the Prime Minister, and consequently can “tell it like it is”. A few quotations for the 2019 report give the flavour of this recent New Zealand report:

“If there is one thing that stands out from [our] reports, it is the extent of what we don’t know about what’s going on with our environment.  

“…the blind spots in our environmental reporting system don’t represent conscious choices to collect data or undertake research in some fields rather than others. Rather, they represent the unplanned consequences of a myriad choices over decades. Ours has been a passive system that has harvested whatever data is there and done the best it can to navigate what’s missing.

“In some ways, the most important recommendations in this report are those that relate to the prioritising and gathering of data in a consistent way. Despite attempts over more than two decades, no agreement has ever been reached on a set of core environmental indicators. This has to happen. Consistent and authoritative time series coupled with improved spatial coverage are essential if we are to detect trends. Only then will we be able to judge confidently whether we are making progress or going backwards – and get a handle on whether costly interventions are having an effect.

https://www.pce.parliament.nz/publications/focusing-aotearoa-new-zealand-s-environmental-reporting-system

This report is full of ecological wisdom and would be a useful starting point for many countries. Canada has (to my knowledge) no Environmental Commissioner and although various provinces and cities provide State of the Environment Reports, they are largely based on inadequate data. In some cases, like commercial fisheries, Parliaments or Congress have mandated annual reports, provided the secure funding, and retained independence of the relevant director and staff. In many cases there is far too much bickering between jurisdictions, use of inadequate methods of data collecting, long time periods between sampling, and no indication that the national interest has been taken into account.

Most Western countries have National Academies or Royal Societies which provide some scientific advice, sometimes requested, sometimes not. But these scientific publications are typically on very specific topics like smoking and lung cancer, vaccine protection, or automobile safety requirements. We can see this problem most clearly in the current climate emergency. The Intergovernmental Panel on Climate Change (IPCC) of the United Nations provides excellent reports on the climate emergency but no government is required to listen to their recommendations or to implement them. So, we have local problems, regional problems and global problems, and we need the political structures to address environmental problems at all these levels. New Zealand has provided a way forward, and here is another quote from the 2019 report that ecologists should echo:

Given that many of the environmental problems we face have been decades in the making and that for nearly 30 years we have [made] specific reference to cumulative effects that arise over time…it is astonishing that we have so little data on trends over time.

….it takes time to assemble time series. If we start collecting data today, it may be a decade or more before we can confidently judge whether the issue being monitored is getting better or worse. Every year that we delay the collection of data in an area identified as a significant gap, we commit New Zealand to flying blind in that area. …..A lack of time series in respect of some environmental pressure points could be costing us dearly in terms of poorly designed policies or irreversible damage.

One example may be enough. Caribou herds in southern Canada are threatened with extinction (Hebblewhite 2017, DeMars et al. 2019). Here is one example of counts on one caribou herd in southern Canada:

2009 = 2093 caribou
2012 = 1003
2019 = 185

It would be difficult to manage the conservation of any species of animal or plant that has such limited monitoring data. We can and must do better. We can start by dragging state of the environment reports out of the control of political parties by demanding to have in every country Commissioners of the Environment that are fully funded but independent of political influence. As long as the vision of elected governments is limited to 3 years, environmental decay will continue, out of sight, out of mind.

There is of course no reason that elected governments need follow the advice of any independent commission, so this recommendation is not a panacea for environmental issues. If citizens have independent information however, they can choose to use it and demand action.

DeMars, C.A.et al. (2019). Moose, caribou, and fire: have we got it right yet? Canadian Journal of Zoology 97, 866-879. doi: 10.1139/cjz-2018-0319.

Hebblewhite, M. (2017). Billion dollar boreal woodland caribou and the biodiversity impacts of the global oil and gas industry. Biological Conservation 206, 102-111. doi: 10.1016/j.biocon.2016.12.014.

The Central Predicament of Ecological Science

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Ecology like all the hard sciences aims to find generalizations that are eternally true. Just as physicists assume that the universal law of gravitation will still be valid 10,000 years from now, so do ecologists assume that we can find laws or generalizations for populations and ecosystems that will be valid into the future. But the reality for ecological science is quite different. If the laws of ecology depend on the climate being stable, soil development being ongoing, evolution being optimized, and extinction being slow in human-generation time, we are in serious trouble.

Paleoecology is an important subdiscipline of ecology because, like human history, we need to understand the past. But the generalizations of paleoecology may be of little use to understand the future changes the Earth faces for one major reason – human disturbance of both climate and landscapes. Climates are changing due to rising greenhouse gases that have a long half-life. Land and water are being appropriated by a rising human population that is very slow to stabilize, so natural habitats are continually lost. There is little hope in the absence of an Apocalypse that these forces will alleviate during the next 200 years. Given these changes in the Anthropocene where does ecology sit and what can we do about it?

If climate is a major driver of ecological systems, as Andrewartha and Birch (1954) argued (to the scorn of the Northern Hemisphere ecologists of the time), the rules of the past will not necessarily apply to a future in which climate is changing. Plant succession, that slow and orderly process we now use to predict future communities, will change in speed and direction under the influence of climatic shifts and the introduction of new plant species, plant pests, and diseases that we have little control over. Technological optimists in agriculture and forestry assume that by genetic manipulations and proper artificial selection we can outwit climate change and solve pest problems, and we can only hope that they are successful. Understanding all these changes in slow-moving ecosystems depends on climate models that are accurate in projecting future climate changes. Success to date has been limited because of both questionable biology and poor statistical procedures in climate models (Frank 2019; Kumarathunge et al. 2019; Yates et al. 2018).

If prediction is the key to ecological understanding, as Houlahan et al. (2017) have cogently argued, we are in a quandary if the models that provide predictions wander with time to become less predictive. Yates et al. (2018) have provided an excellent review of the challenges of making good models for ecological prediction. As such their review is either encouraging – ‘here are the challenges in bold type’ – or terribly depressing – ‘where are the long-term, precise data for predictive model evaluation?’ My colleagues and I have spent 47 years trying to provide reliable data on one small part of the boreal forest ecosystem, and the models we have developed to predict changes in this ecosystem are probably still too imprecise to use for management. Additional years of observations produce some ecosystem states that have been predictable but other changes that we have never seen before over this time frame of nearly 50 years.

In contrast to the optimism of Yates et al. (2018), Houlahan et al. (2017) state that:

“Ecology, with a few exceptions, has abandoned prediction and therefore the ability to demonstrate understanding. Here we address how this has inhibited progress in ecology and explore how a renewed focus on prediction would benefit ecologists. The lack of emphasis on prediction has resulted in a discipline that tests qualitative, imprecise hypotheses with little concern for whether the results are generalizable beyond where and when the data were collected.  (page 1)

I see this difference in views as a dilemma because despite much talk, there is little money or interest in the field work that would deliver reliable data for models in order to test their accuracy in predictions at small and large scales. An example this year is the failure of the expected large salmon runs to the British Columbia fishery, with model failure partly due to the lack of monitoring in the North Pacific (https://globalnews.ca/news/5802595/bc-salmon-stocks-plunge/; https://www.citynews1130.com/2019/09/09/worst-year-for-salmon/ , and in contrast with Alaska runs: https://www.adn.com/business-economy/2019/07/25/bristol-bay-sockeye-harvest-blowing-away-forecast-once-again/ ). Whatever the cause of the failure of B.C. salmon runs in 2019, the lack of precision in models of a large commercial fishery that has been studied for at least 65 yeas is not a vote of confidence in our current ecological modelling.

Andrewartha, H.G. and Birch, L.C. (1954) ‘The Distribution and Abundance of Animals.’ University of Chicago Press: Chicago. 782 pp.

Frank, P. (2019). Propagation of error and the reliability of global air temperature projections. Frontiers in Earth Science 7, 223. doi: 10.3389/feart.2019.00223.

Houlahan, J.E., McKinney, S.T., Anderson, T.M., and McGill, B.J. (2017). The priority of prediction in ecological understanding. Oikos 126, 1-7. doi: 10.1111/oik.03726.

Kumarathunge, D.P., Medlyn, B.E., Drake, J.E., Tjoelker, M.G., Aspinwall, M.J., et al. (2019). Acclimation and adaptation components of the temperature dependence of plant photosynthesis at the global scale. New Phytologist 222, 768-784. doi: 10.1111/nph.15668.

Yates, K.L., Bouchet, P.J., Caley, M.J., Mengersen, K., Randin, C.F., Parnell, S., Fielding, A.H., Bamford, A.J., et al. (2018). Outstanding challenges in the transferability of ecological models. Trends in Ecology & Evolution 33, 790-802. doi: 10.1016/j.tree.2018.08.001.