Category Archives: Conservation Biology

Ecological Science: Monitoring vs. Stamp Collecting

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

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

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

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

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

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

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

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

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

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

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

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

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

Why Ecology Fails to Prosper

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The general science of Ecology has changed dramatically during the last 60 years and my perception is that at present it is failing its critical role in developing science for the good of the Earth. I ask here if this pessimistic view is correct, why that might be, and if it is possible to change our trajectory. Every science must focus on major problems and these problems are too often lost as time progresses. The causes of these changes are rarely due to the competence of the scientists involved and more typically are found in the social milieu.  

The most obvious problem is science funding. You will appreciate that some sciences are funded very extravagantly and others very poorly. It is a decision of most societies that the sciences of medicine, economics and law are the kings of the hill. More funding probably flows to medical science than to all the other sciences combined. You can argue that this is what should occur, since humans are the most dominant and most important species in the Earth’s ecosystems. The confound here is the ethical one – are the poor of the world to be helped or not? Such a question seems outrageous, but just look at the distribution of Covid vaccines at different countries around the world. Economics is a strange bedfellow of medicine in the apparent view of society and its governments. The result is that there are more economists in the world today than non-medical scientists. We will not change this in our day.

The sciences that are most highly regarded are those that achieve two goals: first, rapid developments that improve our wealth, economic, and social goals, and second, developments that enable Earth as a planet to be exploited for human welfare. The physical sciences and engineering permit us to travel quickly, to fight wars against our enemies, and as a spinoff provide us with better automobiles and kitchen appliances. Geology helps us to find oil, iron ore, and lithium while it maps the Earth to help us understand its history. Zoology and Botany are different. They are supported strongly when they interface with the medical sciences and agriculture at a very practical level but otherwise are low in the funding order.

Ecology differs in that it proposes to understand how the populations of animals and plants, the biological communities, and ecosystems operate and what forces cause these to change. The first problem that arises with this mandate it that ecological understanding requires time frames that exceed human lifespans. So, ecology faces the same problem as geology but is not easily able to be useful in telling us where to build dams, where to mine gold and coal. We face an impossible barrier. To describe the biota of the Earth with its millions of species will occupy us for hundreds of years, assuming the funding is there. To understand why communities and ecosystems change will require an equal time span. But since ecological elements are driven in many ways by weather, climate change forces us to analyse an ever-changing network of species interactions.  

A consequence of this dilemma for ecologists is that they must study how humans are destroying the Earth and suggest a resolution of these problems. We are squeezed between our original objective of understanding how ecological interactions structure our world and serious immediate problems. An introduced pest is killing our trees – do something about this. Deer populations are too high so fix that. Fisheries are in difficulty, manage that. Some iconic species are declining in abundance, so citizens push to have more funding for biodiversity conservation. These are all short-term problems, while the need for ecological understanding is almost entirely long term. This takes us back to funding. For the past 30 or more years governments around the world have been reducing funding for ecological investigations. Government biologists have not increased in number given the urgent problems of the day. University funding of ecological sciences and ecological faculty members has declined partly because ecologists do not increase economic growth. Private funding has not come to the rescue because it is largely directed to social and economic issues, partly because of the feeling that it is the government’s job to deal with long-term issues in research.

The only solution is for ecologists to work together on important large-scale ecological problems with minimal funding. But this is impossible within the university system in which teaching is a focus and research can only be short-term. Attempts to address the large-scale ecological issues have resulted in many publications that use meta-analyses to resolve ecological questions. I doubt that these have achieved the resolution of ecological issues that we need (e.g. Geary et al. 2020).

What can we do about this relatively gloomy situation? One suggestion is to continue as we are, addressing short-term questions with limited funding. The advantage of this approach is that it allows individuals freedom from group constraints. One disadvantage is that two studies of the same problem may not be comparable unless the methods used were the same (e.g. Christie et al. 2019). The argument that climate change is happening so everything will change, and the past will not be relevant to the present is an argument of a broad uncoordinated approach to ecological issues.

Another approach can be to identify the critical ecological questions that we need answered now. Few have been brave enough to attempt this (Sutherland et al. 2010, 2013, 2018) for the broad area of conservation biology. An attempt to judge how much progress had been made on the issues listed in these three papers would be profitable in order to determine if this approach is useful in coordinating research programs. We might hope that ecological discord would be reduced if critical ecological questions were attacked with a consistent experimental design.

This discussion of ecology fits under the ‘empirical ecological studies’ framework of Fulton et al. (2019), and the expansive belief that theoretical models and system models will drive ecology into a successful science is illustrated in this recent review (O’Connor et al. 2020) and the accompanying articles. My concern is that these approaches have gotten us very little ahead in understanding ecological systems to date, and that until empirical ecological studies are increased in scope, duration, and precision we will not know whether models and systems analysis are leading us to a better understanding of the Earth’s ecosystems and the drivers of change or not. There is much left to be done.  

Christie, A.P.et al. (2019). Simple study designs in ecology produce inaccurate estimates of biodiversity responses Journal of Applied Ecology 56, 2742-2754. doi: 10.1111/1365-2664.13499.

Fulton, E.A.et al. (2019). Where the ecological gaps remain, a modelers’ perspective. Frontiers in Ecology and Evolution 7. doi: 10.3389/fevo.2019.00424.

Geary, W.L., et al. (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.

O’Connor, M.I.et al. (2020). Editorial: Unifying ecology Across scales: Progress, challenges and opportunities. Frontiers in Ecology and Evolution 8, 610459. doi: 10.3389/fevo.2020.610459.

Sutherland, W.J. et al. (2010). A horizon scan of global conservation issues for 2010. Trends in Ecology & Evolution 25, 1-7. doi: 10.1016/j.tree.2009.10.003.

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

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

A Few Problems Ecologists Need to Face

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This is an overly simple attempt to look ahead, after a summer of extreme heat, extensive forest fires, overheated crops, and excessive flooding, to ask where we ecologists might be going in the next century. 

The first and most important point is that these disasters of the last several months can all be blamed on climate change, and despite what you hear, there is no stopping these changes in the next hundred years. CO2 enrichment is turning Earth into a hot planet. This is a simple fact of physics that the CO2 we have already emitted into our atmosphere will be there for hundreds to thousands of years. The politicians and the media will tell you that carbon-capture is coming soon to solve all our emission problems and cleanse the atmosphere of excess greenhouse gases. If you believe that, ask yourself if you would invest your capital and retirement account in a poker game for a decline in CO2 during the next 20 years.

The critical question for we ecologists is this: How much of the accumulated ecological wisdom will be unchanged in 100 years? If we have only to deal with changing climate, we could develop an understanding of what the limiting factors are and express the anticipated changes in the climatic units of the future. But that becomes a problem when we recognize that food webs have many interactions in them that are climate affected but perhaps not climatically determined. So, for example if we have a simple food web of polar bears feeding on seals, both of which require an ice pack for survival at the present time, what should we expect in 100 years when there is virtually no polar ice to be found. A simple model will predict that the polar bear will go extinct and perhaps seals will learn to use land instead of ice packs, but the fish that are the main food of the seals may also change if they depend on zooplankton that have a water temperature niche boundary that is exceeded. So exactly what will happen to this simple food web cannot be easily understood from current ecological wisdom or models.

Another example is from the current changing dynamics of Stellar sea lions of the North Pacific, summarized in an excellent review by Andrew Trites (2021). Stellar sea lions occupy the coastlines of the North Pacific from the Sea of Okhotsk and the Bering Sea eastward down the west coast of North America to southern California. Forty years ago, scientists noted a decline beginning in the western sea lion populations in the Bering Sea and the Gulf of Alaska and at the same time an increase in sea lion numbers from Southeast Alaska to California. Two explanations compete among seal experts to explain this pattern. The ‘overfishing hypothesis’ suggested that the Alaskan and Russian fishery has removed too much of the sea lion’s favourite food items and thus caused starvation among western sea lions. The alternative to this explanation, the ‘junk-food-hypothesis’ suggested that sea lions in the west were consuming too many fish species of low fat and fewer calories, and that their starvation was self-limited and not caused by the human fisheries.

Here is a “simple” ecological problem with 2 competing hypotheses or explanations that has not yet been resolved after many years of research. Empirical ecologists will possibly argue that we need to monitor the sea lions and their prey and the fishing catches over this extensive area for the next decade or two to find the answer as to which of the two competing hypothesis is closest to being correct. But given climate change and ocean warming, neither of which are uniform over all parts of the Earth, we would expect large changes in the abundance and distribution of many fish species and consequently also in the predators that depend on them. But exactly which ones, and exactly where? Conservation ecology is dogged by this problem and subsists largely by ignoring it in favour of short-term studies in small areas and the effects of human population growth, and perhaps this is all we can do at present. So, should “watch and wait, look and see” become our model? Wildlife and fisheries management thus become short-term ‘watch and wait’ sciences, like passengers on the Titanic long ago, wondering what the future holds.

One way to suggest future paths is to model the various communities and ecosystems that we study, and this activity is now strong in ecology and conservation. But there are many difficulties with this approach boiling down to a ‘wait-and-see’ method of empirical investigation. A review by Furtado (2020) of two books on fisheries management provides an up-to-date view of progress in fisheries ecology and illustrates problems with bluefin tuna management and the modelling approach to fish ecosystems in general. The problem in assuming the modelling approach as an answer to our dilemma is shown clearly by the current Covid pandemic and the reversals in modelling and alternative views that have caused much confusion despite much important research. Whither ecology from this point in time?

Furtado, Miguel (2020). The Future of Bluefin Tunas: Ecology, Fisheries Management and Conservation. Conservation Biology 34, 1600-1602.

Trites, A.W. (2021). Behavioral Insights into the Decline and Natural History of Steller Sea Lions. In ‘Ethology and Behavioral Ecology of Otariids and the Odobenid, Ethology and Behavioral Ecology of Marine Mammals,’. (Ed. C. Campagna and R. Harcourt), pp. 489-518. (Springer Nature Switzerland.)  doi: 10.1007/978-3-030-59184-7_23  

Whither the Big Questions in Ecology?

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The science of ecology grows and grows and perhaps it is time to recognize the subcultures of the discipline which operate as nearly independent areas of science. Few people today would talk of the science of physics or the science of chemistry, but rather the subcultures of physics or chemistry in which critical problems are defined and tested. In a sense this has already been recognized in ecology by the increase in specific journals. No one goes to Conservation Biology to look up recent studies in insect pest control, and no one goes to Limnology and Oceanography to research progress in theoretical ecology. So, by default we ecologists have already subdivided the overall broad science of ecology into subcultures, and the problem then arises when we must consider major issues or big questions like the ecological impacts of climate change that encompass multiple subcultures, and the more specific issue of how we educate students of all ages about the broad problems of ecology and the environment.

The education issue ought to be the easiest part of this conundrum to deal with. The simple rule – Teach the Principles – is what textbook writers try to do. But this is easier said than done. Jim Hone et al. (2015) took on the problem of defining the principles of applied ecology and consolidated these into 22 prescriptive and 3 empirical principles that could serve as a starter for this area of general ecology. The same compilation could be done in many subdisciplines of ecology and there are many good examples of this (e.g., Lidicker, 2020, Ryo et al. 2019). A plethora of ecology textbooks exist to pull the broad subject together, and they are interesting themselves in what they emphasize.  

The larger problem is in the primary literature of ecology, and I pick here four big questions in ecology in which communication could be improved that would be useful both to educators and to the public.

  1. Sustainability of the Earth’s Ecosystems. This broad area covers human population dynamics, which can be generalized to many other species by the principles of population ecology. It would include agricultural issues and the consequences of soil erosion and degradation and cover the basics of atmospheric chemistry at least to question whether everyone going to Mars is particularly useful. Where relevant, every ecological publication should address how this research addresses the large issue of sustainability.
  2. Climate Change Effects. There is a general understanding of the geographic distribution of vegetation communities on Earth, how these have changed in geologic time and are changing now but projections for the future are vague. Much research is ongoing, but the ecological time frame of research is still too short (Hagerman and Pelai 2018). Teaching what we know now would include the essential physics and chemistry of sea level rise, changes in the distribution of good and bad species, including human diseases, and simple warnings about investing in real estate in Miami Beach. Every prediction about climate change effects should include a time frame at which the predictions could be accepted or rejected. If ecologists are to affect government policies, a testable action plan must be specified lest we keep barking up the wrong tree.
  3. Current conflicts in managing the Earth’s natural resources. The concern here is the social and economic drivers of why we continue overfishing and overharvesting resources that result in damage to local environments, and how we can manage conflicts over these resources. To manage intelligently we need to understand the interactions of the major species involved in the ecological community. Ecosystem dynamics will be the central set of concepts here, and the large topic of the resilience of our Earth’s ecosystems. Ecologists are clear that the resilience of ecosystems is limited but exactly where those limits are is far from clear at the present time.
  4. Conservation of Biodiversity. The ecological factors that limit biodiversity, and the consequences of biodiversity loss are major areas of current research and communication to the public. While the volume of concern is high in this subdiscipline, advances in understanding lag far behind. We operate now with only the vaguest of principles of how to achieve conservation results. The set of conservation principles (Prober et al. 2019) interacts strongly with the 3 big questions listed above and should cover advances in paleoecology and the methods of defining ancient environments as well as current conservation problems. Understanding how social conflict resolution can be achieved in many conservation controversies links across to the social sciences here. 

The key here is that all these big questions contain hundreds of scientific problems that need investigation, and the background of all these questions should include the principles by which ecological science advances, as well as the consequences of ignoring scientific advice. For educators, all these big questions can be analysed by examples from your favourite birds, or large mammals, or conifer trees, or fishes so that as scientific progress continues, we will have increased precision in our ecological understanding of the Earth. And more than enough material to keep David Attenborough busy.

For ecologists one recommendation of looking at ecology through the lens of big questions should be to include in your communications how your findings illuminate the road to improved understanding and further insights into how the Earth’s biodiversity supports us and how we need to support it. Ecology is not the science of the total environment, but it is an essential component of it.

Hagerman, S.M. and Pelai, R. (2018). Responding to climate change in forest management: two decades of recommendations. Frontiers in Ecology and the Environment 16, 579-587. doi: 10.1002/fee.1974.

Hone, J., Drake, A., and Krebs, C.J. (2015). Prescriptive and empirical principles of applied ecology. Environmental Reviews 23, 170-176. doi: 10.1139/er-2014-0076.

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

Prober, S.M., Doerr, V.A.J., Broadhurst, L.M., Williams, K.J., and Dickson, F. (2019). Shifting the conservation paradigm: a synthesis of options for renovating nature under climate change. Ecological Monographs 89, e01333. doi: 10.1002/ecm.1333.

Ryo, M., Aguilar-Trigueros, C.A., Pinek, L., Muller, L.A.H., and Rillig, M.C. (2019). Basic Principles of Temporal Dynamics. Trends in Ecology & Evolution 34, 723-733. doi: 10.1016/j.tree.2019.03.007.

Why Science is Frustrating

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Many people train in science because they are convinced that this is an important route to doing good in the world. We operate on the simple model that science leads to knowledge of how to solve problems and once we have that knowledge the application to policy and management should be reasonably simple. This model is of course wildly incomplete, so if you are a young person contemplating what to do with your life, you should perhaps think very carefully about how to achieve progress. I review here three current examples of failures of science in the timely management of acute problems.

The first and most complex current problem is the Covid-19 pandemic. Since this virus disease became a pandemic more than a year ago, many scientists have investigated how to thwart it. There was spectacular success in developing vaccines and advances in a basic understanding the virus. However, some proposals had no value, and this was often because the scientific papers involved were not yet peer reviewed but were released to the news media as though they were the truth. All the common mistakes of scientific investigation were in clear view, from simple hypotheses with no testing to a failure to consider multiple working hypotheses, to a failure to evaluate data because of non-disclosure agreements. Speed seemed to be of the essence, and if there is a sure way to accumulate poor science it is by means of speed, including little attention to experimental design, probabilities, and statistical analysis. Many books will soon appear about this pandemic, and blame for failures will be spread in all directions. Perhaps the best advice for the average person was the early advice suitable for all pandemics – avoid crowds, wash your hands, do not travel. But humans are impatient, and we await life going “back to normal”, which is to say back to rising CO2 and ignoring the poor.  

A second example is the logging of old growth forests. Ecologists all over the world from the tropics to the temperate zone have for the last 40-50 years decried logging practices that are not sustainable. Foresters have too often defended the normal practices as being sustainable with clever statements that they plant one tree for every one they cut, and look out your car window, trees are everywhere. It is now evident to anyone who opens their eyes that there is little old growth left (< 1% in British Columbia). But why does that matter when the trees are valuable and will grow back in a century or two or four? Money and jobs trump biodiversity and promises of governments adopting an “old-growth logging policy” appear regularly, to be achieved in a year or two. The tragedy is written large in the economics where for example in British Columbia the local government has spent $10 billion in the last 10 years supporting the forestry industry while the industry has contributed $6 billion in profits, not exactly a good rate of return on investment, particularly when the countryside has been laid waste in the process. Another case in which economics and government policy has trumped ecological research in the past but the need to protect old growth forests is gaining with public support now.

A third example comes again from medicine, a fertile area where money and influence too often outrace medical science. We have now a drug that is posed to alleviate or reduce the effects of Alzheimer’s, a tragic disease which affects many older people (Elmaleh et al. 2019, Nardini et al. 2021). A variety of drugs have been developed in an attempt to stop the mental deterioration of Alzheimer’s but none so far has been shown to work. A new drug (Aducanumab) is now available in the USA for treatment of Alzheimer’s but it already has a checkered history. This drug seemed to fail its first major trials yet was then approved by the Federal Drug Administration in the USA over the protests of several doctors (Knopman, Jones, and Greicius 2021). Given a cost of thousands of dollars a month for administering this new drug to a single patient, we can see the same scenario developing that we described for the forest industry and old growth logging – public pressure for new drugs resulting in questionable regulatory decisions.

There are several general messages that come out of this simple list. The most important one is that science-on-demand is not feasible for most serious problems. Plan Ahead ought to be the slogan written on every baseball hat, sombrero, Stetson, toque and turban to remind us that science takes time, as well as wisdom and money. If you think we are having problems in the current pandemic, start planning for the next one. If you think that drought is now a problem in western North America, start hedging your bets for the next drought. Sciences moves more slowly than iPhone models and requires long-term investments.

I think the bottom line of all the conflict between science and policy is discouraging for young people and scientists who are doing their best to unravel problems in modern societies and to join these solutions to public policy (González-Márquez and Toledo 2020). Examples are too numerous to list. Necessary policies for controlling climate change interfere with people’s desires for increased global travel but we now realize controls are necessary. Desirable human development goals can conflict with biodiversity conservation, but we must manage this conflict (Clémençon 2021). The example of feral horses and their effects on biodiversity in Australia and the USA is another good example of a clash of scientific goals with social preferences for horses (Boyce et al. 2021). Nevertheless, there are many cases in which public policy and conservation have joint goals (Tessnow-von Wysocki and Vadrot 2020, Holden et al. 2021). The key is to carry the scientific data and our frustration into policy discussions with social scientists and politicians. We may be losing ground in some areas but the present crises in human health and climate change present opportunities to design another kind of world than we have had for the last century.

Boyce, P. N., Hennig, J. D., Brook, R. K., and McLoughlin, P. D. (2021). Causes and consequences of lags in basic and applied research into feral wildlife ecology: the case for feral horses. Basic and Applied Ecology 53, 154-163. doi: 10.1016/j.baae.2021.03.011.

Clémençon, R. (2021). Is sustainable development bad for global biodiversity conservation? Global Sustainability 4. doi: 10.1017/sus.2021.14 2021.14.

Elmaleh, D.R., Farlow, M.R., Conti, P.S., Tompkins, R.G., Kundakovic, L., and Tanzi, R.E. (2019). Developing effective Alzheimer’s Disease therapies: Clinical experience and future directions. Journal of Alzheimer’s Disease 71, 715-732. doi: 10.3233/JAD-190507.

González-Márquez, I. and Toledo, V.M. (2020). Sustainability Science: A paradigm in crisis? Sustainability 12, 2802. doi: 10.3390/su12072802.

Holden, E., Linnerud, K., and Rygg, B.J. (2021). A review of dominant sustainable energy narratives. Renewable & Sustainable Energy Reviews 144. doi: 10.1016/j.rser.2021.110955.

Knopman, D.S., Jones, D.T., and Greicius, M.D. (2021). Failure to demonstrate efficacy of aducanumab: An analysis of the EMERGE and ENGAGE trials as reported by Biogen, December 2019. Alzheimer’s & Dementia 17, 696-701. doi:/10.1002/alz.12213.

Nardini, E., Hogan, R., Flamier, A., and Bernier, G. (2021). Alzheimer’s disease: a tale of two diseases? Neural Regeneration Research 16, 1958. doi: 10.4103/1673-5374.308070

Tessnow-von Wysocki, I. and Vadrot, A.B.M. (2020). The voice of science on marine biodiversity negotiations: A systematic literature review. Frontiers in Marine Science 7, 614282. doi: 10.3389/fmars.2020.614282.

The Crunch is Here

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There are times when we either act or give up, so if you think that the Covid epidemic, the conservation of endangered species, and the protection of old growth forests are irrelevant problems to your way of life, stop reading here. These three major problems are here and now and have come to a head as a crunch: do something or quit.

The Covid epidemic is the most obvious of the current crises and it is on the radio and TV every day with an array of instructions of how to avoid this virus disease. You can respond to all this in three ways: ignore the problem because you are immortal, take a few precautions when you have time but minimize inconvenience, or take the mortality rate and the sickness rate of Covid to heart and do all you can to prevent infection or spread of infection. In the third wave of this virus, too many people in North America are taking option 1 and 2, perhaps in the hope that the vaccines arriving now will solve the problem of infection. If you think the pandemic will go away without much death and disruption, read Kolata (2019) or one of the many good books on pandemics in history (e.g., Kelly (2006). They are with us and our governments must take note.

Of less visibility in the news media are conservation issues that are equally at a crunch point. The most obvious one in Canada is the decline of mountain caribou, and the current status of conservation efforts on their behalf. Nagy-Reis et al. (2021) have recently reported on the lack of success to date in conserving mountain caribou. We have known for more than 20 years that habitat loss and habitat changes were the critical factors driving mountain caribou populations in Western Canada to extinction. Forest cover within the caribou range is the key indicator for caribou conservation, and forest harvest is the main cause of habitat loss added to by forest fires in more northern areas. From 2000 to 2018 caribou lost twice as much habitat as they gained by restoration policies from forest companies and the governments involved. Loss rates of habitat in different subregions of Western Canada ranged from about 1% per year to 8% per year loss. If we had a bank account with these continued losses over 20 years, we would start a revolution. The accepted policies are failing caribou. Seismic lines that break up caribou habitat are regenerating at a slow rate. Changes in land use management must be implemented to prevent extinction but the crunch comes there – jobs in the forestry industry vs. conservation goals that do not generate cash for governments. Temporary fixes like wolf control will help, but as Nagy-Reis et al. (2021) point out are not sufficient to solve the problem. If we wish to reverse these caribou declines, we must make long-term commitments to land use planning and reduce human alterations of landscapes. 

The third problem in which crunch time is coming is the loss of old growth forests, and thus is related to some extent to the caribou conservation issue. Old growth forest is disappearing globally and in any country on Earth you can hear the cry (e.g. Lindenmayer et al. 2020, Watson et al. 2018). In British Columbia now you must drive many hours to see old growth (3 meters diameter) and they are still logging these stands. The reason for this is the clever foresters who classify “old growth” in this province, so that in their arithmetic at present 26% of our forests are called ‘old growth’. At high elevations many ‘old growth’ stands are small trees, and at one extreme old growth in terms of age could be Krummholz (‘knee timber’) < 1 m tall. The government classifies old growth in wetter areas as stands of 250 years or more in age, and in dryer areas trees of 140 years old, primarily because the logging companies so far have not wanted to log such “small” trees. Price et al. (2021) analysed the forest structure of British Columbia and classified old growth with a proper definition of a productivity class of trees that will grow to 25 m or more in height by age 150 years. By government definitions B.C. has about 50 million ha of forest, of which 26% is classified as ‘old’growth’. So, this means they believe that 13 million ha of forest in B.C. is old growth. But if you consider the more correct ecological definition of old growth as stated by Price et al. (2021) of trees that will grow > 25 m tall in 50 years you find that <1% of B.C. forest is old growth at the present time. People do not drive for miles to see 5 m trees which they already have in cities. They will drive to see trees that are 800-1000 years old and more than 3 m in diameter, so a common-sense definition of old growth prevails in the tourist population. But again, we are back at jobs in forestry vs tourism potentials and the government is so committed to the forest industry that you have to search hard to find anyone who will give you a public lecture on “old growth” logging. So, this is another crunch for our time, jobs vs some 800-year-old trees with a lot of wood that inspire us and our children as being part of nature. All these considerations do not even begin to consider the other species that are lost in logging old growth because they are small and rarely measured (Doak 1989). The accepted government policies are failing us and our children. It is time to use science to challenge these changes which will affect us all now and in the future.

Doak, D. (1989). Spotted owls and old growth logging in the Pacific Northwest. Conservation Biology 3, 389-396.

Kelly, J. (2006) ‘The Great Mortality: An Intimate History of the Black Death, the Most Devastating Plague of All Time.’ (Harper Perennial: New York.). ISBN: 978-0060-00693-8.

Lindenmayer, D.B., Kooyman, R.M., Taylor, C., Ward, M., and Watson, J.E.M. (2020). Recent Australian wildfires made worse by logging and associated forest management. Nature Ecology & Evolution 4, 898-900. doi: 10.1038/s41559-020-1195-5.

Kolata, G.B. (2019) ‘Flu: The Story of the Great Influenza Pandemic of 1918 and the Search for the Virus that caused it.’ (Atria Books: New York.). ISBN: 978-14299-79351

Nagy-Reis, M., Dickie, M., Calvert, A.M., Hebblewhite, M., Hervieux, D., Seip, D.R., Gilbert, S. L., Venter, O., DeMars, C., Boutin, S., and Serrouya, R. (2021). Habitat loss accelerates for the endangered woodland caribou in western Canada. Conservation Science and Practice (in press), e437. doi: 10.1111/csp2.437 .

Price, K., Holt, R.F., and 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-2020-0453.

Watson, J.E.M., Evans, T., Venter, O., Williams, B., and Tulloch, A. (2018). The exceptional value of intact forest ecosystems. Nature Ecology & Evolution 2, 599-610. doi: 10.1038/s41559-018-0490-x.

Why Ecological Understanding Progresses Slowly

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I begin with a personal observation spanning 65 years of evaluating ecological and evolutionary science – we are making progress but very slowly. This problem would be solved very simply in the Middle Ages by declaring this statement a heresy, followed by a quick burning at the stake. But for the most part we are more civil now, and we allow old folks to rant and rave without listening much.

By a stroke of luck, Betts et al. (2021) have reached the same conclusion, but in a more polite and nuanced way than I. So, for the whole story please read their paper, to which I will only add a footnote of a tirade to make it more personal. The question is simple and stark: Should all ecological research be required to follow the hypothetico-deductive framework of science? Many excellent ecologists have argued against this proposal, and I will offer only an empirical, inductive set of observations to make the contrary view in support of H-D science.  

Ecological and evolutionary papers can be broadly categorized as (1) descriptive natural history, (2) experimental hypothesis tests, and (3) future projections. The vast bulk of papers falls into the first category, a description of the world as it is today and in the past. The h-word never appears in these publications. These papers are most useful in discovering new species, new interactions between species, and the valuable information about the world of the past through paleoecology and the geological sciences. Newspapers and TV thrive on these kinds of papers and alert the public to the natural world in many excellent ways. Descriptive natural history in the broad sense fully deserves our support, and it provides information essential to category (2), experimental ecology, by asking questions about emerging problems, introduced pests, declining fisheries, endangered mammals and all the changing components of our natural world. Descriptive papers typically provide ideas that need follow up by experimental studies. 

Public support for science comes from the belief that scientists solve problems, and if the major effort of ecologists and evolutionary biologists is to describe nature, it is not surprising that financial support is minimal in these areas of study. The public is entertained but ecological problems are not solved. So, I argue we need more of papers (2). But we can get these only if we attack serious problems with experimental means, and this requires long-term thinking and long-term funding on a scale we rarely see in ecology. The movement at present is in the direction of big-data, technological methods of gathering data remotely to investigate landscape scale problems. If big data is considered only observational, we remain in category (1) and there is a critical need to make sure that big data projects are truly experimental, category (2) science (Lindenmayer, Likens and Franklin 2018). That this change is not happening so far is clear in Betts et al. (2021) Figure 2, which shows that very few papers in ecology journals in the last 25 years provide a clear set of multiple alternative hypotheses that they are attempting to test. If this criterion is a definition of good science, there is far less being done than we might think from the explosion of papers in ecology and evolution.

The third category of ecological and evolution papers is focused on future predictions with a view to climate change. In my opinion most of these papers should be confined to a science fiction journal because they are untestable model extrapolations for a future beyond our lifetimes. A limited subset of these could be useful is they were projecting a 5-10 year scenario that scientists could possibly test in the short term. If they are to be printed, I would suggest an appendix in all these papers of the list of assumptions that must be made to reach their future predictions.

There is of course the fly in the ointment that even when ecologists diagnose a conservation problem with good experiments and analysis the policy makers will not follow their advice (e.g. Palm et al. 2020). The world is not yet perfect.

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

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

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: e219. doi: 10.1111/csp2.219.

On Declining Insect Populations

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Judy Myers, Charles Krebs, Gergana Daskalova and Isla Myers-Smith

The rising concern about conservation issues is echoed in recent months by newspaper reports of collapses in insect populations world-wide: the “insect Armageddon”. As part of our general concern that the-devil-is-in-the-details, we want to discuss these reports within the general question of how we decide if this simple statement is correct or not, and what methods are needed to establish declining population trends.

We require four procedures to decide if a population or a series of populations are declining:

(1) Reliable census methods and appropriate statistical analyses must be used. This is not a trivial exercise. Results can be biased by the chance occurrence of particularly high numbers at the beginning of the data trend as in Seibold et al. (2019), the failure to correct for temporal pseudoreplication in data sets as pointed out by Daskalova et al. (2021) or by searching the literature only for studies of insect decline and then claiming to show widespread population declines as in Sánchez-Bayo et al. (2019). It is important to avoid biasing data toward a conclusion that declines are occurring. Increasing trends and examples showing no trend must be acknowledged and published to allow a true assessment.

(2) The taxonomic group of concern must be delineated since what applies to butterflies may or may not apply to carabid beetles. It can be difficult and time consuming to sort through samples to identify taxonomic groups. For this reason, the biomass of trap collections has been used as a surrogate for insect numbers in some studies (Hallman et al. 2019). This tells us nothing about population trends or diversity of different types of insects. Population data are required, and the biology of the focus group identified when considering causal mechanisms for population trends. For example, aquatic and terrestrial species are likely to respond to different environmental conditions and these must be separated (Van Klink et al., 2020).

(3) The scale of the study must be carefully outlined, whether it is 1 ha of grassland, a region, a country, or a continent. Lumping together results from studies done at different scales makes interpretation impossible. Accounting for scale in analyses is challenging, but detected trends in metrics such as species richness can differ markedly across scales (Vellend et al. 2017; Chase et al. 2019).

(4) The duration of the study must be related to the generation time of the insect group and population dynamics of those taxa. Many insects have a single generation a year and others multiple generations. Shorter time series are more variable (Daskalova et al. 2021), time trends in many insect populations are often more saw shaped than linear (Macgregor et al. 2019), and some insect species experience outbreaks or population cycles (Myers and Cory 2013).

These four requirements are not new, and many authors have discussed the details of these issues and how they play out in specific insect populations (Didham et al. 2020; Wagner 2020). A fifth requirement needs to be added when multiple studies are included in meta-analyses:

(5) All data inclusion must be scrutinized to determine if the four above requirements have been met before they are included in the meta-analysis.

Census methods for insect populations were presented long ago by Southwood (1966) in a classic book, updated in Southwood and Henderson (2000) and now reviewed recently in Montgomery et al. (2021). Montgomery et al. (2021) noted that even at this late date there is a general lack of standardization in insect monitoring methods, and that this standardization is essential if we are to track insect population or community changes. Statistical methods for time series data must be rigorous as pointed out by Daskalova et al. (2021).  The general message is that there is no one insect monitoring method that can apply to all species, and the scale of the study, along with the sampling effort needed for reliable inferences on population trends, must be decided well in advance of starting a monitoring study.

Newspaper articles dramatize the collapse of insect populations while the reality shown by detailed studies is much more nuanced. Much of the decline in insects could be traced to climate change, agricultural intensification, forestry, human population growth, urbanization and other factors (Wagner 2021). Consequently, it is important to state what the baseline for any evaluation is. The pure ecologist may wish to know how much insect populations have changed in areas where only one factor like climate change has operated. The agricultural insect ecologist may wish to know overall changes in the presence of all human and natural changes in the agricultural landscapes in which insects live (Laussmann et al. 2021). To find out the actual mechanisms behind the observed declines, a clear experimental protocol is necessary. As useful as monitoring is by itself, it can only provide weak evidence of mechanisms responsible for insect declines.

The restoration of individual species that are declining is more difficult than we might like. Warren et al. (2021) provide details of management changes that attempt to restore populations of the endangered British butterfly Hamearis lucina by landscape level habitat improvements. Funds for restoration will not be available at the scale needed for tropical and subtropical habitats losing insect diversity under stress from agricultural intensification (Raven and Wagner 2021).

The bottom line is that there are enough data now to be concerned about insect declines, but we must be careful not to cry that the “sky is falling” (Saunders et al. 2020). As in many issues with changes in populations and communities, census methods and experimental designs must be sharpened and standardized. Our take-home message is that any tests of insect population, abundance or biodiversity trends require rigorous methods of analysis before publication, or phoning the local newspaper.

Daskalova, G.N., A.B. Phillimore, and I.H. Myers‐Smith. 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.

Didham, R.K., Basset, Y., Collins, C.M., Leather, S.R., et al. (2020). Interpreting insect declines: seven challenges and a way forward. Insect Conservation and Diversity 13, 103-114. doi: 10.1111/icad.12408.

Chase, J.M., McGill, B.J., Thompson, P.L., Antão, L.H., Bates, A.E., et al. 2019. Species richness change across spatial scales. Oikos 128:1079-1091. doi: 10.1111/oik.05968

Hallmann, C.A., et al. 2017. More than 75 percent decline over 27 years in total flying insect biomass in protected areas. PLoS ONE 12, e0185809. doi: 10.1371/journal.pone.0185809

Laussmann, T., Dahl, A., Radtke, A., 2021. Lost and found: 160 years of Lepidoptera observations in Wuppertal (Germany). Journal of Insect Conservation (in press). doi: 10.1007/s10841-021-00296-w

Macgregor, C.J., J. H. Williams, J.R. Bell, and C.D. Thomas. 2019. Moth biomass increases and decreases over 50 years in Britain. Nature Ecology & Evolution 3:1645-1649. doi: 10.1038/s41559-019-1028-6

Montgomery, G.A., M.W. Belitz, R.P. Guralnick, and M.W. Tingley. 2021. Standards and best practices for monitoring and benchmarking insects. Frontiers in Ecology and Evolution 8: 579193. doi: 10.3389/fevo.2020.579193.

Myers, J.H., Cory, J.S., 2013. Population cycles in forest Lepidoptera revisited. Annual Review of Ecology, Evolution, and Systematics 44, 565–592. https://doi.org/10.1146/annurev-ecolsys-110512-135858

Raven, P. H., and D. L. Wagner. 2021. Agricultural intensification and climate change are rapidly decreasing insect biodiversity. Proceedings of the National Academy of Sciences 118 (2): e2002548117. doi: 10.1073/pnas.2002548117. 

Sánchez-Bayo, F., and K. A. Wyckhuys. 2019. Worldwide decline of the entomofauna: A review of its drivers. Biological Conservation 232:8-27. doi: 10.1016/j.biocon.2019.01.020

Saunders, M.E., Janes, J.K. and O’Hanlon, J.C., 2020. Moving on from the insect apocalypse narrative: Engaging with evidence-based insect conservation. BioScience, 70(1):80-89. doi: 10.1093/biosci/biz143

Seibold, S., M. M. Gossner, N. K. Simons, N. Blüthgen, et. al. 2019. Arthropod decline in grasslands and forests is associated with landscape-level drivers. Nature 574:671-674. doi: 10.1038/s41586-019-1684-3.

Southwood, T.R.E. (1966) ‘Ecological Methods.’ (Methuen: London.)

Southwood, T.R.E. and Henderson, P.A. (2000) ‘Ecological Methods.’ (Blackwell Science: Oxford.) 575 pp.  ISBN: 0632054778

van Klink, R., Bowler, D.E., Gongalsky, K.B., Swengel, A.B., et al. (2020). Meta-analysis reveals declines in terrestrial but increases in freshwater insect abundances. Science 368, 417-420. doi: 10.1126/science.aax9931.

Vellend, M., Baeten, L., Becker-Scarpitta, A., Boucher-Lalonde, V., McCune, J.L., Messier, J., Myers-Smith, I.H. and Sax, D.F., 2017. Plant biodiversity change across scales during the Anthropocene. Annual Review of Plant Biology 68:563-586. doi: 10.1146/annurev-arplant-042916-040949 .

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

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

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

On Innovative Ecological Research

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Ecological research should have an impact on policy development. For the most part it does not. You do not need to take my word for this, since I am over the age of 40, so for confirmation you might read the New Zealand Environmental Science Funding Review (2020) which stated:

“I am not confident that there is a coherent basis for our national investment in environmental science. I am particularly concerned that there is no mechanism that links the ongoing demand environmental reporting makes for an understanding of complex ecological processes that evolve over decades, and a science funding system that is constantly searching for innovation, impact and linkages to the ever-changing demands of business and society.” (page 3)

Of course New Zealand may be an outlier, so we must seek confirmation in the Northern Hemisphere. Bill Sutherland and his many colleagues has every 3-4 years since 2006 (nearly in concert with the lemming cycle) put out an extraordinary array of suggestions for important ecological questions that need to be answered for conservation and management. If you should be running a seminar this year, you might consider doing a historical survey of how these suggestions have changed since 2006, 2010, 2013, to 2018. Excellent questions, and how much progress has there been on answering his challenges?

Some progress to be sure, and for that we are thankful, but the problems multiply faster than ecological progress, and I am reminded of trying to stop a snow avalanche with a shovel. Why should this be? There are some very big questions in ecology that we need to answer but my first observation is that we have made little progress with the Sutherland et al. (2006) list, which would be largely culled from the previous many years of ecological studies. The first problem is that research funding is too often geared to novel and innovative proposals, so that if you would ask for funding to answer an old question that Charles Elton proposed in the 1950s, you would be struck off the list of innovative ecologists and possibly exiled to Mars with Elon Musk. Innovation in the mind of the granting agencies is based on the iPhone and the latest models of cars which have a time scale of one year. Any ecologist working on a problem that has a time scale of 30 years is behind the times. So when you write a grant request proposal you are pushed to restate the problems recognized long ago as though they were newly recognized with new methods of analysis.

There is no doubt some truly innovative ecological research, and to list these might be another interesting seminar project, but most of the environmental problems of our day are very old problems that remain unresolved. Government agencies in some countries have a list of problems of the here-and-now that university research rarely focuses on because the research cannot be innovative. These mostly practical problems must then be solved by government environmental departments with their ever-shrinking resources, so they in turn contract these out to the private sector with its checkered record of gathering the data required for solving the problems at hand.

Environmental scientists will complain that when they do reach conclusions that will at least partly resolve the problems of the day, governments refuse to act on this knowledge because of a variety of vested interests; if the environment wins, the vested interests lose, not a zero-sum game. If you want a good example, note that John Tyndall recognized CO2 and the Greenhouse Effect in 1859, and Svante Arrhenius and Thomas Chamberlin calculated in 1896 that burning fossil fuels increased CO2 such that 2 X CO2 would = + 5ºC rise in temperature. And in 2021 some people still argue about this conclusion.

My suggestion is that we would be better off striking the word ‘innovation’ from all our granting councils and environmental research funding organizations, and replacing it with ‘excellent’ and ‘well designed’ as qualities to support. You are still allowed to talk about ‘innovative’ iPhones and autos, but we are better off with ‘excellent’ environmental and ecological research.

New Zealand Parliamentary Commissioner for the Environment. (2020). A review of the funding and prioritisation of environmental research in New Zealand (Wellington, New Zealand.) Available online: https://www.pce.parliament.nz/publications/environmental-research-funding-review

Sutherland, W.J., et al. (2006). The identification of 100 ecological questions of high policy relevance in the UK. Journal of Applied Ecology 43, 617-627. doi: 10.1111/j.1365-2664.2006.01188.x.

Sutherland, W.J., et al. (2010). A horizon scan of global conservation issues for 2010. Trends in Ecology & Evolution 25, 1-7. doi: 10.1016/j.tree.2009.10.003

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

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

On the Focus of Biodiversity Science

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Biodiversity science has expanded in the last 25 years to include scientific disciplines that were in a previous time considered independent disciplines. Now this could be thought of as a good thing because we all want science to be interactive, so that geologists talk to ecologists who also talk to mathematicians and physicists. University administrators might welcome this movement because it could aim for a terminal condition in which all the departments of the university are amalgamated into one big universal science department of Biodiversity which would include sociology, forestry, agriculture, engineering, fisheries, wildlife, geography, and possibly law and literature as capstones. Depending on your viewpoint, there are a few problems with this vision or nightmare that are already showing up.

First and foremost is the problem of the increasing amount of specialist knowledge that is necessary to know how to be a good soil scientist, or geographer, or fisheries ecologist. So if we need teams of scientists working on a particular problem, there must be careful integration of the parts and a shared vision of how to reach a resolution of the problem. This is more and more difficult to achieve as each individual science itself becomes more and more specialized, so that for example your team now needs a soil scientist who specializes only in clay soils. The results of this problem are visible today with the Covid pandemic, many research groups working at odds to one another, many cooperating but not all, vaccine supplies being restricted by politics and nationalism, some specialists claiming that all can be cured with hydroxychloroquine or bleach. So the first problem is how to assemble a team. If you want to do this, you need to sort out a second issue.

The second hurdle is another very big issue upon which there is rarely good agreement: What are the problems you wish to solve? If you are a university department you have a very restricted range of faculty, so you cannot solve every biodiversity problem on earth. At one extreme you can have the one faculty member = one problem approach, so one person is concerned with the conservation of birds on mountain tops, another is to study frogs and salamanders in southern Ontario, and a third is to be concerned about the conservation of rare orchids in Indonesia. At the other extreme is the many faculty = one problem approach where you concentrate your research power on a very few issues. Typically one might think these should be Canadian issues if you were a Canadian university, or New Zealand issues if you were a New Zealand university. In general many universities have taken the first approach and have assumed that government departments will fill in the second approach by concentrating on major issues like fisheries declines or forest diseases.

Alas the consequences of the present system are that the government is reducing its involvement in solving large scale issues (take caribou in Canada, the Everglades in Florida, or house mice outbreaks in Australia). At the same time university budgets are being cut and there is less and less interest in contributing to the solution of environmental problems and more and more interest in fields that increase economic growth and jobs. Universities excel at short term challenges, 2–3-year problem solving, but do very poorly at long-term issues. And it is the long term problems that are destroying the Earth’s ecosystems.

The problem facing biodiversity science is exactly that no one wishes to concentrate on a single major problem, so we drift in bits and pieces, missing the chance to make any significant progress in any one of the major issues of our day. Take any major issue you wish to discuss. How many species are there on Earth? We do not even know that very well except in a few groups, so how much effort must go into taxonomy? Are insect populations declining? Data are extremely limited to a few groups gathered over a small number of years in a small part of the Earth with inadequate sampling. Within North America, why are charismatic species like monarch butterflies declining, or are they really declining? How much habitat must be protected to ensure the continuation of a migratory species like this butterfly. Can we ecologists claim that any one of our major problems are being resourced adequately to discover answers?

When biodiversity science interfaces with agricultural science and the applied sciences of fisheries and wildlife management we run into another set of major questions. Is modern agriculture sustainable? Certainly not, but how can we change it in the right direction? Are pelagic fisheries being overharvested? Questions abound, answers are tentative and need more evidence. Is biodiversity science supposed to provide solutions to these kinds of applied ecological questions? The current major question that appears in most biodiversity papers is how will biodiversity respond to climate change?  This is in principle a question that can be answered at the local species or community scale, but it provides no resolution to the problem of biodiversity loss or indeed even allows adequate data gathering to map the extent and reality of loss. Are we back to mapping the chairs on the Titanic but now with detailed satellite data?

What can be done about this lack of focus in biodiversity science? At the broadest level we need to increase discussions about what we are trying to accomplish in the current state of scientific organization. Trying to write down the problems we are currently studying and then the possible ways in which the problem can be resolved would be a good start. If we recognize a major problem but then can see no possible way of resolving it, perhaps our research or management efforts should be redirected. But it takes great courage to say here is a problem in biodiversity conservation, but it can never be solved with a finite budget (Buxton et al. 2021). So start by asking: why am I doing this research, and where do I think we might be in 50 years on this issue? Make a list of insoluble problems. Here is a simple one to start on: eradicating invasive species. Perhaps eradication can be done in some situations like islands (Russell et al. 2016) but is impossible in the vast majority of cases. There may be major disagreements over goals, in which case some rules might be put forward, such as a budget of $5 million over 4 years to achieve the specified goal. Much as we might like, biodiversity conservation cannot operate with an infinite budget and an infinite time frame.

Buxton, R.T., Nyboer, E.A., Pigeon, K.E., Raby, G.D., and Rytwinski, T. (2021). Avoiding wasted research resources in conservation science. Conservation Science and Practice 3. doi: 10.1111/csp2.329.

Russell, J.C., Jones, H.P., Armstrong, D.P., Courchamp, F., and Kappes, P.J. (2016). Importance of lethal control of invasive predators for island conservation. Conservation Biology 30, 670-672. doi: 10.1111/cobi.12666.