Category Archives: General Ecology

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.

What does Ecology have to offer for Covid pandemic response planning?

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It has already occurred to many ecologists that Covid pandemic management could obtain some useful advice from ecologists in many subdisciplines. Yet there is apparently no clear use of established ecological idioms for Covid planning that I can find in the literature. No doubt there were many informal meetings among ecologists and medical scientists, and epidemiology is an ecological subdiscipline. Some papers have been published about the behavioural ecology of individual interactions that could lead to infection spread (e.g., Shaw et al. 2021) and books and symposia will no doubt appear once the pandemic is over. But I can find no direct evidence that ecologists were consulted in the early days of the pandemic for ideas about disease spread in spite of an abundant literature on the subject (e.g., Jones et al. 2008, Halliday et al. 2017 and many others). Let us try to list some of the ecological principles that might have been useful if they were injected into the Covid pandemic planning and discussions from the start.

I can see six ecological principles that could be useful for any disease planning:
(1) Invasion ecology
(2) Island eradications
(3) Biosecurity considerations
(4) Pest control
(5) Population regulation.
(6) Evolutionary ecology.

Invasion ecology provides many examples of the clear principle that avoiding the introduction of a new species or disease is the simplest way to avoid potential future issues. Once a species is introduced it is typically impossible to get rid of it or alternatively very expensive.

Island eradications have given us several lessons in the difficulties of eradication of a pest once it is established. The best examples come from introduced rats on islands (Russell and Broome 2016, Wheeler et al. 2019) and cat eradication on Macquarie Island (Dowding et al. 2009). Advances are being made in eradication on islands but to achieve this on a continental scale eludes us unless the species is caught very early in its establishment.

Biosecurity considerations flow from the trade in illegal drugs but of late have focused on endangered wildlife. The principle is to prevent the entry or exit of dangerous or threatened organisms. ‘Do not let the organism in’ seems to be a message lost on most countries during the Covid pandemic.

Pest control has been a major issue both in conservation, in agriculture, and in epidemiology. It is the one ecological principle that has occupied 95% of the energy and the funding for Covid problems that have arisen partly from ignoring the previous three principles. Our success in dealing with Covid is about on par with our success in pest control, which is not a compliment.

Population regulation would seem to be an issue far from a pandemic, but it is an essential feature of the spread of the virus in densely populated areas. Much attention has been paid to social interactions and their behavioural consequences (e.g., Xu and Cheng 2021), but the matter has emerged again as ‘hot spots’ of viral infections and the discussions of whether vaccine availability should be prorated to these areas to reduce contagion or given to more susceptible older people or to essential workers however defined. Individual differences are a major area of behavioural ecology and there is an extensive literature that I think has not been mined for ideas of how to respond to a pandemic.  

Evolutionary ecology is another critical area of great interest in disease management because of the speed of mutational changes in disease organisms. Much of the current discussion is about virus variants that are ‘of concern’ and those that are variants ‘of interest’. Distinguishing these is relatively simple but has not been used as much as it should to prevent continued outbreaks from the new mutations by widespread testing. Much modelling has been done but too little empirical work to trace these invasions in detail from one continent to another.

The bottom line of this discussion is a plea for medical specialists to talk to ecologists and other natural scientists. I suspect too few medical people feel that biologists would have any insight to pandemic management decisions, and I am certain that many or most politicians have no idea of the complexities of the ecology of pandemics. So, this is a plea following Haley et al. (2021) and Shaw et al. (2021) for more cooperation and consultation between scientists who have knowledge of details that might help us in keeping ahead of the next wave.

Dowding, J.E., Murphy, E.C., Springer, K., Peacock, A.J., and Krebs, C.J. (2009). Cats, rabbits, Myxoma virus, and vegetation on Macquarie Island: a comment on Bergstrom et al. (2009). Journal of Applied Ecology 46, 1129-1132. doi: 10.1111/j.1365-2664.2009.01690.x

Haley, D., Paucar-Caceres, A., and Schlindwein, S. (2021). A critical inquiry into the value of systems thinking in the time of COVID-19 crisis. Systems 9, 1-14. doi: 10.3390/systems9010013.

Halliday, J.E.B., Hampson, K., Hanley, N., Lembo, T., Sharp, J.P., Haydon, D.T., and Cleaveland, S. (2017) Driving improvements in infectious disease surveillance through locally relevant capacity strengthening. Science 357:146–148. doi:10.1126/science.aam8332.

Jones, K.E., Patel, N.G., Levy, M.A. et al. (2008) Global trends in emerging infectious diseases. Nature 451: 990–993. doi:10.1038/nature06536.

Russell, J.C. and Broome, K.G. (2016). Fifty years of rodent eradications in New Zealand: another decade of advances. New Zealand Journal of Ecology 40, 197-204. doi: 10.20417/nzjecol.40.22.

Shaw, A.K., White, L.A., Michalska-Smith, M., Borer, E.T., Craft, M.E., Seabloom, E.W., et al.  (2021). Lessons from movement ecology for the return to work: Modeling contacts and the spread of COVID-19. PLoS ONE 16, e0242955. doi: 10.1371/journal.pone.0242955.

Wheeler, R., Priddel, D., O’Dwyer, T., Carlile, N., Portelli, D., and Wilkinson, I. (2019). Evaluating the susceptibility of invasive black rats (Rattus rattus) and house mice (Mus musculus) to brodifacoum as a prelude to rodent eradication on Lord Howe Island. Biological Invasions 21, 833-845. doi: 10.1007/s10530-018-1863-4.

Xu, P. and Cheng, J. (2021). Individual differences in social distancing and mask-wearing in the pandemic of COVID-19: The role of need for cognition, self-control and risk attitude. Personality and Individual Differences 175, 110706. doi: 10.1016/j.paid.2021.110706.

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 Dollar Value of Nature

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The Dasgupta Report was released last week with great promise. The news outlets were happy: The Guardian newspaper for example reported:

“The world is being put at “extreme risk” by the failure of economics to take account of the rapid depletion of the natural world and needs to find new measures of success to avoid a catastrophic breakdown, a landmark review has concluded.

Prosperity was coming at a “devastating cost” to the ecosystems that provide humanity with food, water and clean air, said Prof Sir Partha Dasgupta, the Cambridge University economist who conducted the review.

The 600-page review was commissioned by the UK Treasury, the first time a national finance ministry has authorised a full assessment of the economic importance of nature.”

What should we make of this scenario? Are ecologists happy that economists now think all the things we have been fighting for are finally recognized? Or are we barking up the wrong tree? The first assumption is that we have surrendered all environmental decision making to economists. A corollary of this assumption might be that we tried having David Attenborough and the many excellent nature presenters convince the world that nature is wonderful and should be kept for all to enjoy, and this has mostly failed to alleviate our environmental problems. Many people do not seem to really care about nature unless it affects their livelihood directly. A second assumption is that economics is king of all, and by rolling out the big guns we will finally get progress in resolving environmental problems. Forget studying ecology and take up economics instead. If these two assumptions are correct, I would propose that we have lost the plot, and if we can deal with our ecological mess only by talking dollars, we really are lost.

Many people believe that we can overcome environmental changes and at the same time carry on much as we are today. The ever-increasing number of sustainability institutes and journals will attest to the reversal of environmental damage. Unfortunately, the correlation is positive rather than negative, and as this and many other reports detail, environmental damages continue to increase and at an increasing rate. What can we do to change this?

The first problem is that the environmental mess accumulates at too slow a rate, so the simplest solution for each person is to live by the maxim “I will pass away soon anyway, so why bother”. That does not help our children, and the next convenient viewpoint is that technology will save us. It is quite clear that technology will entertain us, but there are legitimate doubts that technology can be relied on for environmental salvation.

The nub of our problem is that we live in a world that has no leader. There certainly are leaders good and bad in many countries, but there is no supreme leader who can tell all the world’s peoples to act sustainably, and to be the police chief if they do not (Mearsheimer 2018). So burn coal if you wish, and mine coal even if people complain, and spread pollution as your individual right in spite of the clear rules of sustainable living. And the key is that you can ban mining and burning coal in one advanced country, but you have no power to tell other countries that they must do the same for the good of the Earth.   

When Nicholas Stern in 2006 released his 692-page report on the effect of global warming on the world’s economy, he summarized it this way:

  • there is still time to avoid the worst impacts of climate change, if we take strong action now
  • climate change could have very serious impacts on growth and development
  • the costs of stabilising the climate are significant but manageable; delay would be dangerous and much more costly
  • action on climate change is required across all countries, and it need not cap the aspirations for growth of rich or poor countries
  • a range of options exists to cut emissions; strong, deliberate policy action is required to motivate their take-up
  • climate change demands an international response, based on a shared understanding of long-term goals and agreement on frameworks for action.

The comments of some of the reviewers echoed that “the Stern Review was critically important in moving the climate issue from one of science to one of economics”. The Dasgupta Report of 2021 devotes 606 pages to the economics of biodiversity and perhaps will be lauded as moving the biodiversity issue from the realm of science to the realm of economics. The realms of science and of economics are intertwined, as the current Covid epidemic illustrates all too well. But I think it is a mistake to convert human beings into Homo oeconomicus because the world of biodiversity should not be worthy of protection solely because of its economic value to humans. There are many values that are of higher importance than economic values.

It is nevertheless important to align economic policies with biodiversity protection, and there is already an enormous literature discussing this from one extreme (Gray and Milne 2018) to another (Maron et al. 2018). Ecologists have tried mightily to incorporate our ecological world view into the economic realities but with only limited success (Constanza et al. 2017). The history of human treatment of nature is not very inviting to consider, and I do not like to project the past linearly on the future. But even in this pandemic one sees too many people who ignore all reasonable requests to alleviate problems, and the political systems of our day are so weak when it comes to protecting nature that most policy people seem to think that protecting a few small parks and reserves is enough. We certainly value the David Attenborough presentations on our TV but the need for real world responses seems muted and very slow to develop. I fear that economic science will do little better than biodiversity science to stop the juggernaut, but I hope to be wrong. To date the Titanic paradigm fits the facts too closely. If you are optimistic, go back and read the Stern Report of 2006 and then the Dasgupta Report of 2021. Progress?

Costanza, R., et al. (2017). Twenty years of ecosystem services: How far have we come and how far do we still need to go? Ecosystem Services 28, 1-16. doi: 10.1016/j.ecoser.2017.09.008.

Dasgupta, P. (2021) The Economics of Biodiversity: The Dasgupta Review. (London: HM Treasury. Available at: www.gov.uk/official-documents.

Gray, R. and Milne, M.J. (2018). Perhaps the Dodo should have accounted for human beings? Accounts of humanity and (its) extinction. Accounting, Auditing, & Accountability 31, 826-848. doi: 10.1108/AAAJ-03-2016-2483.

Maron, M., et al. (2018). The many meanings of No Net Loss in environmental policy. Nature Sustainability 1, 19-27. doi: 10.1038/s41893-017-0007-7.

Mearsheimer, J.J. (2018) ‘The Great Delusion: Liberal Dreams and International Realities.’ (Yale University Press: New Haven.). ISBN: 978-0-300-24856-2

Stern, N. (2006). The Economics of Climate Change: The Stern Review. (London: HM Treasury). ISBN number: 0-521-70080-9 (Cambridge University Press, 2007).