Category Archives: Climate Emergency

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.

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).

On the Bonn Challenge: Tree Restoration and the Climate Emergency

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“Plant a tree and save the world” is the short version of the Bonn Challenge of 2011 and the UN Decade of Ecosystem Restoration 2021-2030 (Stanturf and Mansourian 2020), and so here we are with a major ecological challenge for the decade we have just started. Planting trees around the world to restore 350 million hectares of degraded land is the goal, and it is a challenge that ecologists must think clearly about to avoid failure of another grand scheme.

Restoring ecosystems is not easy as we have already learned to our dismay. What began as a relatively simple restoration of old fields used in agriculture, a few hectares of ploughed ground surrounded by forest or grassland, has now morphed into very large areas devastated by forest fires, insect outbreaks, or drought. The largest forest fires in Arizona prior to the year 2000 were 20,000 ha, but after prolonged drought by 2020 they have reached nearly 300,000 ha (Falk 2017). The larger and more severe the fire, the greater the distance seed must disperse to recolonize burnt areas, and hence the recovery from large fires differs dramatically from the recovery from small or patchy fires.

I concentrate here on forest restoration, but always with the caveat in mind that the trees are not the forest – there are a plethora of other species involved in the forest ecosystem (Temperton et al. 2019). The restoration of forest landscapes is driven by the estimate that forest originally covered about 5.9 billion ha of the Earth but at the present time there is about 4 billion ha of forest remaining. Restoration of degraded ecosystems has always been a good idea, and this program can now be tied in with the climate emergency. New trees will remove CO2 from the air as they grow so we can score 2 points with every tree we plant (Bernal and Pearson 2018).  

The scale of plans for the UN Decade of Ecosystem Restoration 2021-2030 are challenging and Stanturf and Mansourian (2020) provide current details country by country. For example, Brazil a country of 836 million ha has pledged to restore 12 million ha (1.44%), with some countries like Spain and Russia so far not pledging any Bonn Challenge restoration. The take-up of actual restoration is uneven globally. The USA has committed to restore 12 million ha to the Bonn Challenge, but Canada has made no formal commitment, although the federal government has proposed to plant 2 billion trees during this decade to counteract climate change.  

Many problems arise with every ecological restoration. Not the least is the time frame of the recovery of damaged ecosystems. Forests recover slowly even when carefully tended, and 100 years might be a partial target for temperate forests. For North American west-coast forests a 400+-year time frame might be a target. Most private companies and governments can not even conceive of this scale of time. For those who think everything should work faster than this, Moreno-Mateos et al. (2020) report a large sample of >600 restored wetlands that recovered to only 74% of the target value in 50-100 years. Schmid et al. (2020) found that the microbial community of a lignite mine in Germany had not recovered to the control level even after 52 years. Ecological time does not always conform readily to industrial time.

Other constraints blur the grand global picture. Restoration with trees should not be done on tropical grasslands because of their inherent biodiversity values (c.f. Silveira et al. 2020 for excellent examples), nor can we restore trees on rangeland that is used for agricultural production lest we engage in robbing agricultural Peter to pay forester Paul (Vetter 2020). These important ecological critiques must be incorporated into country-wide plans for reforestation whose primary aim might be CO2 capture. Again the devil is in the details, as Vetter (2020) clearly articulates.  

The Bonn Challenge remains ongoing, waiting for another review after 2030. Who will remember what was promised, and who will be given the awards for achievements reached? What quantitative goals exactly have been promised, and what happens if they slip to 2050 or 2070?  

Bernal, B., Murray, L.T., and Pearson, T.R.H. (2018). Global carbon dioxide removal rates from forest landscape restoration activities. Carbon Balance and Management 13, 22. doi: 10.1186/s13021-018-0110-8.

Bonnesoeur, V., Locatelli, B., Guariguata, M.R., Ochoa-Tocachi, B.F., Vanacker, V. et al. (2019). Impacts of forests and forestation on hydrological services in the Andes: A systematic review. Forest Ecology and Management 433, 569-584. doi: 10.1016/j.foreco.2018.11.033.

Falk, Donald A. (2017). Restoration ecology, resilience, and the axes of change. Annals of the Missouri Botanical Garden 102, 201-216, 216. doi: 10.3417/2017006.

Moreno-Mateos, D., et al. (2020). The long-term restoration of ecosystem complexity. Nature Ecology & Evolution 4, 676-685. doi: 10.1038/s41559-020-1154-1.

Silveira, F.A.O., Arruda, A.J., Bond, W., Durigan, G., Fidelis, A., et al. (2020). Myth-busting tropical grassy biome restoration. Restoration Ecology 28, 1067-1073. doi: 10.1111/rec.13202.

Stanturf, J.A. and Mansourian, S. (2020). Forest landscape restoration: state of play.
Royal Society Open Science 7, 201218. doi: 10.1098/rsos.201218.

Temperton, V.M., Buchmann, N., Buisson, E., Durigan, G. and Kazmierczak, L. (2019). Step back from the forest and step up to the Bonn Challenge: how a broad ecological perspective can promote successful landscape restoration. Restoration Ecology 27, 705-719. doi: 10.1111/rec.12989.

Vetter, S. (2020). With Power Comes Responsibility – A rangelands perspective on forest landscape restoration. Frontiers in Sustainable Food Systems 4, 549483. doi: 10.3389/fsufs.2020.549483.

How Much Evidence is Enough?

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

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

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

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

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

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

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

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

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

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

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

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

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

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

But It is Complicated in Ecology

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

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

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

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

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

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

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

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

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

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

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

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

On a Department of Monitoring Biology

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Begin with the current university structure in North America. Long ago it was simple: a Department of Biology, a Department of Microbiology, a Department of Forestry, and possibly a Department of Fisheries and Wildlife Management. We could always justify a Department of Microbiology because people get sick, a Department of Forestry because people buy wood to build houses, and a Department of Fisheries and Wildlife Management because people fish and hunt. But what are we going to do with a Department of Biology? It rarely deals with anything that will make money, so we divide it into interest groups, a Department of Botany, and a Department of Zoology. All is well. But now a new kid appears on the block, Molecular Biology, and it claims to be able to solve all the issues that were formerly considered the focus of Botany and Zoology and probably several other departments. Give us all the money, the molecular world shouted, and we will solve all your problems and do it quickly. So now we get a complete hassle for money, buildings and prestige, and the world turns on which of the bevy of bureaucrats races to the top to make all the major decisions. If you wish to have proof of concept, ask anyone you can find who teaches at a university if he or she was ever consulted about what direction the university should take.

At this point we begin to proceed based on ‘follow the money’. So, for example if the Department of Forestry gets the most money from whomever, it must get the biggest buildings, the largest salaries, and the newest appointments. So soon you have a system of intrigue that would rival the Vatican. The winners of late are those departments that have most to do with people, health, and profit. So Medical Schools march on, practical matters like economics and engineering do well, and molecular biology rises rapidly.

What has happened to the old Departments of Botany and Zoology? They make no profit; their only goal is to enrich our lives and our understanding of the world around us. How can we make them profitable? A new program races to the rescue, a Department of Biodiversity, which will include everyone in plant, animal and microbe science who cannot get into one of the more practical, rich, existing departments. The program now is to convince the public and the governments that biodiversity is important and must be funded more. David Attenborough to the fore, and we are all abandoning the old botany and zoology and moving to biodiversity.

Now the problem arises for ecologists. Biodiversity includes everything, so where do we start? If we have so far described and named only about 15% of the life on Earth, should we put all our money into descriptive taxonomy? Should we do more biogeography, more ecology, more modelling, or more taxonomy, or a bit of all? So, the final question of our quest arrives: what should we be doing in a Department of Biodiversity if indeed we get one?

If you have ever been involved in herding cats, or even sheep without a dog you can imagine what happens if you attempt to set a priority in any scientific discipline. The less developed the science, the more the arguments about where to put our money and people. Ecology is a good example because it has factions with no agreement at all about what should be done to hasten progress. The result is that we fall back on the Pied Pipers of the day, form bandwagons, and move either forward, sideways, or backwards depending on who is in charge.

So, let us step back and think amid all this fighting for science funding. The two major crises of our time are human population growth and the climate change emergency. In fact, there is only one major crisis, climate change, because as it apparently progresses, everything will be overwhelmed in a way only few can try to guess (Wallace-Wells 2019, Lynas 2020). After some discussion you might suggest that we do two things in biology: first, get a good grip on what we have now on Earth, and second, keep monitoring life on Earth as the climate emergency unravels so that we can respond with mitigation as required. This is not to say we should stop doing other things. We should be more than unifactorial scientists, and it may be a small recommendation to the world of thinkers that we consider endowing at least some universities with a Department of Monitoring Biology and endow it with enough funding to do the job well. (Lindenmayer 2018; Lindenmayer et al. 2018; Nichols et al. 2019). It might be our best investment in the future of biology.

Lindenmayer, D. (2018). Why is long-term ecological research and monitoring so hard to do? (And what can be done about it). Australian Zoologist 39: 576-580. doi: 10.7882/az.2017.018.

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.

Lynas, Mark (2020) ‘Our Final Warning: Six Degrees of Climate Emergency’. 4th Estate, Harper Collins, London. E book ISBN: 978-0008308582

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

Wallace-Wells, David (2019) ‘The Uninhabitable Earth: Life After Warming ‘ Tim Duggan Books: New York. 304 pp. ISBN: 978-0-525-57670-9.  

How Should We Test Global Models in Ecology?

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

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

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

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

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

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

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

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

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

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

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

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