Category Archives: Biology Education

On the Focus of Biodiversity Science

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

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

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

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

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

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

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

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

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

On an Experimental Design Mafia for Ecology

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Ecologist A does an experiment and publishes Conclusions G and H. Ecologist B reads this paper and concludes that A’s data support Conclusions M and N and do not support Conclusions G and H. Ecologist B writes to Journal X editor to complain and is told to go get stuffed because Journal X never makes a mistake with so many members of the Editorial Board who have Nobel Prizes. This is an inviting fantasy and I want to examine one possible way to avoid at least some of these confrontations without having to fire all the Nobel Prize winners on the Editorial Board.

We go back to the simple question: Can we agree on what types of data are needed for testing this hypothesis? We now require our graduate students or at least our Nobel colleagues to submit the experimental design for their study to the newly founded Experimental Design Mafia for Ecology (or in French DEME) who will provide a critique of the formulation of the hypotheses to be tested and the actual data that will be collected. The recommendations of the DEME will be nonbinding, and professors and research supervisors will be able to ignore them with no consequences except that the coveted DEME icon will not be able to be published on the front page of the resulting papers.

The easiest part of this review will be the data methods, and this review by the DEME committee will cover the current standards for measuring temperature, doing aerial surveys for elephants, live-trapping small mammals, measuring DBH on trees, determining quadrat size for plant surveys, and other necessary data collection problems. This advice alone should hypothetically remove about 25% of future published papers that use obsolete models or inadequate methods to measure or count ecological items.

The critical part of the review will be the experimental design part of the proposed study. Experimental design is important even if it is designated as undemocratic poppycock by your research committee. First, the DEME committee will require a clear statement of the hypothesis to be tested and the alternative hypotheses. Words which are used too loosely in many ecological works must be defended as having a clear operational meaning, so that idea statements that include ‘stability’ or ‘ecosystem integrity’ may be questioned and their meaning sharpened. Hypotheses that forbid something from occurring or allow only type Y events to occur are to be preferred, and for guidance applicants may be referred to Popper (1963), Platt (1964), Anderson (2008) or Krebs (2019). If there is no alternative hypothesis, your research plan is finished. If you are using statistical methods to test your hypotheses, read Ioannidis (2019).

Once you have done all this, you are ready to go to work. Do not be concerned if your research plan goes off target or you get strange results. Be prepared to give up hypotheses that do not fit the observed facts. That means you are doing creative science.

The DEME committee will have to be refreshed every 5 years or so such that fresh ideas can be recognized. But the principles of doing good science are unlikely to change – good operational definitions, a set of hypotheses with clear predictions, a writing style that does not try to cover up contrary findings, and a forward look to what next? And the ecological world will slowly become a better place with fewer sterile arguments about angels on the head of a pin.

Anderson, D.R. (2008) ‘Model Based Inference in the Life Sciences: A Primer on Evidence.‘ (Springer: New York.) ISBN: 978-0-387-74073-7.

Ioannidis, J.P.A. (2019). What have we (not) learnt from millions of scientific papers with P values? American Statistician 73, 20-25. doi: 10.1080/00031305.2018.1447512.

Krebs, C.J. (2020). How to ask meaningful ecological questions. In Population Ecology in Practice. (Eds D.L. Murray and B.K. Sandercock.) Chapter 1, pp. 3-16. Wiley-Blackwell: Amsterdam. ISBN: 978-0-470-67414-7

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

Popper, K. R. (1963) ‘Conjectures and Refutations: The Growth of Scientific Knowledge.’ (Routledge and Kegan Paul: London.). ISBN: 9780415285940

On Logging Old Growth Forests

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Old growth forests in western Canada and many parts of the Earth are composed of very large trees whose diameters are measured in meters and whose heights are measured in football field lengths. The trees in these forests are economically valuable for their wood, and this has produced a conflict that almost all governments wish to dodge. I do not want to speak here as a terrestrial ecologist but as a human being to discuss the consequences of logging these old growth forests.

As I write this there are a mob of young people blockading the roads into old-growth forest stands in southwestern British Columbia to prevent the logging of some of the largest trees remaining in coastal western Canada. Their actions are all illegal of course because the government has given permission to companies to log these large trees, the classic case of ‘we need jobs’. We certainly need jobs, and we need wood, but if you ask the citizens of British Columbia if these very large trees should be logged you get a resounding majority of NO votes. The government is adept at ignoring the majority will here, it is called democracy.

My simple thought is this. These trees are 500 to 1000 years old. Cut them all down and your children will never see a big tree, or their children or perhaps 25 generations of children, since the foresters say that this is sustainable logging because, if left alone, the forest will regenerate into large old growth trees again by the year 2900. A splendid program for all except for our children for the nest 800 years.

The other ecological issue of course is that these forests form an ecosystem, so it is not just the loss of large old trees but all the other plants and animals in this ecosystem that will be lost. To be sure you can argue that all this forest management is completely sustainable, and you will be able to see this clearly if you are still alive in 2900. Sustainability has unfortunately become a meaningless term in much of our forest land management. Forest management could become sustainable, as many ecologists have been saying for the last 50 years, but as with agriculture the devil is in the details of what this actually means. And if the forest management plan to retain old growth is to keep 6 very large trees somewhere in coastal British Columbia, each one surrounded by a fence and a ring of high-rise hotels for tourists of the future to see “old growth”, then we are well on our way there.

Guz, J. and Kulakowski, D. (2020). Forests in the Anthropocene. Annals of the American Association of Geographers 110, 1-11. doi: 10.1080/24694452.2020.1813013.

Lindenmayer, D.B., et al. (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.

Thorn, S., et al. (2020). The living dead: acknowledging life after tree death to stop forest degradation. Frontiers in Ecology and the Environment 18, 505-512. doi: 10.1002/fee.2252.

Watson, J.E.M., et al. (2018). The exceptional value of intact forest ecosystems. Nature Ecology & Evolution 2, 599-610. doi: 10.1038/s41559-018-0490-x.

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 biodiversity research be directed?

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

On Ecological Models and the Coronavirus

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

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

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

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

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

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

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

On Fires in Australia

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The fires of Australia in their summer 2019-20 are in the news constantly, partly because the media survive on death and destruction and partly because to date we have never seen a whole continent burn up. It is hardly a ‘Welcome to the Anthropocene”  kind of event to celebrate, and the northern media display the fires as nearly all news of the Southern Hemisphere is treated, something unusual, often bad, but of no general importance to the real world of the Northern Hemisphere.

What do we hear from a cacophony of public opinion?

“Nothing unusual. We have always had fires in the past. Why in 1863…..”
“Nothing to do with climate change. Climate has always been changing….(see point 1)
“Main cause had been Green Policies. If we had more forestry, there would have been many fewer trees to burn….”
“Inadequate controlled burning because of the Greens’ policies….(see point 3)
“Why doesn’t the Government do something about this?”
“Fortunately these fires are a rare event and not likely to occur again…….

In reply an ecologist might offer these facts:

  1. Much research by plant geographers and ecologists have shown how many plant communities are dominated by fire. The boreal forest is one, the chaparral of Southern California is another, the grasslands of Africa and the Great Plains of the USA are yet more.
  2. By preventing fire in these communities over time the fuel load builds up so that, should there be a subsequent fire, the fire severity would be very high.
  3. By building houses, towns, and cities in these plant communities fire danger increases, and an active plan of fire management must be implemented. Most of these plans are effective for normal fires but for extreme conditions no fire management plan is effective.
  4. Climate change is now producing extreme conditions that were once very rare but are now commonly achieved. With no rainfall, high winds, and temperatures over 40-45ºC fires cannot be contained. Severe fires generate their own weather that accelerates fire spread with embers being blown kilometers ahead of the active fire front.
  5. The long-term plan to have controlled patch burns to relieve these fire conditions are impossible to implement because they require no wind, low temperatures, and considerable person-power to prevent controlled burns getting away from containment lines should the weather change.

Since a sizeable fraction of dangerous fires are deliberately set by humans, methods to detect and prevent this behaviour could help in some cases. Infrastructure such as power lines could be upgraded to reduce the likelihood of falling power poles and lines shorting out. All this will cost money, and the less the fire frequency, the fewer the people willing to pay more taxes to reduce public risk. Some serious thinking is needed now because Australia 2020 is just the start of a century of fire, drought, floods, and high winds. We do not need the politicians of 2050 telling us “why didn’t someone warn us?

There is a very large literature on fire in human landscapes (e.g. Gibbons et al. 2012), and I include only a few references here. They illustrate that the landscape effects of fire are multiple and area specific. Much more field research is needed, and landscape ecology has a vital role to play in understanding and managing the interface of humans and fire.

Badia, A. et al. (2019). Wildfires in the wildland-urban interface in Catalonia: Vulnerability analysis based on land use and land cover change. Science of The Total Environment 673, 184-196. doi: 10.1016/j.scitotenv.2019.04.012.

Gibbons, P, et. al. (2012) Land management practices associated with house loss in wildfires. PLoS ONE 7(1): e29212. https://doi.org/10.1371/journal.pone.0029212

Gustafsson, L. et al. (2019). Rapid ecological response and intensified knowledge accumulation following a north European mega-fire. Scandinavian Journal of Forest Research 34, 234-253. doi: 10.1080/02827581.2019.1603323.

Minor, J. and Boyce, G.A. (2018). Smokey Bear and the pyropolitics of United States forest governance. Political Geography 62, 79-93. doi: 10.1016/j.polgeo.2017.10.005.

Ramage, B.S., O’Hara, K.L., and Caldwell, B.T. (2010). The role of fire in the competitive dynamics of coast redwood forests. Ecosphere 1(6), art20. doi: 10.1890/ES10-00134.1.

The Central Predicament of Ecological Science

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

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

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

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

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

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

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

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

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

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

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

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

On Random Sampling and Generalization in Ecology

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Virtually every introduction to statistics book makes the point that random sampling is a critical assumption that underlies all statistical inferences. It is assumption #1 of statistical inference and it carries with it an often-hidden assumption that in trying to make your inference, you have clearly defined what the statistical population is that you are sampling. Defining the ‘population’ under consideration should perhaps be rule # 1, but that is usually left as a vague understanding in many statistical studies. As an exercise consult a series of papers on ecological field studies and see if you can find a clear statement of what the ‘population’ under consideration is. An excellent example of this kind of analysis is given by Ioannidis (2003, 2005).

The problem of random sampling does not occur in theoretical statistics and all effort is concentrated on mathematical correctness. This is illustrated well in the polls we are subjected to on political or social issues, and in the medical studies that we hear about daily. The social sciences have considered sampling for polls in much more detail that have biologists. In a historical overview (Lusinchi 2017) provides an interesting and useful analysis of how pollsters have over the years bent the science of statistical inference to their methods of polling to provide an unending flow of conclusions about who will be elected, or which coffee is better tasting. By confounding sample size with an approach to Truth and ignoring the problem of random sampling, the public has been brainwashed to believe what should be properly labeled as ‘fake news’.

What has all of this got to do with the science of ecology? Much of the data we accumulate is uncertain when we ask what is the ‘population’ to which it applies. If you are concerned about the ecology of sharks, you face the problem that most species of shark have never been studied (Ducatez 2019). If you are interested in fish populations, for example, you may find that the fish you catch with hooks are not a random sample of the fish population (Lennox et al. 2017). If you are studying the trees in a large woodlot, that may be your universe for statistical purposes. Interest then shifts to the question of how much you will generalize to other woodlots over what geographical space, a question too rarely discussed in data papers. In an ideal world we would sample several woodlots randomly selected from a larger sample of similar woodlots, so that we could infer processes that were common to woodlots in general.

There are a couple of problems that confound ecologists at this point. No series of woodlots or study sites in general are identical, so we assume they are a collective of ‘very similar’ woodlots about which we could make an inference. Alternatively, we can simply state that we wish to make inferences about only this single woodlot, it is our total population. At this point your supervisor/boss will say that he or she is not interested only in this one woodlot but much more general conclusions, so you will be cut from research funding for having too narrow an interest.

The solution is in general to study one ‘woodlot’ and then generalize to all ‘woodlots’ with no further study on your part, so that it will be up to the next generation to find out if your generalization is right or wrong. While this way of proceeding will perhaps not matter to people interested in ‘woodlots’, it might well matter greatly if your ‘population of interest’ was composed of humans considering a drug for disease treatment. We are further confounded in this era of climate change in dealing with changing ecosystems, so that a study in 2000 about coral reef fish communities could be completely different if it were repeated in 2040 as oceans warm.

Back to random sampling. I would propose that random sampling in ecological systems is impossible and cannot be achieved in a global sense. Be concerned about local processes and sample accordingly. Descriptive ecology must come to the rescue here, so that we know as background information (for example) that trees grow slower as they age, that tree growth varies from year to year, that insect attacks vary with summer temperature, and so on, and sample accordingly following your favourite statistician. There are many very useful statistical techniques and sampling designs you can use as an ecologist to achieve random sampling on a local scale, and statisticians are most useful to consult to validate the design of your field studies.

But it is important to remember that your results and conclusions even though carried out with a perfect statistical design cannot ensure that your generalizations are correct in time or in space. The use of meta-analysis can assist in validating generalizations when enough replicated studies are available, but there are problems even with this approach (Siontis and Ioannidis 2018). Continued discussion of p-values in ecology could benefit much from similar discussions in medicine where funding is higher, and replication is more common (Ioannidis 2019b; Ioannidis 2019a).

All these statistical issues provide a strong argument as to why ecological field studies and experiments should never stop, and all our studies and conclusions are temporary signposts along a path that is never ending.

Ducatez, S. (2019). Which sharks attract research? Analyses of the distribution of research effort in sharks reveal significant non-random knowledge biases. Reviews in Fish Biology and Fisheries 29, 355-367. doi: 10.1007/s11160-019-09556-0.

Ioannidis, J.P.A. (2005). Contradicted and initially stronger effects in highly cited clinical research. Journal of the American Medical Association 294, 218-228. doi: 10.1001/jama.294.2.218.

Ioannidis, J.P.A. (2005). Why most published research findings are false. PLOS Medicine 2, e124. doi: 10.1371/journal.pmed.0020124.

Ioannidis, J.P.A. (2019a). What have we (not) learnt from millions of scientific papers with p values? American Statistician 73, 20-25. doi: 10.1080/00031305.2018.1447512.

Ioannidis, J.P.A. (2019b). The importance of predefined rules and prespecified statistical analyses: do not abandon significance. Journal of the American Medical Association 321, 2067-2068. doi: 10.1001/jama.2019.4582.

Lennox, R.J., et al. (2017). What makes fish vulnerable to capture by hooks? A conceptual framework and a review of key determinants. Fish and Fisheries 18, 986-1010. doi: 10.1111/faf.12219.

Lusinchi, D. (2017). The rhetorical use of random sampling: crafting and communicating the public image of polls as a science (1935-1948). Journal of the History of the Behavioral Sciences 53, 113-132. doi: 10.1002/jhbs.21836.

Siontis, K.C. and Ioannidis, J.P.A. (2018). Replication, duplication, and waste in a quarter million systematic reviews and meta-analyses. Circulation Cardiovascular Quality and Outcomes 11, e005212. doi: 10.1161/circoutcomes.118.005212.

Why do Scientists Reinvent Wheels?

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We may reinvent wheels by repeating research that has already been completed and published elsewhere. In one sense there is no great harm in this, and statisticians would call it replication of the first study, and the more replication the more we are convinced that the results of the study are robust. There is a problem when the repeated study reaches different results from the first study. If this occurs, there is a need to do another study to determine if there is a general pattern in the results, or if there are different habitats with different answers to the question being investigated. But after a series of studies is done, it is time to do something else since the original question has been answered and replicated. Such repeated studies are often the subject of M.Sc. or Ph.D. theses which have a limited 1-3-year time window to reach completion. The only general warning for these kinds of replicated studies is to read all the old literature on the subject. There is a failure too often on this and reviewers often notice missing references for a repeated study. Science is an ongoing process but that does not mean that all the important work has been carried out in the last 5 years.

There is a valid time and place to repeat a study when the habitat for example has been greatly fragmented or altered by human land use or when climate change has made a strong impact on the ecosystem under study. The problem in this case is to have an adequate background of data that allows you to interpret your current data. If there is a fundamental problem with ecological studies to date it is that we have an inadequate baseline for comparison for many ecosystems. We can conclude that a particular ecosystem is losing species (due to land use change or climate) only if we know what species comprised this ecosystem in past years and how much the species composition fluctuated over time. The time frame desirable for background data may be only 5 years for some species or communities but for many communities it may be 20-40 years or more. We are too often buried in the assumption that communities and ecosystems have been in equilibrium in the past so that any fluctuations now seen are unnatural. This time frame problem bedevils calls for conservation action when data are deficient.

The Living Planet Report of 2018 has been widely quoted as stating that global wildlife populations have decreased 60% in the last 4 decades. They base their analysis on the changes in 4000 vertebrate species. There are about 70,000 vertebrate species on Earth, so this statement is based on about 6% of the vertebrates. The purpose of the Living Planet Report is to educate us about conservation issues and encourage political action. No ecologist in his or her right mind would question this 60% quotation lest they be cast out of the profession, but it is a challenge to the graduate students of today to analyze this statistic to determine how reliable it is. We all ‘know’ that elephants and rhinos are declining but they are hardly a random sample. The problem in a nutshell is that we have reliable long-term data on perhaps 0.01% or less of all vertebrate species. By long term I suggest we set a minimal limit of 10 generations. As another sobering test of these kinds of statements I suggest picking your favorite animal and reading all you can on how to census the species and then locate how many studies of this species meet the criteria of a good census. The African elephant could be a good place to start, since everyone is convinced that it has declined drastically. The information in the Technical Supplement is a good starting point for a discussion about data accuracy in a conservation class.

My advice is that ecologists should not without careful thought repeat studies that have already been carried out many times on common species . Look for gaps in the current wisdom. Many of our species of concern are indeed declining and need action but we need knowledge of what kinds of management actions are helpful and possible. Many of our species have not been studied long enough to know if they are under threat or not. It is not helpful to ‘cry wolf’ if indeed there is no wolf there. We need precision and accuracy now more than ever.

World Wildlife Fund. 2018. Living Planet Report – 2018: Aiming Higher. Grooten, M. and Almond, R.E.A.(Eds). WWF, Gland, Switzerland. ISBN: 978-2-940529-90-2.
https://wwf.panda.org/knowledge_hub/all_publications/living_planet_report_2018/