Category Archives: General Ecology

Whither Demography in an Era of Biodiversity Science?

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Biodiversity science has overtaken traditional ecological science in an important way that bears some discussion. Biodiversity science seeks as its main goal to protect species from declining to extinction. It overlaps traditional population and community ecology partly by concentrating on iconic species that are declining in abundance and thus trying to prevent species loss, but the major focus of biodiversity science is on the species composition of communities and ecosystems and trying to understand what factors are driving deleterious changes. This task is difficult to complete currently because of a shortage of research time, person-power and money, so we are driven to select relatively few ecosystems to concentrate our conservation efforts upon. If we cannot do everything for all species, we must choose what to do at the present time, and this releases a cascade of discussions and arguments about what species are ‘flagship’, “umbrella”, or “keystone” in any particular community or ecosystem (Barua 2011).

Now we can go in two directions. We can take the simplest route and say that all species are of equal importance, so the objective of biodiversity science becomes ‘occupancy” – is species X still existing in ecosystem Y? Occupancy can be established in a variety of ways from simple visual sightings, traps, cameras, e-DNA, to electronic sound recording devices. Occupancy for species in a particular ecosystem is a useful parameter for biodiversity studies but it is alpha-level ecology for understanding community or ecosystem dynamics. Determining occupancy every month, year, or decade will provide a start in community and ecosystem understanding but in order to achieve its goal as a science it needs population and community ecology to measure and understand the dynamics underlying occupancy, and this is the more complicated route that we can take. The defining science for this second level of understanding comes from dynamics, both population and community dynamics.

Population dynamics is necessary for determining if a particular species is declining in numbers or biomass, and what the causes are of the observed trends. We are led into demography, the measurement of births, deaths, and movements in animals and the equivalent parameters in plants. But now we run into the most serious problem of determining what parameters are the causal agents of declines in abundance and what procedures will alleviate species declines. If we have many species in our community or ecosystem, the requirements for research are extravagant, given the current workers and dollars currently available for environmental science. All ecologists want to protect biodiversity but how might we best achieve that goal?

We fall back at this point into simple general procedures for biodiversity conservation like designation of national parks or protected areas with the hope that the biodiversity of the designated area will not decline. We do not have the person-power to have frequent occupancy surveys for any national park, much less to have the investigations of why an iconic species is declining in an area. At present we must fall back on ‘umbrella species’ or ‘flagship species’ (Simberloff 1998). There is an extensive literature on this approach to biodiversity conservation and recent reviews, some critical (Tälle et al. 2023), others somewhat more positive (Sumbh and Hof 2022, Clark-Wolf et al. 2024), combining this approach with food web structure (Wang and Zhou 2023).   

Complicating the whole issue of protecting biodiversity is the issue of cryptic species, undescribed species, and rare species that are capable of taxonomic and ecological resolution but only at a large cost and a long timeframe to achieve results (Cheng et al. 2024). Once we are successful in protecting our communities and ecosystems, we immediately face the demographic issue of what affects the abundance of all the species of interest, and then the social and political issue of the funds available for conservation of these species. We need to bring the approaches of biodiversity science and classical demographic ecology together to achieve conservation goals. We can do this only by recognizing that knowing occupancy is not enough to achieve conservation success, and we need to follow up with population and community ecology within the context of food webs so that we can understand trends in abundance and finally propose possible actions for conservation management. We have much to do.

Barua, M. (2011) Mobilizing metaphors: the popular use of keystone, flagship and umbrella species concepts. Biodiversity and Conservation, 20, 1427-1440.doi:10.1007/s10531-011-0035-y.

Cheng, R., Luo, A., Orr, M., Ge, D., Houu, Z.e., Qu, Y., Guo, B., Zhang, F., Sha, Z., Zhao, Z., Wang, M., Shi, X., Han, H., Zhou, Q., Li, Y., Liu, X., Shao, C., Zhang, A., Zhou, X. & Zhu, C. (2024) Cryptic diversity begets challenges and opportunities in biodiversity research. Integrative Zoology, (in press). doi: 10.1111/1749-4877.12809.

Clark-Wolf, T.J., Holt, K.A., Johansson, E., Nisi, A.C., Rafiq, K., West, L., Boersma, P.D., Hazen, E.L., Moore, S.E. & Abrahms, B. (2024) The capacity of sentinel species to detect changes in environmental conditions and ecosystem structure. Journal of Applied Ecology, (in press). doi: 10.1111/1365-2664.14669.

Simberloff, D. (1998) Flagships, umbrellas, and keystones: is single-species management passe in the landscape era? Biological Conservation, 83, 247-257.doi: 10.1016/S0006-3207(97)00081-5.

Sumbh, O. & Hof, A.R. (2022) Can pikas hold the umbrella? Understanding the current and future umbrella potential of keystone species Pika (Ochotona spp.). Global Ecology and Conservation, 38, e02247.doi: 10.1016/j.gecco.2022.e02247.

Tälle, M., Ranius, T. & Öckinger, E. (2023) The usefulness of surrogates in biodiversity conservation: A synthesis. Biological Conservation, 288; e110384. doi: 10.1016/j.biocon.2023.110384.

Wang, Q., Li, X.C. & Zhou, X.H. (2023) New shortcut for conservation: The combination management strategy of “keystone species” plus “umbrella species” based on food web structure. Biological Conservation, 286, 110265.doi: 10.1016/j.biocon.2023.110265.

On Discourse and Evidence

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A major problem that bedevils society as well as science today is the distinction between opinion and evidence. The world is awash in opinions and short of evidence for many questions that fill the news media as well as the scientific literature. In trying to evaluate this statement we should recognize that there are many important issues for which we have no evidence but only beliefs. A current discussion in the news media is whether or not any particular country should spend 2% of its GDP on military expenses. Much hot air follows from these discussions because as an individual person you have no evidence one way or the other for different points of view, spend more, spend less. You will have an opinion that everyone should respect but for this and many issues any evidence that can be cited is vague. Discussion on many issues like this example are important and should be civilized but often are not.

But there are a range of issues for which scientific evidence is available. The first rule of discourse on these issues ought to be that you as a person are allowed to have any opinion you wish but you must be able to present evidence to support your opinions. You should be allowed as a person to proclaim that the Earth is not round but flat and provide the evidence one way or the other. More serious issues with different opinions involve issues like vaccination for a particular disease. On these issues scientists can only advise and provide evidence. But if a vaccine X for example has a complex side effect rate of 1 person in 1000, you could always argue that you are that one person and you are opposed to vaccination X.

How does all this relate to ecological science? First, we should recognize that many of the arguments in the ecological literature are about opinions rather than evidence. In many cases this should lead to more studies of particular problems to gather more evidence. But as we see with climate change research the evidence is accumulating but varies greatly in quality and time span from area to area and from taxonomic group to taxonomic group. We cannot agree whether our research should be focused on the oceans or on land, or on birds rather than mammals or insects. We cannot do everything, and the consequence is that ecological research funding is driven in many directions depending on who is on the committee dispersing funding and what their opinions are. The result is that for large scale problems like climate change we have convinced most people that it is a reality, but we cannot agree on the details of future change. So, we build models with past data and try to project them into the future with uncertain confidence.

The consequence is that the ecological world is awash in opinions in the same way as other parts of society, and in support of opinions the evidence often gets lost. The main problem here is that opinions are generated rapidly while evidence accumulates slowly. We see this more readily in medical science in which the media trumpets treatment X rather than Y with opinions and little evidence. We cannot demand answers to important questions tomorrow when the problem spans years or decades for evidence to accumulate. 

Ecology like every science becomes more complicated with age, and a fisheries biologist trained 40 years ago lives in a different world from one trained today. The accumulated evidence from research changes our list of important questions illustrated well by the reviews of progress in conservation science by Sutherland et al. (2022, 2023) and Christie et al. (2023), in predator- prey dynamics by Sheriff et al. (2020), wildlife management by Hone et al. (2023), and in insect conservation by Saunders et al. (2020). Understanding and solving ecology problems must rely more on evidence and less on opinions.

Christie, A.P., Christie, A.P., Morgan, W.H. & Sutherland, W.J. (2023) Assessing diverse evidence to improve conservation decision‐making. Conservation Science and Practice, 5, e13024.doi. 10.1111/csp2.13024

Hone, J., Drake, A. & Krebs, C.J. (2023) Evaluation Options for Wildlife Management and Strengthening of Causal Inference. BioScience, 73, 48-58.doi: 10.1093/biosci/biac105.

Saunders, M.E., Janes, J.K. & O’Hanlon, J.C. (2020) Moving On from the Insect Apocalypse Narrative: Engaging with Evidence-Based Insect Conservation. BioScience, 70, 80-89.doi: 10.1093/biosci/biz143.

Sheriff, M.J., Peacor, S.D., Hawlena, D. & Thaker, M. (2020) Non-consumptive predator effects on prey population size: A dearth of evidence. Journal of Animal Ecology, 89, 1302-1316.doi: 10.1111/1365-2656.13213.

Sutherland, W.J. & Jake M. Robinson, D.C.A., Tim Alamenciak, Matthew Armes, Nina Baranduin, Andrew J. Bladon, Martin F. Breed, Nicki Dyas, Chris S. Elphick, Richard A. Griffiths, Jonny Hughes, Beccy Middleton, Nick A. Littlewood, Roger Mitchell, William H. Morgan, Roy Mosley, Silviu O. Petrovan, Kit Prendergast, Euan G. Ritchie,Hugh Raven, Rebecca K. Smith, Sarah H. Watts, Ann Thornton (2022) Creating testable questions in practical conservation: a process and 100 questions. Conservation Evidence Journal, 19, 1-7.doi. 10.52201/CEJ19XIFF2753

Sutherland, W.J., Sutherland, W.J., Bennett, C. & Thornton, A. (2023) A global biological conservation horizon scan of issues for 2023. Trends in Ecology & Evolution, 38, 96-107.doi. 10.1016/j.tree.2022.10.005

Should Ecology Abandon Popper?

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The first question I must ask is whether you the reader have ever heard of Karl Popper. If the answer is no, then you could profit from reading Popper (1963) before you read this. An abbreviated version of the Popperian approach to science is presented in a short paper by Platt (1963) The simplest version of Popper and Platt is that we should have a hypothesis with specific predictions and one or more alternative hypotheses with other predictions, and science advances by finding out which hypotheses could be rejected with empirical evidence. The focus of this blog is on a recent paper by Raerinne (2024) claiming that Popperian ecology is a delusion. This is a claim well worth discussing particularly since most of the sciences progress using a Popperian approach to testing hypotheses.

To begin perhaps we should recognize two kinds of papers that appear in ecological journals. A very large set of ecological papers appear to be largely or entirely descriptive natural history typically of past or present events with no hypotheses in mind. Many of these papers end with a conclusion that could be designated as a hypothesis but with little discussion of alternatives. These papers can be very valuable in giving us the state of populations, communities, or ecosystems with recommendations for changes that should be made to alleviate developing problems. A good example are papers describing forest and grassland fires of recent years which can end with some management recommendations, and perhaps with alternative recommendations. These recommendations usually arise from experience and judgements, and they may or not be valid. The Popperian approach would be to set up hypotheses and test them empirically, but if we are people of action, we press onward with a preferred management action. The non-Popperian approach would be very efficient if we were correct in our diagnosis, and in many cases this approach works well. The basis of the issue here is what is evidence in ecology and how should it be sharpened into recommendations for conservation and management.  

The Popperian approach to ecological science is to recognize problems that require a solution to increase our knowledge base, and to suggest a series of alternative set of mechanisms that could solve or alleviate the problem. Ecological papers supporting this approach can often be recognized by searching for the word “hypothesis” in the text. A simple example of this Popperian approach could be finding the causes of the continuing decline of a commercial fishery. The decline might be due to predation on the target fish or invertebrate, a disease, added pollution to the water body, climate change increasing the water temperature and thus metabolic functions, introduced species of competitors for food or space. One or more of these causal factors could be involved and the job of the ecologist is to find out which one or several are diagnostic. Given the complexity of ecological problems, it is typically not possible to test these alternative hypotheses in one grand experiment, and the typical approach will involve adaptive management or evidence-based conservation (Gillson et al. 2019, Serrouya et al., Westgate et al. 2013). Complexity however should not be used as an excuse to do poor science.

What is the alternative if we abandon Popper? We could adopt the inductive approach and gather data that we put together with our judgement to declare that we have a correct answer to our questions, “seat of the pants” ecology. But this approach is heavily dependent on the idea that “the future will be like the past”. This approach to ecological problems will be most useful for the very short term. The simplest example comes from weather forecasting in which the prognosis for today’s weather is what it was like yesterday with minor adjustments. We could observe trends with this approach but then we must have a statistical model that predicts, for example, that the trend is linear or exponential. But the history of science is that we can do much better by understanding the mechanisms underlying the changes we see. A good overview of the dilemmas of this inductive approach for conservation biology is provided by Caughley (1994). The operative question here is whether the inductive approach achieves problem resolutions more efficiently than the Popperian approach through conjecture and refutation.

Raerinne (2023, 2024) does biology in general and ecology in particular a disservice in criticizing Popper’s approach to ecology by arguing that ecology should not be criticized nor evaluated from the Popperian perspective. I think this judgement is wrong, and Raerinne’s conclusion arises from a philosophical viewpoint which could well have little applicability to how ecologists solve empirical problems in the real world. But you can judge.  

Carducci, A., Federigi, I. & Verani, M. (2020) Airborne transmission and its prevention: Waiting for evidence or applying the Precautionary Principle? Atmosphere, 11 (7), 710.doi: 10.3390/atmos11070710.

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

Gillson, L., Biggs, H. & Rogers, K. (2019) Finding common ground between adaptive management and evidence-based approaches to biodiversity conservation. Trends in Ecology & Evolution, 34, 31-44.doi: 10.1016/j.tree.2018.10.003.

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.

Raerinne, J. (2023) Myths of past biases and progress in biology. Theory in Biosciences, 142, 383-399.doi: 10.1007/s12064-023-00403-2.

Raerinne, J. (2024) Popperian ecology is a delusion. Ecology and Evolution, 14, e11106.doi: 10.1002/ece3.11106.

Serrouya, R., Seip, D.R., Hervieux, D., McLellan, B.N., McNay, R.S., Steenweg, R., Heard, D.C., Hebblewhite, M., Gillingham, M. & Boutin, S. (2019) Saving endangered species using adaptive management. Proceedings of the National Academy of Sciences, 116, 6181-6186.doi: 10.1073/pnas.1816923116 .

Westgate, M.J., Likens, G.E. & Lindenmayer, D.B. (2013) Adaptive management of biological systems: A review. Biological Conservation, 158, 128-139.doi: 10.1016/j.biocon.2012.08.016 .

On What to Read in the Ecological Literature

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Postgraduate students in ecology face a wall of literature that they must come to grips with in their career. Time is limited and unlike the French naturalist Comte de Buffon who produced 36 volumes of Histoire Naturelle from 1749 to 1788, most of us do not have the luxury of several assistants reading the current literature to us during all waking hours (even during meals). So, there are three options available now if you wish to become a scientist. First, you can decide that there was nothing serious written before a specified date like 2008, and then concentrate on the recent literature only. Alternatively, you can decide that all the current wisdom in ecology is summarized in a few books and read them. This option has the danger that your choice of books to read may give you a distorted orientation to ecological science. Thirdly, you may decide that your thesis supervisor is a concentrated source of ecological wisdom and simply do what he or she says. This is certainly the most parsimonious way to proceed but the risk here is that you may find later when looking for a job that your supervisor was considered a fringe player rather than the central cutting edge of future ecological science.

Whatever your decision you will still face a large pile of scientific papers. So, the skill you need to sharpen is how to cull the literature. If you wish to study cone production in Pinus banksiana, you can search for all the literature with this Latin name in the search terms of the Web of Science or a similar source program. Given all that, you can now (I am told) get AI to write your thesis automatically. This is of course nonsense since any specific set of ecological literature will have many contradictory papers, some papers that are outright incorrect because of statistics or experimental design, and others that are speculation rather than data rich. So, you will have to read a great deal to fix on a specific problem within this specified field that you can address with your thesis work. The key question is as always What Next? New ideas, new insights, new speculation are the keys at this point.

Perhaps the most important insight here is that there are many thousands of unanswered questions in science, and ecology may be particularly difficult in having many critical issues that have simply been dropped because they are too difficult. But what was too difficult 10 years ago may be easy to measure now, so advances in understanding are possible. But here you must pick a problem that is solvable, and there are many problems floating around in the ecological literature that are impossible to solve, and others that if solved will be of little use for the critical issues that are now visible. There is no simple guidance here for new scientists. We can see in textbooks and reviews the problems of the past clearly stated and investigated, but the problems of the past that AI or your library can highlight may not be the problems that are most important for the future of our science. Bravery here is desirable but dangerous.

There are other issues that I think worth noting for young ecologists. Read widely. There are many good ecological journals, and do not assume that all you need to read are British ones, or American ones, or Science and Nature. With all due respects, there is much nonsense published in Science and Nature, not to mention lesser renowned journals. Do not assume that only English papers present ecological wisdom. Read sceptically and ask what is the evidence for any conclusion and how good it is. However, a word of caution to postgraduate students is in order here: be careful not to apply these rules to your thesis supervisor’s research. Some things in science are sacred.

Andrew (2020), Fox (2021) and Fox et al (2023) discuss some of the reasons ecological journals do not reach perfection, and their analyses may help relieve your anxiety if your recent paper has been rejected by your favourite journal.

Andrew, N. R. (2020). Design flaws and poor language: Two key reasons why manuscripts get rejected from austral ecology across all countries between 2017 and 2020. Austral Ecology, 45, 505–509.doi: 10.1111/aec.12908.

Fox, C. W. (2021). Which peer reviewers voluntarily reveal their identity to authors? Insights into the consequences of open-identities peer review. Proceedings of the Royal Society B: Biological Sciences, 288(1961), 20211399. doi: 10.1098/rspb.2021.1399.

Fox, C.W., Meyer, J. & Aime, E. (2023) Double‐blind peer review affects reviewer ratings and editor decisions at an ecology journal. Functional Ecology, 37, 1144-1157.doi. 10.1111/1365-2435.14259.

On Critical Evaluation in Ecology

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Science proceeds by “conjecture-and-refutation” if we agree with Karl Popper (1963). There is a rich literature on science in general and ecological science in particular that is well worth a series of graduate discussions even if it is pre-2000 ancient history (Peters 1991, Weiner 1995, Woodward and Goodstein 1996). But I wish to focus on a current problem that I think is hindering ecological progress. I propose that ecological journals at this time are focusing their publications on papers that present apparent progress and are shedding papers that are critical of apparent progress. Or in Popper’s words, they focus on publishing ‘conjecture’ and avoid ‘refutation’. The most important aspect of this issue involves wildlife management and conservation issues. The human side of this issue may involve personal criticism and on occasion the loss of a job or promotion. The issue arises in part because of a confusion between the critique of ideas or data and the interpretation that all critiques are personal. So, the first principle of this discussion is that I discuss here only critiques of ideas or data.

There are many simple reasons for critiques of experimental design and data gathering. Are the treatments replicated, are the estimates of data variables reliable and sufficient, are proxy variables good or poor? Have the studies been carried out long enough? All these critiques can be summarized under the umbrella of measurement reliability. There are many examples we can use to illustrate these ideas. Are bird populations declining across the globe or locally? Are fisheries overharvesting particular species? Can we use climate change as a universal explanation of all changes in wildlife populations? Are survey methods for population changes across very large areas reliable? The problem is tied into the need for good or bad news that must be filtered to the news media or social media with high impact but little reliability. 

The problem at the level of science is the temptation to extrapolate beyond the limits of the available data. Now we come to the critical issue – how do our scientific journals respond to critical reviews of papers already published? My concern is that in the present time journals do not wish to receive or accept manuscripts that are critical of previously published papers. These decisions are no doubt confidential for journal publishers. There is perhaps some justification for this rejection policy, given that in the few cases where critiques are published on existing papers, the citation score of the original paper may greatly exceed that of the critique. So, conjecture pays, refutation does not.

Journals are flooded with papers and for the better journals I would expect at least a 60-80% rejection rate. For Science the rejection rate is 94%, for Nature 92%, and for the Journal of Animal Ecology 85% of submitted manuscripts are rejected. Consequently, the suggestion that they reserve space for ‘refutation’ is too negative to their publication model. There is little I can suggest if one in caught in this dilemma except to try another less premium journal, and remember that web searches find papers easily no matter where published. If you need inspiration, you can follow Peters (1991) and write a book critique and suffer the brickbats from the establishment (e.g. Nature 354: 444, 12 December 1991).

But if you are upset about a particular paper or series of papers, remember critiques are valuable but follow these rules for a critique:

  1. Keep it short, 5 typed pages should be near maximal length.
  2. Raise a set of major points. Do not try to cover everything.
  3. Summarize briefly the key points you are in agreement with, so they are not confounded in the discussion.
  4. Discuss what studies might distinguish hypothesis A vs B, or A+B vs C.
  5. Discuss what better methods of measurement might be used if funding is available.
  6. Never attack individuals or research groups. The discussion is about ideas, results, and inferences.

Decisions to accept some management actions may have to be taken immediately and journal editors must take that into consideration. Prognostication over accepting critiques may be damaging. But all actions must be continually evaluated and changed once the understanding of the problem changes.

There are too many examples to recommend reading about past and present controversies in ecology, so here are only two examples. Dowding et al. (2009) report a comment on suggested methods of controlling introduced pests on Macquarie Island in the Southern Ocean. I was involved in that discussion. A much bigger controversy in Canada involves Southern Mountain caribou populations which are in rapid decline. The proximate explanation for the decline is postulated to be predation by wolves and thus the suggested management action is shooting the wolves. Johnson et al. (2022), Lamb et al. (2022) and Superbie et al. (2022) provide an entre into this literature and the decisions of what to do now and in the future to prevent extinction of these ungulates. The caribou problem is complicated by the interaction of human alteration of landscapes and the natural processes of predation and food availability. Alas nothing is simple.

All these ecological dilemmas are controversial and the important role of criticism involving evaluations of alternative hypotheses are the only way forward for ecologists involved in controversies. In my opinion most ecological journals are not doing their part is publishing critiques of the conventional wisdom.

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

Johnson, C.J., Ray, J.C. & St-Laurent, M.-H. (2022) Efficacy and ethics of intensive predator management to save endangered caribou. Conservation Science and Practice, 4: e12729. doi: 10.1111/csp2.12729.

Lamb, C.T., Willson, R., Richter, C., Owens-Beek, N., Napoleon, J., Muir, B., McNay, R.S., Lavis, E., Hebblewhite, M., Giguere, L., Dokkie, T., Boutin, S. & Ford, A.T. (2022) Indigenous-led conservation: Pathways to recovery for the nearly extirpated Klinse-Za mountain caribou. Ecological Applications 32 (5): e2581. doi: 10.1002/eap.2581.

Peters, R.H. (1991) A Critique for Ecology. Cambridge University Press, Cambridge, England. 366 pp. ISBN:0521400171.

Popper, K.R. (1963) Conjectures and Refutations: The Growth of Scientific Knowledge. Routledge and Kegan Paul, London. 412 pp. ISBN-13: 978-0415285940.

Superbie, C., Stewart, K.M., Regan, C.E., Johnstone, J.F. & McLoughlin, P.D. (2022) Northern boreal caribou conservation should focus on anthropogenic disturbance, not disturbance-mediated apparent competition. Biological Conservation, 265, 109426. doi: 10.1016/j.biocon.2021.109426.

Weiner, J. (1995) On the practice of ecology. Journal of Ecology, 83, 153-158.

Woodward, J. & Goodstein, D. (1996) Conduct, misconduct and the structure of science. American Scientist, 84, 479-490.

The Problem of Evidence in Ecology

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The good news is that the general public are becoming more concerned about the problems of wildlife management and conservation in general. The bad news arising from this interest is the lack of understanding exhibited by many of the comments in the media about ecological problems. This leads to a suggestion that we need an ecological “fact checking” team that looks at what is said about broad scale environmental issues and points out how much evidence there is for what is stated in the media. My interest in this issue is driven by so many news stories that are stated as fact with very little scientific understanding. Too many well-meaning reports fly around the media that border on complete error or complete nonsense. One consequence of this problem is a failure of evidence-based decision making for ecological problems (Christie et al. 2022).

This is not of course a problem confined to ecological science as you can see by reading nonsense claims about medical issues like Covid. It will not go away and with the climate crisis the number of ‘experts’ has multiplied. The problem comes down to the issue of evidence and how we evaluate evidence. A partial solution to this is better education about what is evidence in ecology as well as all of science. We need to teach workshops or courses on concrete examples of what is suggested to be evidence in ecological papers. The first step might be to analyse one or a few papers with the following procedure:

  1. What is the major conclusion of the paper?
  2. What data are presented to reach this conclusion?
  3. What background assumptions are being made to move from data to conclusions?

These questions lead us back to basic questions illustrated well by statistical inference. What is the ‘population’ to which the major conclusions apply? There is very little discussion of this in most ecological papers and the consequence can be overgeneralizations. Suppose for example we are examining the hypothesis that the geographic range of a species set is moving toward the poles because of a warming climate. We must for practical purposes restrict our study to a small set of species, so this is a major assumption that the species selected are a random sample of the biota under discussion. Another limitation is that it may be difficult to isolate climate change without considering for example human disturbances to the landscape from forestry and agriculture. A consequence of these complications is that our major conclusion for all this research rests on minimal data. So, a conclusion might be that we need to design further extensive studies. But perhaps of the 6 species under study, 4 are moving as the climate hypothesis predicts, but one is not moving at all, and one is moving in the opposite direction to what is predicted. Do we now turn our attention to these anomalous species that do not follow our major hypothesis? Or should we be happy that most of our candidate species follow the rule specified in our major conclusion?

       By doing manipulative experiments ecologists attempt to insert more rigor into their conclusions, but many of the generic questions mentioned above apply equally to these experimental designs. If we do a set of experiments in Iowa and in Germany, should we get the same results? We are back to the question of generality in all our studies. We hope for global rules, but experiments are all limited in time and space.

Can we escape all these bottlenecks with models that capture the generality and behave according to our assumptions? But models suffer from the same problems that make empirical studies difficult – what are the hidden assumptions? Taper et al. (2021) discuss the problem of errors arising from model misspecification in evaluating empirical data. Perhaps every ecological publication should end with an additional short section listing the assumptions made in reaching the major conclusions of the research.

These points come to the fore when we attempt to predict future environmental changes. A simple example is the hypothesis that, by humans increasing CO2 in the atmosphere, plants will increase photosynthesis and thus negate part or all the effects of climate change on our current ecosystems. This has caused much discussion ranging from planting more trees to alleviate climate change to relying on engineering solutions to climate change.

The bottom line that we should all recognize is that our predictions in ecology and our understanding of ecosystem changes are more limited than we admit. We know that we cannot rely on the old adage of the equilibrium hypothesis that “Mother Nature will take care of the earth” so all will be well. Wisdom always relies on critical evaluations which are too often lost in the media of our current world.

An important alternative approach is illustrated by the Conservation Evidence Journal and the approaches recommended by Sutherland et al. (2022) to specify local actions that can improve the conservation status of particular species or groups of species, for example by reintroducing birds to islands or areas from which they have been extirpated. The dichotomy here is a divide between the particular and the general, from short-term local questions to long-term general questions (Saunders et al. 2020). The hope is that progress on local questions will gradually inform the dominant global theories of ecology to bring them together and support the “devil in the details’ approach that can define ecological progress in our time (Sutherland et al. 2021).

Christie, A.P., et al. (2022) Principles for the production of evidence-based guidance for conservation actions. Conservation Science and Practice, 4, e579.doi: 10.1111/csp2.12663 .

Saunders, M.E., Janes, J.K. & O’Hanlon, J.C. (2020) Moving on from the Insect Apocalypse Narrative: Engaging with Evidence-Based Insect Conservation. BioScience, 70, 80-89.doi: 10.1093/biosci/biz143.

Sutherland, W.J., Downey, H., Frick, W.F., Tinsley-Marshall, P. & McPherson, T. (2021) Planning practical evidence-based decision making in conservation within time constraints: the Strategic Evidence Assessment Framework. Journal for Nature Conservation, 60, 125975.doi: 10.1016/j.jnc.2021.125975.

Sutherland, W.J. et al. (2022) Creating testable questions in practical conservation: a process and 100 questions. Conservation Evidence Journal, 19, 1-7.doi: 10.52201/CEJ19XIFF2753.

Taper, M., Lele, S., Ponciano, J., Dennis, B. & Jerde, C. (2021) Assessing the global and local uncertainty of scientific evidence in the presence of model misspecification Frontiers in Ecology and Evolution, 9, 679155.doi: 10.3389/fevo.2021.679155.

The Problem of Time in Ecology

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There is a problem in doing ecological studies that is too little discussed – what is the time frame of a good study? The normal response would be that the time frame varies with each study so that no guidelines can be provided. There is increasing recognition that more long-term studies are needed in ecology (e.g. Hughes et al. 2017) but the guidelines remain unclear.

The first issue is usually to specify a time frame, e.g. 5 years, 10 years. But this puts the cart before the horse, as the first step ought to be to define the hypothesis being investigated. In practice hypotheses in many ecological papers are poorly presented and there should not be one hypothesis but a series of alternative hypotheses. Given that, the question of time can be given with more insight. How many replicated time periods do you need to measure the ecological variables in the study? If your time scale unit is one year, 2 or 3 years is not enough to come to any except very tentative conclusions. We have instantly fallen into a central dilemma of ecology – studies are typically planned and financed on a 3–5-year time scale, the scale of university degrees.

Now we come up against the fact of climate change and the dilemma of trying to understand a changing system when almost all field work assumes an unchanging environment. Taken to some extreme we might argue that what happens in this decade tells us little about what will happen in the next decade. The way around this problem is to design experiments to test the variables that are changing ahead of time, e.g., what a 5⁰C temperature increase will do to the survival of your corals. To follow this approach, which is the classic experimental approach of science, we must assume we know the major variables affecting our population or community changes. At present we do not know the answer to this question, and we rely on correlations of a few variables as predictors of how large a change to expect.

There is no way out of this empirical box, which defines clearly how physics and chemistry differ from ecology and medicine. There are already many large-scale illustrations of this problem. Forest companies cut down old-growth timber on the assumption that they can get the forest back by replanting seedlings in the harvested area. But what species of tree seedlings should we replant if we are concerned that reforestation often operates on a 100–500-year time scale? And in most cases, there is no consideration of the total disruption of the ecosystem, and we ignore all the non-harvestable biodiversity. Much research is now available on reforestation and the ecological problems it produces. Hole-nesting birds can be threatened if old trees with holes are removed for forestry or agricultural clearing (Saunders et al. 2023). Replanting trees after fire in British Columbia did not increase carbon storage over 55 years of recovery when compared with unplanted sites (Clason et al. 2022). Consequently, in some forest ecosystems tree planting may not be useful if carbon storage is the desired goal.

At the least we should have more long-term monitoring of the survival of replanted forest tree seedlings so that the economics of planting could be evaluated. Short-term Australian studies in replanted agricultural fields showed over 4 years differences in survival of different plant species (Jellinek et al. 2020). For an on-the-ground point of view story about tree planting in British Columbia see:
https://thetyee.ca/Opinion/2023/11/02/Dont-Thank-Me-Being-Tree-Planter/. But we need longer-term studies on control and replanted sites to be more certain of effective restoration management. Gibson et al. (2022) highlighted the fact that citizen science over a 20-year study could make a major contribution to measuring the effectiveness of replanting. Money is always in short supply in field ecology and citizen science is one way of achieving goals without too much cost. 

Forest restoration is only one example of applied ecology in which long-term studies are too infrequent. The scale of restoration of temperate and boreal ecosystems is around 100 years, and this points to one of the main failures of long-term studies, that they are difficult to carry on after the retirement of the principal investigators who designed the studies.

The Park Grass Experiment begun in 1856 on 2.8 ha of grassland in England is the oldest ecological experiment in existence (Silvertown et al. 2006). As such it is worth a careful evaluation for the questions it asked and did not ask, for the scale of the experiment, and for the experimental design. It raises the question of generality for all long-term studies and cautions us about the utility and viability of many of the large-scale, long-term studies now in progress or planned for the future.

The message of this discussion is that we should plan for long-term studies for most of our critical ecological problems with clear hypotheses of how to conserve biodiversity and manage our agricultural landscapes and forests. We should move away from 2–3-year thesis projects on isolated issues and concentrate on team efforts that address critical long-term issues with specific hypotheses. Which says in a nutshell that we must develop a vision that goes beyond our past practices in scatter-shot, short-term ecology and at the same time avoid poorly designed long-term studies of the future.

Clason, A.J., Farnell, I. & Lilles, E.B. (2022) Carbon 5–60 Years After Fire: Planting Trees Does Not Compensate for Losses in Dead Wood Stores. Frontiers in Forests and Global Change, 5, 868024. doi: 10.3389/ffgc.2022.868024.

Gibson, M., Maron, M., Taws, N., Simmonds, J.S. & Walsh, J.C. (2022) Use of citizen science datasets to test effects of grazing exclusion and replanting on Australian woodland birds. Restoration Ecology, 30, e13610. doi: 10.1111/rec.13610.

Hughes, B.B.,et al. (2017) Long-term studies contribute disproportionately to ecology and policy. BioScience, 67, 271-281. doi.: 10.1093/biosci/biw185.

Jellinek, S., Harrison, P.A., Tuck, J. & Te, T. (2020) Replanting agricultural landscapes: how well do plants survive after habitat restoration? Restoration Ecology, 28, 1454-1463. doi: 10.1111/rec.13242.

Saunders, D.A., Dawson, R. & Mawson, P.R. (2023) Artificial nesting hollows for the conservation of Carnaby’s cockatoo Calyptorhynchus latirostris: definitely not a case of erect and forget. Pacific Conservation Biology, 29, 119-129. doi: 10.1071/PC21061.

Silvertown, J., Silvertown, J., Poulton, P. & Biss, P.M. (2006) The Park Grass Experiment 1856–2006: its contribution to ecology. Journal of Ecology, 94, 801-814. doi: 10.1111/j.1365-2745.2006.01145.x.

The Ecological Outlook

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There is an extensive literature on ecological traps going back two decades (e.g. Schlaepfer et al. 2002, Kristan 2003, Battin 2004) discussing the consequences of particular species selecting a habitat for breeding that is now unsuitable. A good example is discussed in Lamb et al. (2017) for grizzly bears in southeastern British Columbia in areas of high human contact. The ecological trap hypothesis has for the most part been discussed in relation to species threatened by human developments with some examples of whole ecosystems and human disturbances (e.g. Lindenmayer and Taylor 2020). The concept of an ecological trap can be applied to the Whole Earth Ecosystem, as has been detailed in the IPCC 2022 reports and it is this global ecological trap that I wish to discuss.

The key question for ecologists concerned about global biodiversity is how much biodiversity will be left after the next century of human disturbances. The ecological outlook is grim as you can hear every day on the media. The global community of ecologists can ameliorate biodiversity loss but cannot stop it except on a very local scale. The ecological problem operates on a century time scale, just the same as the political and social change required to escape the global ecological trap. E.O. Wilson (2016) wrote passionately about our need to set aside half of the Earth for biodiversity. Alas, this was not to be. Dinerstein et al. (2019) reduced the target to 30% in the “30 by 30” initiative, subsequently endorsed by 100 countries by 2022. Although a noble political target, there is no scientific evidence that 30 by 30 will protect the world’s biodiversity. Saunders et al. (2023) determined that for North America only a small percentage of refugia (5– 14% in Mexico, 4–10% in Canada, and 2–6% in the USA) are currently protected under four possible warming scenarios ranging from +1.5⁰C to +4⁰C. And beyond +2⁰C refugia will be valuable only if they are at high latitudes and high elevations.

The problem as many people have stated is that we are marching into an ecological trap of the greatest dimension. A combination of global climate change and continually increasing human populations and impacts are the main driving factors, neither of which are under the control of the ecological community. What ecologists and conservationists can do is work on the social-political front to protect more areas and keep analysing the dynamics of declining species in local areas. We confront major political and social obstacles in conservation ecology, but we can increase our efforts to describe how organisms interact in natural ecosystems and how we can reduce undesirable declines in populations. All this requires much more monitoring of how ecosystems are changing on a local level and depends on how successful we can be as scientists to diagnose and solve the ecological components of ecosystem collapse.

As with all serious problems we advance by looking clearly into what we can do in the future based on what we have learned in the past. And we must recognize that these problems are multi-generational and will not be solved in any one person’s lifetime. So, as we continue to march into the ultimate ecological trap, we must rally to recognize the trap and use strong policies to reverse its adverse effects on biodiversity and ultimately to humans themselves. None of us can opt out of this challenge.

There is much need in this dilemma for good science, for good ecology, and for good education on what will reverse the continuing degradation of our planet Earth. Every bit counts. Every Greta Thunberg counts.

Battin, J. (2004) When good animals love bad habitats: ecological traps and the conservation of animal populations. Conservation Biology, 18, 1482-1491.

Dinerstein, E., Vynne, C., Sala, E., et al. (2019) A Global Deal For Nature: Guiding principles, milestones, and targets. Science Advances, 5, eaaw2869.doi: 10.1126/sciadv.aaw2869..

IPCC, 2022b. In: Skea, J., Shukla, P.R., et al. (Eds.), Climate Change 2022: Mitigation of Climate Change. Contribution of Working Group III to the Sixth Assessment Report of theIntergovernmental Panel on Climate Change. Cambridge University Press. doi: www.ipcc.ch/report/ar6/wg3/.

Kristan III, W.B. (2003) The role of habitat selection behavior in population dynamics: source–sink systems and ecological traps. Oikos, 103, 457-468.

Lamb, C.T., Mowat, G., McLellan, B.N., Nielsen, S.E. & Boutin, S. (2017) Forbidden fruit: human settlement and abundant fruit create an ecological trap for an apex omnivore. Journal of Animal Ecology, 86, 55-65. doi. 10.1111/1365-2656.12589.

Lindenmayer, D.B. and Taylor, C. (2020) New spatial analyses of Australian wildfires highlight the need for new fire, resource, and conservation policies. Proceedings of the National Academy of Sciences 117, 12481-124485. doi. 10.1073/pnas.2002269117.

Saunders, S.P., Grand, J., Bateman, B.L., Meek, M., Wilsey, C.B., Forstenhaeusler, N., Graham, E., Warren, R. & Price, J. (2023) Integrating climate-change refugia into 30 by 30 conservation planning in North America. Frontiers in Ecology and the Environment, 21, 77-84. doi. 10.1002/fee.2592.

Schlaepfer, M.A., Runge, M.C. & Sherman, P.W. (2002) Ecological and evolutionary traps. Trends in Ecology & Evolution, 17, 474-480.

Wilson, E.O. (2016) Half-Earth: Our Planet’s Fight for Life. Liveright, New York. ISBN: 978-1-63149-252-5.

The Time Frame of Ecological Science

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Ecological research differs from many branches of science in having a more convoluted time frame. Most of the sciences proceed along paths that are more often than not linear – results A → results B → results C and so on. Of course, these are never straight linear sequences and were described eloquently by Platt (1964) as strong inference:

“Strong inference consists of applying the following steps to every problem in science, formally and explicitly and regularly: 1) Devising alternative hypotheses; 2) Devising a crucial experiment (or several of them), with alternative possible outcomes, each of which will, as nearly as possible, exclude one or more of the hypotheses; 3) Carrying out the experiment so as to get a clean result; “Recycling the procedure, making sequential hypotheses to refine the possibilities that remain; and so on. It is like climbing a tree.” (page 347 in Platt).

If there is one paper that I would recommend all ecologists read it is this paper which is old but really is timeless and critical in our scientific research. It should be a required discussion topic for every graduate student in ecology.

Some ecological science progresses as Platt (1964) suggests and makes good progress, but much of ecology is lost in a failure to specify alternative hypotheses, in changing questions, in abandoning topics because they are too difficult, and in a shortage of time. It is the time component of ecological research that I wish to discuss in this blog.

The idea of long-term studies has always been present in ecology but was perhaps brought to our focus by the compilation by Gene Likens in 1989 in a book of 14 chapters that are as vital now as they were 34 years ago. Many discussions of long-term studies are now available to examine this issue. Buma et al. (2019) for example discuss plant primary succession at Glacier Bay, Alaska which has 100 years of data, and which illustrates in a very slow ecosystem a test of conventional rules of community development. Cusser et al. (2021) follow this by asking a critical question of how long field experiments need to be. They restrict long-term to be > 10 years of study and used data from the USA LTER sites. This question depends very much on the community or ecosystem of study. Studies in areas with a stable climate produced results more quickly than those in highly seasonal environments, and plant studies needed to be longer term than animal studies to reach stable conclusions. Ten years may not be enough.

Reinke et al. (2019) reviewed 3 long term field studies and suggest that long-term studies can be useful to allow us to predict how ecosystems will change with time. All these studies lead to three unanswered questions that are critical for progress in ecology. The first question is how we decide as a community exactly which ecological system we should be studying long-term. No one knows how to answer this question, and a useful graduate seminar could debate the utility of what are now considered model long-term studies, such as the three highlighted in Reinke et al. (2019) or the Park Grass Experiment (Addy et al. 2022). At the moment these decisions are opportunistic, and we should debate how best to proceed. Clearly, we cannot do everything for every population and community of interest, so how do we choose? We need model systems that can be applied to a wide variety of environments across the globe and that ask questions of global significance. Many groups of ecologists are trying to do this, but a host of decisions about who to fund and support in what institution are vital to avoid long-term studies driven more by convenience than by ecological importance.

A second question involves the implied disagreement whether many important questions in ecology today could be answered by short-term studies, so we reach a position where there is competition between short- and long-term funding. These decisions about where to do what for how long are largely uncontrolled. One would prefer to see an articulated set of hypotheses and predictions to proceed with decision making, whether for short-term studies suitable for graduate students or particularly for long-term studies that exceed the life of individual researchers.

A third question is the most difficult one of the objectives of long-term research. Given climate change as it is moving today, the hope that long-term studies will give us reliable predictions of changes in communities and ecosystems is at risk, the same problem of extrapolating a regression line beyond the range of the data. Depending on the answer to this climate dilemma, we could drop back to the suggestion that because we have only a poor ability to predict ecological change, we should concentrate more on widespread monitoring programs and less on highly localized studies of a few sites that are of unknown generality. Testing models with long-term data is enriching the ecological literature (e.g. Addy et al 2022). But the challenge is whether our current understanding is sufficient to make predictions for future populations or communities. Should ecology adopt the paradigm of global weather stations?

Addy, J.W.G., Ellis, R.H., MacLaren, C., Macdonald, A.J., Semenov, M.A. & Mead, A. (2022) A heteroskedastic model of Park Grass spring hay yields in response to weather suggests continuing yield decline with climate change in future decades. Journal of the Royal Society Interface, 19, 20220361. doi: 10.1098/rsif.2022.0361.

Buma, B., Bisbing, S.M., Wiles, G. & Bidlack, A.L. (2019) 100 yr of primary succession highlights stochasticity and competition driving community establishment and stability. Ecology, 100, e02885. doi: 10.1002/ecy.2885.

Cusser, S., Helms IV, J., Bahlai, C.A. & Haddad, N.M. (2021) How long do population level field experiments need to be? Utilising data from the 40-year-old LTER network. Ecology Letters, 24, 1103-1111. doi: 10.1111/ele.13710.

Hughes, B.B., Beas-Luna, R., Barner, A., et al. (2017) Long-term studies contribute disproportionately to ecology and policy. BioScience, 67, 271-281. doi: 10.1093/biosci/biw185.

Likens, G.E. (Editor, 1989) Long-term Studies in Ecology: Approaches and Alternatives. Springer Verlag, New York. 214 pp. ISBN: 0387967435.

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

Reinke, B.A., Miller, D.A.W. & Janzen, F.J. (2019) What have long-term field studies taught as about population dynamics? Annual Review of Ecology, Evolution, and Systematics, 50, 261-278. doi: 10.1146/annurev-ecolsys-110218-024717.

The Two Questions: So what? What next?

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Assuming that these two questions are not copyright, I wanted to explore them as a convenient part of writing a scientific or popular paper in ecology, conservation, and wildlife and fisheries management. To protect the innocent, I will not identify which of many ecological colleagues has stimulated this blog.

The first question should be addressed in every scientific paper but clearly is not if you read a random sample of the articles in many ecological journals. So what? is the critical question of exactly what current problem this paper or book will contribute to. It is the microscopic and macroscopic focus of why we do science, and it does not matter at all if it addresses a minor problem or a major catastrophe like species loss in conservation. In writing one should assume that time is the critical limiting factor in our lives, and while it is fine to be entertained by watching a movie, scientists do not read scientific papers to be entertained. Some journals demand that the abstract of every paper ends with a statement of the importance of the research findings, captured by So what? Too often these statements are weak and editors as well as granting agencies should demand more incisive statements. Asking yourself So what? can be a useful guide as you progress in your research and evaluate others.

While most scientists should agree on the findings presented in a paper or lecture, not all of them will agree about the importance of the answer to So what? What is a major and important scientific finding for some may be of minor significance to others, but the key is to remember here that science is a broad church that should be progressing on a broad front, so that differences of opinion are to be expected, and we rely on evidence to evaluate these differences of opinion. Tests of ideas that turn out to be incorrect or only partly correct must not be considered as failures. If you doubt that, interview any senior scientist in your area and ask about progress and regress during their scientific career. If you find a scientist who insists that they were correct in all their ideas, you should probably request them to go into politics to improve decision making in the real world.

The second question is probably the most critical for all scientific research. Once research is completed, there are two paths. If the original question or problem is solved or answered, the question becomes what does this work suggest needs to be done to advance the general area of research. Most typically however a research project will end up with more questions than it solves. The growing end of science is the critical one, and by asking What next? we delve deeper into the area of research to fill in details that were not evident when it was started. Read Sutherland et al. (2013, 2022) for an excellent example of this approach in conservation science. A simple example of this approach comes from many conservation problems. A particular species of bird may be thought to be declining in numbers, so the first issue is whether this is correct, and so an investigation into the changes in abundance of the species becomes the first step. This could lead to an analysis of the demography of the species population, birth, death and movement rates could be determined to isolate more precisely why abundance is changing. Given these data, the next step might be (for example) why the death rate is increasing if indeed this is the case. The next step is what management methods can be applied to reduce the death rate, and does this situation apply to other closely related species. It is important that asking What next? does not imply a linear sequence in time, and a study could be designed to address more than one question at the same time. We finish the What next? approach with a web of information and conclusions that address a broader question than the original simple question. And What next? should not be answered with a broad set of statements like “climate change is the cause” but by suggestions of very specific experiments and studies to carry investigations forward.

The result in ecology is an increasing precision of thought into ecological interactions and the processes that link species, communities, and ecosystems to very large questions such as the environmental response to climate change. Not all questions need to be large-scale because there are important local questions about the adequacy of designated parks and protected areas to protect species, communities, and ecosystems. The key message is that ecological understanding is not static but grows incrementally by well-designed research programs that by themselves seem to address only small-scale issues.

Seemingly failed research programs are not to be scorned but rather to indicate what avenues of research have not led to good insights. In a sense ecological science is like an evolutionary tree in which some branches fade away with time and others blossom into a variety of forms that surprise us all. So, my advice is to carry on asking these two simple questions in science to help sharpen your research program.

Sutherland, W.J., Freckleton, R.P., Godfray, H.C.J., Beissinger, S.R., Benton, T., Cameron, D.D., Carmel, Y., Coomes, D.A., Coulson, T., Emmerson, M.C., Hails, R.S., Hays, G.C., Hodgson, D.J., Hutchings, M.J., Johnson, D., Jones, J.P.G., Keeling, M.J., Kokko, H., Kunin, W.E. & Lambin, X. (2013) Identification of 100 fundamental ecological questions. Journal of Ecology, 101, 58-67.doi: 10.1111/1365-2745.12025.

Sutherland, W.J. & Jake M. Robinson, D.C.A., Tim Alamenciak, Matthew Armes, Nina Baranduin, Andrew J. Bladon, Martin F. Breed, Nicki Dyas, Chris S. Elphick, Richard A. Griffiths, Jonny Hughes, Beccy Middleton, Nick A. Littlewood, Roger Mitchell, William H. Morgan, Roy Mosley, Silviu O. Petrovan, Kit Prendergast, Euan G. Ritchie,Hugh Raven, Rebecca K. Smith, Sarah H. Watts, Ann Thornton (2022) Creating testable questions in practical conservation: a process and 100 questions. Conservation Evidence Journal, 19, 1-7.doi: 10.52201/CEJ19XIFF2753.