Tag Archives: hypothesis testing

Do We Need to Replicate Ecological Experiments?

If you read papers on the philosophy of science you will very quickly come across the concept of replication, the requirement to test the same hypothesis twice or more before you become too attached to your conclusions. As a new student or a research scientist you face this problem when you wish to replicate some previous study. If you do replicate, you risk being classed as an inferior scientist with no ideas of your own. If you refuse to replicate and try something new, you will be criticized as reckless and not building a solid foundation in your science.  

There is an excellent literature discussing the problem of replication in ecology in particular and science in general. Nichols et al. (2019) argue persuasively that a single experiment is not enough. Amrheim et al. (2019) approach the problem from a statistical point of view and caution that single statistical tests are a shaky platform for drawing solid conclusions. They point out that statistical tests not only test hypotheses, but also countless assumptions and particularly for ecological studies the exact plant and animal community in which the study takes place. In contrast to ecological science, medicine probably has more replication problems at the other extreme – too many replications – leading to a waste of research money and talent. (Siontis and Ioannidis 2018).

A graduate seminar could profitably focus on a list of the most critical experiments or generalizations of our time in any subdiscipline of ecology. Given such a list we could ask if the conclusions still stand as time has passed, or perhaps if climate change has upset the older predictions, or whether the observations or experiments have been replicated to test the strength of conclusions. We can develop a stronger science of ecology only if we recognize both the strengths and the limitations of our current ideas.

Baker (2016) approached this issue by asking the simple question “Is there a reproducibility crisis?” Her results are well worth visiting. She had to cast a wide net in the sciences so unfortunately there are no details specific to ecological science in this paper. A similar question in ecology would have to distinguish observational studies and experimental manipulations to narrow down a current view of this issue. An interesting example is explored in Parker (2013) who analyzed a particular hypothesis in evolutionary biology about plumage colour in a single bird species, and the array of problems of an extensive literature on sexual selection in this field is astonishing.

A critic might argue that ecology is largely a descriptive science that should not expect to develop observational or experimental conclusions that will extend very much beyond the present. If that is the case, one might argue that replication over time is important for deciding when an established principle is no longer valid. Ecological predictions based on current knowledge may have much less reliability than we would hope, but the only way to find out is to replicate. Scientific progress depends on identifying goals and determining how far we have progressed to achieving these goals (Currie 2019). To advance we need to discuss replication in ecology.

Amrhein, V., Trafinnow, D. & Greenland, S. (2019) Inferential statistics as descriptive statistics: There is no replication crisis if we don’t expect replication. American Statistician, 73, 262-270. doi: 10.1080/00031305.2018.1543137.

Baker, M. (2016) Is there a reproducibility crisis in science? Nature, 533, 452-454.

Currie, D.J. (2019) Where Newton might have taken ecology. Global Ecology and Biogeography, 28, 18-27. doi: 10.1111/geb.12842.

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

Parker, T.H. (2013) What do we really know about the signalling role of plumage colour in blue tits? A case study of impediments to progress in evolutionary biology. Biological Reviews, 88, 511-536. doi: 10.1111/brv.12013.

Siontis, K.C. & 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.

On Ecology and Medicine

As I grow older and interact more with doctors, it occurred to me that the two sciences of medicine and ecology have very much in common. That is probably not a very new idea, but it may be worth spending time on looking at the similarities and differences of these two areas of science that impinge on our lives. The key question for both is how do we sort out problems? Ecologists worry about population, community and ecosystem problems that have two distinguishing features. First, the problems are complex and the major finding of this generation of ecologists is to begin to understand and appreciate how complex they are. Second, the major problems that need solving to improve conservation and wildlife management are difficult to study with the classical tools of experimental, manipulative scientific methods. We do what we can to achieve scientific paradigms but there are many loose ends we can only wave our hands about. As an example, take any community or ecosystem under threat of global warming. If we heat up the oceans, many corals will die along with the many animals that depend on them. But not all corals will die, nor will all the fish and invertebrate species, and the ecologists is asked to predict what will happen to this ecosystem under global warming. We may well understand from rigorous laboratory research about temperature tolerances of corals, but to apply this to the real world of corals in oceans undergoing many chemical and physical changes we can only make some approximate guesses. We can argue adaptation, but we do not know the limits or the many possible directions of what we predict will happen.

Now consider the poor physician who must deal with only one species, Homo sapiens, and the many interacting organs in the body, the large number of possible diseases that can affect our well-being, the stresses and strains that we ourselves cause, and the physician must make a judgement of what to do to solve your particular problem. If you have a broken arm, it is simple thankfully. If you have severe headaches or dizziness, many different causes come into play. There is no need to go into details that we all appreciate, but the key point is that physicians must solve problems of health with judgements but typically with no ability to do the kinds of experimental work we can do with mice or rabbits in the laboratory. And the result is that the physician’s judgements may be wrong in some cases, leading possibly to lawyers arguing for damages, and one appreciates that once we leave the world of medical science and enter the world of lawyers, all hope for solutions is near impossible.

There is now some hope that artificial intelligence will solve many of these problems both in ecological science and in medicine, but this belief is based on the premise that we know everything, and the only problem is to find the solutions in some forgotten textbook or scientific paper that has escaped our memory as humans. To ask that artificial intelligence will solve these basic problems is problematic because AI depends on past knowledge and science solves problems by future research.

Everyone is in favour of personal good health, but alas not everyone favours good environmental science because money is involved. We live in a world where major problems with climate change have had solutions presented for more than 50 years, but little more than words are presented as the solutions rather than action. This highlights one of the main differences between medicine and ecology. Medical issues are immediate since we have active lives and a limited time span of life. Ecological issues are long-term and rarely present an immediate short-term solution. Setting aside protected areas is in the best cases a long-term solution to conservation issues, but money for field research is never long term and ecologists do not live forever. Success stories for endangered species often require 10-20 years or more before success can be achieved; research grants are typically presented as 3- or 5-year proposals. The time scale we face as ecologists is like that of climate scientists. In a world of immediate daily concerns in medicine as in ecology, long-term problems are easily lost to view.

There has been an explosion of papers in the last few years on artificial intelligence as a potentially key process to use for answering both ecological and medical questions (e.g. Buchelt et al. 2024, Christin, Hervet, and Lecomte, 2019, Desjardins-Proulx, Poisot, & Gravel, 2019). It remains to be seen exactly how AI will help us to answer complex questions in ecology and medicine. AI is very good in looking back, but will it be useful to solve our current and future problems? Perhaps we still need to continue training good experimental scientists in ecology and in medicine.  

Buchelt, A., Buchelt, A., Adrowitzer, A. & Holzinger, A. (2024) Exploring artificial intelligence for applications of drones in forest ecology and management. Forest Ecology and Management, 551, 121530. doi: 10.1016/j.foreco.2023.121530.

Christin, S., Hervet, É. & Lecomte, N. (2019) Applications for deep learning in ecology. Methods in Ecology and Evolution, 10, 1632-1644. doi: 10.1111/2041-210X.13256.

Desjardins-Proulx, P., Poisot, T. & Gravel, D. (2019) Artificial Intelligence for ecological and evolutionary synthesis. Frontiers in Ecology and Evolution, 7. doi: 10.3389/fevo.2019.00402.

On Critical Evaluation in Ecology

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.

Back to Nature vs. Nurture

The ancient argument of ‘nature’ versus ‘nurture’ continues to arise in biology. The question has arisen very forcefully in a new book by James Tabery (Tabery 2023). The broad question he examines in this book is the conflict between ‘nature’ and ‘nurture’ in western medicine. In a broad sense ‘nature’ is discussed as the modern push in medicine to find the genetic basis of some of the common human degenerative diseases – Parkinson’s, dementia, asthma, diabetes, cancer, hypertension – to mention only a few medical problems of our day. The ‘nature’ approach to medicine in this book is represented by molecular genetics and the Human Genome Project. The ‘nurture’ approach to treating these medical conditions is via studying health outcomes in people subject to environmental contamination, atmospheric pollution, water quality, chemicals in food preparations, asbestos in buildings, and other environmental issues including how children are raised and educated. The competition over these two approaches was won very early by the Human Genome Project, and many of the resources for medicine over the last 30 years were put into molecular biology which made spectacular progress in diving into the genome of affected people and then making great promises of personalized medicine. The environmental approach to these medical conditions received much less money and was not viewed as sufficiently scientific. The irony of all this in retrospect is that the ‘nature’ or DNA school had no hypotheses about the problems being investigated but relied on the assumption that if we got enough molecular genetic data on thousands of people that something would jump out at us, and we would locate for example the gene(s) causing Parkinson’s, and then we could alter these genes with gene therapy or specific pharmaceuticals. By contrast the ‘nurture’ school had many specific hypotheses to test about air pollution and children’s health, about lead in municipal water supply and brain damage, and a host of very specific insights about how some of these health problems could be alleviated by legislation and changes in diet for example.

So, the question then becomes where are we today? The answer Tabery (2023) gives is that the ‘nature’ or molecular genetic “personalized medicine” approach has largely failed in achieving its goals despite the large amount of money invested because there is no single or small set of genes that cause specific diseases, but many genes that have complex interactions. In contrast, the ‘nurture’ school has made progress in identifying conditions that help decrease the occurrence of some of our common diseases, realizing that the problems are often difficult because they require changes in human behaviour like stopping smoking or improving diets.

All this discussion would possibly produce the simple conclusion that both “nature” and “nurture” are both involved in these complex human conditions. So, what could this medical discussion tell us about the condition of modern ecological science? I think two things perhaps. First, it is a general error to use science without hypotheses. Yet this is too often what ecologists do – gather a large amount of data that can be measured without too much prolonged effort and then try to make sense of it by applying hypotheses after the fact. And second, technology in ecology can be a benefit or a curse. Take, for example, the advances in vertebrate ecology that have come from the ability to describe the movements of individual animals in space. To have a map of hundreds of locations of an individual animal provides good natural history but does not address any specific hypothesis. Contrast this approach with that of Studd et al. (2021) and Shiratsuru et al. (2023) who use movement data to test important questions about kill rates of predators on different species of prey.

Many large-scale ecological approaches suffer from the same problem as the ‘nature’ paradigm – use ‘big science’ to measure many variables and then try to answer some important question for example about how climate change is affecting communities of plants and animals. Nagy et al. (2021) and Li et al. (2022) provide excellent examples of this approach. Schimel and Keller (2015) discuss what is needed to bring hypothesis testing to ‘big science’. Lindenmayer et al. (2018) discuss how conventional, question-driven long-term monitoring and hypothesis testing need to be combined with ‘big science’ to better ecological understanding. Pau et al. (2022) give a warning of how ‘big science’ data from airborne imaging can fail to agree with ground-based field studies in one core NEON grassland site in central USA.

The conclusion to date is that there is little integration in ecology of the equivalent of “nature” and “nurture” in medicine if in ecology we match ‘big science’ with ‘nature’ and field studies on the ground with ‘nurture’. Without that integration we risk in future another negative review in ecology like that provided now by Tabery (2023) for medical approaches to human diseases.

Lindenmayer, D.B., Likens, G.E. & 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.

Li, D., et al. (2022) Standardized NEON organismal data for biodiversity research. Ecosphere, 13, e4141.doi:10.1002/ecs2.4141.

Nagy, R.C., et al. (2021) Harnessing the NEON data revolution to advance open environmental science with a diverse and data-capable community. Ecosphere, 12, e03833.doi: 10.1002/ecs2.3833.

Pau, S., et al. (2022) Poor relationships between NEON Airborne Observation Platform data and field-based vegetation traits at a mesic grassland. Ecology, 103, e03590.doi: 10.1002/ecy.3590.

Schimel, D. & Keller, M. (2015) Big questions, big science: Meeting the challenges of global ecology. Oecologia, 177, 925-934.doi: 10.1007/s00442-015-3236-3.

Shiratsuru, S., Studd, E.K., Majchrzak, Y.N., Peers, M.J.L., Menzies, A.K., Derbyshire, R., Jung, T.S., Krebs, C.J., Murray, D.L., Boonstra, R. & Boutin, S. (2023) When death comes: Prey activity is not always predictive of diel mortality patterns and the risk of predation. Proceedings of the Royal Society B, 290, 20230661.doi.

Studd, E.K., Derbyshire, R.E., Menzies, A.K., Simms, J.F., Humphries, M.M., Murray, D.L. & Boutin, S. (2021) The Purr-fect Catch: Using accelerometers and audio recorders to document kill rates and hunting behaviour of a small prey specialist. Methods in Ecology and Evolution, 12, 1277-1287.doi. 10.1111/2041-210X.13605

Tabery, J. (2023) Tyranny of the Gene: Personalized Medicine and the Threat to Public Health. Knopf Doubleday Publishing Group, New York. 336 pp. ISBN: 9780525658207.

The Meaningless of Random Sampling

Statisticians tell us that random sampling is necessary for making general inferences from the particular to the general. If field ecologists accept this dictum, we can only conclude that it is very difficult to nearly impossible to reach generality. We can reach conclusions about specific local areas, and that is valuable, but much of our current ecological wisdom on populations and communities relies on the faulty model of non-random sampling. We rarely try to define the statistical ‘population’ which we are studying and attempting to make inferences about with our data. Some examples might be useful to illustrate this problem.

Marine ecologists ae mostly agreed that sea surface temperature rise is destroying coral reef ecosystems. This is certainly true, but it camouflages the fact that very few square kilometres of coral reefs like the Great Barrier Reef have been comprehensively studied with a proper sampling design (e.g. Green 1979, Lewis 2004). When we analyse the details of coral reef declines, we find that many species are affected by rising sea temperatures, but some are not, and it is possible that some species will adapt by natural selection to the higher temperatures. So we quite rightly raise the alarm about the future of coral reefs. But in doing so we neglect in many cases to specify the statistical ‘population’ to which our conclusions apply.

Most people would agree that such an approach to generalizing ecological findings is tantamount to saying the problem is “how many angels can dance on the head of a pin”, and in practice we can ignore the problem and generalize from the studied reefs to all reefs. And scientists would point out that physics and chemistry seek generality and ignore this problem because one can do chemistry in Zurich or in Toronto and use the same laws that do not change with time or place. But the ecosystems of today are not going to be the ecosystems of tomorrow, so generality in time cannot be guaranteed, as paleoecologists have long ago pointed out.

It is the spatial problem of field studies that collides most strongly with the statistical rule to random sample. Consider a hypothetical example of a large national park that has recently been burned by this year’s fires in the Northern Hemisphere. If we wish to measure the recovery process of the vegetation, we need to set out plots to resample. We have two choices: (1) lay out as many plots as possible, and sample these for several years to plot recovery. Or (2) lay out plots at random each year, never repeating the same exact areas to satisfy the specifications of statisticians to “random sample” the recovery in the park. We typically would do (1) for two reasons. Setting up new plots each year as per (2) would greatly increase the initial field work of defining the random plots and would probably mean that travel time between the plots would be greatly increased. Using approach (1) we would probably set out plots with relatively easy access from roads or trails to minimize costs of sampling. We ignore the advice of statisticians because of our real-world constraints of time and money. And we hope to answer the initial questions about recovery with this simpler design.

I could find few papers in the ecological literature that discuss this general problem of inference from the particular to the general (Ives 2018, Hauss 2018) and only one that deals with a real-world situation (Ducatez 2019). I would be glad to be sent more references on this problem by readers.

The bottom line is that if your supervisor or research coordinator criticizes your field work because your study areas are not randomly placed or your replicate sites were not chosen at random, tell him or her politely that virtually no ecological research in the field is done by truly random sampling. Does this make our research less useful for achieving ecological understanding – probably not. And we might note that medical science works in exactly the same way field ecologists work, do what you can with the money and time you have. The law that scientific knowledge requires random sampling is often a pseudo-problem in my opinion.  

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

Green, R.H. (1979) Sampling Design and Statistical Methods for Environmental Biologists. Wiley, New York. 257 pp.

Hauss, K. (2018) Statistical Inference from Non-Random Samples. Problems in Application and Possible Solutions in Evaluation Research. Zeitschrift fur Evaluation, 17, 219-240. doi.

Ives, A.R. (2018) Informative Irreproducibility and the Use of Experiments in Ecology. BioScience, 68, 746-747. doi. 10.1093/biosci/biy090

Lewis, J. (2004) Has random sampling been neglected in coral reef faunal surveys? Coral Reefs, 23, 192-194. doi: 10.1007/s00338-004-0377-y.

The Time Frame of Ecological Science

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?

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.

The Two Ecologies

Trying to keep up with the ecological literature is a daunting task, and my aging efforts shout to me that there are now two ecologies that it might be worth partially separating. First, many published “ecological” papers are natural history. This is certainly an important component of the environmental literature but for the most part good observations alone are not science in the formal sense of science addressing problems and trying to solve them with the experimental approach. The information provided in the natural history literature regarding both plants and animals include their identification, where they live, what nutrients or food resources they utilize and in some cases information on their conservation status. A good foundation of natural history is needed to do good ecological research to be sure so my statements must not be misinterpreted to suggest that I do not appreciate natural history. Good natural history leads into the two parts of ecology that I would like to discuss. I call these social ecology and scientific ecology.

Social ecology flows most easily out of natural history and deals with the interaction between humans and the biota. Thus, for example, many people love birds which are ever present in both cities and countryside, are often highly colourful and vocal in our environment. Similarly, many tourists from North America visit Australia, Africa and Central America to see birds that are unique to those regions. Similar adventures are available to see elephants, bison, bears, and whales in their natural habitats. Social ecology flows into conservation biology in cases where preferred species are threatened by human changes to the landscape. The key here is that there is a mix in social ecology between human entertainment and a concern for species losses that are driven by human actions. Social ecology is mostly about people and their views of what parts of the environment are important to them. People love elephants but are little concerned about earthworms unless they bother them.

Scientific ecology should operate with a broader perspective of testing hypotheses to understand how populations and communities of animals and plants interact to produce the world as we see it. It asks about how species interactions change over time and whether they lead to environmental stability or instability. Scientific ecology has a time dimension that is much longer than that of social ecology. The focus of scientific ecology is hypothesis testing to answer problems or questions about how the biological world works. This perspective interacts strongly with climate change and human disturbances as well as natural disturbances like flooding or forest fires. While social ecology asks what is happening, scientific ecology asks why this is happening in our ecosystems. Scientific ecology allows us to determine the causal factors behind problems of change and the management approaches that might be required. While social ecology observes that migratory birds appear to be declining in abundance, scientific ecology asks exactly which bird species are at risk and what factors like food supplies, predation, or disease are the cause of the decline. And most importantly can humans change the environment to prevent species losses?

Conservation ecology has become the link between social and scientific ecology and shares elements of both approaches. Too much of social conservation biology consists of moaning and groaning about changes with little data and unverifiable speculations. As such it provides little help to solve conservation problems. When there is clear public support for issues like old growth logging, politicians often do not act ethically to follow public support because of economics or inertia. Scientific ecology has been strongly influenced by Karl Popper’s (1963) book, with much discussion today among philosophers about Popper’s approach to hypotheses within the context of our social values and objectives (Dias 2019). Lundblad and Conway (2021) provide a classic example of hypothesis testing for clutch size in birds which illustrates well the path of scientific ecology over many years from initial conjectures to more refined understanding of the original scientific question.

In a sense this ecological dichotomy is found in many of the sciences. Medicine is a good example. We can observe and describe symptoms of people dying of lung cancer, but medical scientists really wish to know what environmental causes like air pollution or cigarette smoking are producing this mortality, and whether genetic backgrounds are involved. Science is far from perfect and there are many false leads in proposals of drugs in medicine that turn out to be counterproductive to solving a particular problem. Kim and Kendeou (2021) discuss the critical question of knowledge transfer as science progresses in our society today through knowledge transfer from generation to generation.

My concern is that social ecology is replacing scientific ecology in the ecological literature so that as we are so enamoured with the beauty of nature, we forget the need to find out quantitatively what is happening and how it might be mitigated. As with medicine, talking about problems does not solve them without serious empirical scientific study.

Dias, E.A. (2019) Science as a game in Popper. Griot : Revista de Filosofia,, 19, 327-337.doi: 10.31977/grirfi.v19i3.1239. (in Portuguese; use Google Translate)

Kim, J. & Kendeou, P. (2021) Knowledge transfer in the context of refutation texts. Contemporary Educational Psychology, 67, 102002.doi: 10.1016/j.cedpsych.2021.102002.

Lundblad, C.G. & Conway, C.J. (2021) Ashmole’s hypothesis and the latitudinal gradient in clutch size. Biological Reviews, 96, 1349-1366.doi: 10.1111/brv.12705.

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

Belief vs. Evidence

There is an interesting game you could enter into if you classified the statements you hear or read in the media or in ecological papers. The initial dichotomy is whether or not a statement is a BELIEF or EVIDENCE BASED. There is a continuum between these polar opposites so there can easily be disagreements based on a person’s background. If I say “I believe that the earth is round” you will recognize that this is not a simple belief but a physical fact that is evidence-based. Consequently we use the word ‘belief’ in many different ways. If I say that “Aliens from outer space are firing ray guns to cause flooding in California and Australia”, it is unlikely that you will be convinced because there is no evidence of how this process could work.

If we listen to the media or read the news, you will hear many statements that I or we ‘believe’ that speed limits on streets should be reduced, or that certain types of firearms should be prohibited. The natural response of a scientist to such statements is to ask for what evidence is available that such actions will solve problems, and if there is no evidence, we deal only with opinions or beliefs. If  you lived several hundred years ago, you would be told that “malaria” was a disease caused by “bad air” coming from swamps and rivers, since there was no evidence at the time about microorganisms causing disease. So in a broad sense historical progress was made by people looking for ‘evidence’ to temper and test ‘beliefs’.

How does all this relate to ecological science? I would add the requirement to papers that state some conclusions in ecology journals to also state the beliefs the paper rely on to reach its conclusions, in addition to stating clear hypotheses and alternative hypotheses. Consider the simple case of random sampling, a basic requirement in all statistical methods. But almost no paper states what statistical population is being sampled, and if it does often the study plots are not placed randomly. The standard excuse to this is that our results apply to a large biome, and it is not physically possible to sample randomly, or that we get the same results whether we sample randomly or not. Whatever the excuse, we need to recognize this as a belief or an assumption, a less damning scientific term. And if this assumption is not accepted it is possible to sample other areas or with other methods to test if the evidence validates the assumption. Evidence can always be improved with enough funding, and this replication is exactly what many scientists are doing daily.

Until recently most scientists believed that CO2 was good for plants, and so the more CO2 the better. But the evidence provided was based on simple theory and short term lab experiments. Reich et al. (2018) and Zhu et al. (2018) pointed out that this was not correct when long-term studies were done on C3 plants like rice. So this is a good illustration of the progress of science from belief to evidence. And over the past 50 years it has become very clear that increased CO2 increases atmospheric temperature with drastic climatic and biodiversity consequences (Ripple et al. 2021). The result of these scientific advances is that now there is an extensive amount of scientific research giving the empirical evidence of climate change and CO2 effects on plants and animals. Most people agree with these broad conclusions, but there are people in large corporations and governments around the world who deny these scientific conclusions because they believe that climate change is not happening and is of little consequence to biodiversity or to daily life.

It is quite possible to ignore all the scientific literature about the consequences of climate change, CO2 increase, and biodiversity loss but the end result of passing over these problems now will fall heavily onto your children and grandchildren. The biosphere is screaming the message that ignorance will not necessarily lead to bliss.

Reich, P.B., Hobbie, S.E., Lee, T.D. & Pastore, M.A. (2018) Unexpected reversal of C3 versus C4 grass response to elevated CO2 during a 20-year field experiment. Science, 360, 317-320.doi: 10.1126/science.aas9313.

Ripple, W.J., Wolf, C., Newsome, T.M., Gregg, J.W., Lenton, T.M., Palomo, I., Eikelboom, J.A.J., Law, B.E., Huq, S., Duffy, P.B. & Rockström, J. (2021) World Scientists’ Warning of a Climate Emergency 2021. BioScience, 71, 894-898.doi: 10.1093/biosci/biab079.

Shivanna, K.R. (2022) Climate change and its impact on biodiversity and human welfare. Proceedings of the Indian National Science Academy, 88, 160-171.doi: 10.1007/s43538-022-00073-6.

Watson, R., Kundzewicz, Z.W. & Borrell-Damián, L. (2022) Covid-19, and the climate change and biodiversity emergencies. Science of The Total Environment, 844, 157188.doi: 10.1016/j.scitotenv.2022.157188.

Williams, S.E., Williams, S.E. & de la Fuente, A. (2021) Long-term changes in populations of rainforest birds in the Australia Wet Tropics bioregion: A climate-driven biodiversity emergency. PLoS ONE, 16.doi: 10.1371/journal.pone.0254307.

Zhu, C., Kobayashi, K., Loladze, I., Zhu, J. & Jiang, Q. (2018) Carbon dioxide (CO2) levels this century will alter the protein, micronutrients, and vitamin content of rice grains with potential health consequences for the poorest rice-dependent countries. Science Advances, 4, eaaq1012 doi: 10.1126/sciadv.aaq1012.

Have we moved on from Hypotheses into the New Age of Ecology?

For the last 60 years a group of Stone Age scientists like myself have preached to ecology students that one needs hypotheses to do proper science. Now it has always been clear that not all ecologists followed this precept, and a recent review hammers this point home (Betts et al. 2021). I have always asked my students to read the papers from the Stone Age about scientific progress – Popper (1959), Platt (1964), Peters (1991) and even back to the Pre-Stone Age, Chamberlin (1897). There has been much said about this issue, and the recent Betts et al. (2021) paper pulls much of it together by reviewing papers from 1991 to 2015. Their conclusion is dismal if you think ecological science should make progress in gathering evidence. No change from 1990 to 2015. Multiple alternative hypotheses = 6% of papers, Mechanistic hypotheses = 25% of papers, Descriptive hypotheses = 12%, No hypotheses = 75% of papers. Why should this be after years of recommending the gold standard of multiple alternative hypotheses? Can we call ecology a science with these kinds of scores? 

The simplest reason is that in the era of Big Data we do not need any hypotheses to understand populations, communities, and ecosystems. We have computers, that is enough. I think this is a rather silly view, but one would have to interview believers to find out what they view as progress from big data in the absence of hypotheses. The second excuse might be that we cannot be bothered with hypotheses until we have a complete description of life on earth, food webs, interaction webs, diets, competitors, etc. Once we achieve that we will be able to put together mechanistic hypotheses rapidly. An alternative statement of this view is that we need very much natural history to make any progress in ecology, and this is the era of descriptive natural history and that is why 75% of papers do not list the word hypothesis.

But this is all nonsense of course, and try this view on a medical scientist, a physicist, an aeronautical engineer, or a farmer. The fundamental principle of science is cause-and-effect or the simple view that we would like to see how things work and why often they do not work. Have your students read Romesburg (1981) for an easy introduction and then the much more analytical book by Pearl and Mackenzie (2018) to gain an understanding of the complexity of the simple view that there is a cause and it produces an effect. Hone et al. (2023) discuss these specific problems with respect to improving our approach to wildlife management

What can be done about the dismal situation described by Betts et al. (2021)? One useful recommendation for editors and reviewers would be to request for every submitted paper for a clear statement of the hypothesis they are testing, and hopefully for alternative hypotheses. There should be ecology journals specifically for natural history where the opposite gateway is set: no use of ‘hypothesis’ in this journal. This would not solve all the Betts et al. problems because some ecology papers are based on the experimental design of ‘do something’ and then later ‘try to invent some way to support a hypotheses’, after the fact science. One problem with this type of literature survey is, as Betts et al. recognized, is that papers could be testing hypotheses without using this exact word. So words like ‘proposition’, ‘thesis’, ‘conjectures’ could camouflage thinking about alternative explanations without the actual word ‘hypothesis’.

One other suggestion to deal with this situation might be for journal editors to disallow all papers with hypotheses that are completely untestable. This type of rejection could be instructive to authors to assist rewriting your paper to be more specific about alternative hypotheses. If you can make a clear causal set of predictions that a particular species will go extinct in 100 years, this could be described as a ‘possible future scenario’ that could be guided by some mechanisms that are specified. Or if you have a hypothesis that ‘climate change will affect species geographical ranges, you are providing  a very vague inference that is difficult to test without being more specific about mechanisms, particularly if the species involved is rare.

There is a general problem with null hypotheses which state there is “no effect”. In some few cases these null hypotheses are useful but for the most part they are very weak and should indicate that you have not thought enough about alternative hypotheses.

So read Platt (1964) or at least the first page of it, the first chapter of Popper (1959), and Betts et al. (2021) paper and in your research try to avoid the dilemmas they discuss, and thus help to move our science forward lest it become a repository of ‘stamp collecting’.

Betts, M.G., Hadley, A.S., Frey, D.W., Frey, S.J.K., Gannon, D., Harris, S.H., et al. (2021) When are hypotheses useful in ecology and evolution? Ecology and Evolution, 11, 5762-5776. doi: 10.1002/ece3.7365.

Chamberlin, T.C. (1897) The method of multiple working hypotheses. Journal of Geology, 5, 837-848 (reprinted in Science 148: 754-759 in 1965). doi. 10.1126/science.148.3671.754.

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.

Pearl, J., and Mackenzie, D. 2018. The Book of Why. The New Science of Cause and Effect. Penguin, London, U.K. 432 pp. ISBN: 978-1541698963.

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

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

Popper, K.R. (1959) The Logic of Scientific Discovery. Hutchinson & Co., London. ISBN: 978-041-5278-447.

Romesburg, H.C. (1981) Wildlife science: gaining reliable knowledge. Journal of Wildlife Management, 45, 293-313. doi:10.2307/3807913.