Author Archives: Charles Krebs

On Random Sampling and Generalization in Ecology

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Thoughts on Wildlife Management

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Stop for a moment and think about where we are now in the science of wildlife management and conservation. Look at the titles of paper in our scientific journals. The vast majority of the problems and questions being investigated are basically about how to reverse some human-caused folly. Many wildlife scientists, ecologists, and organismal biologists entered science with the goal of understanding natural systems from the ecosystem down to the molecular level but in the past 60 years the focus has had to shift. This shift has occurred almost unnoticed because it has been gradual in the time scale of human employment and turnover. The ecosystems of the world are in a frightful mess, and virtually all the mess is human caused. So while we engage in many discussions about how to define the ‘Anthropocene’ in the geological sciences (Correia et al. 2018; Zalasiewicz et al. 2017) ecological science is left in the dust because it never leads to ‘progress’.

This came home to me when I considered which of the many study sites in which classical ecological research has been carried out over the last century still exist. They have been replaced by suburbs, highways, shopping malls, farms, and industrial sites, and the associated waterways have been altered beyond recognition. A simple consequence is that if you wished to repeat a famous ecological study done 50-100 years ago, you could not do it because the site has been obliterated. One consequence is that if we wish to do field work today, we choose a new site that has so far been protected from development.

The elephant in the room now is climate change, so if you choose to investigate the trophic dynamics of an Amazonian forest area (for example), you face two problems – the site could be obliterated by ‘development’ before your work is completed, or the climate changes expected during the next 80 years will alter the trophic dynamics of your site so that your current results are no guide to the future state of these ecosystems. Whither predictive ecology? Many of us thought that by discovering and analyzing ecological principles, we could closely approach the precision of the physical sciences, the laws of physics and chemistry. But the more we search for generality in ecology the less we find. We retreat to general principles that are too vague to be of any predictive use for the wildlife managers of the future.

The thought has been prevalent that by investigating the changes in communities and ecosystems in the past we would have a guide to the future. This belief guides much of paleo-ecological research as well as the projections from evolutionary research of how species have recovered from the recent ice ages. But the past is perhaps not necessarily a good guide to the future when we add in the human footprint arising from the combination of population growth and climate change. Ecologists are left with the concern that our findings have much current value but perhaps little long-term insight. 

Many current papers on ecological changes assume a simple extrapolation predicting the future state of ecosystems (e.g. Martin et al. 2019; Yu et al. 2019). Testing these kinds of extrapolations is virtually possible within the lifetime of the typical ecologist, and my concern is that management actions that are recommended now may be completely off the mark in 30 years. Several papers have warned about this (e.g. Inkpen 2017; La Marca et al. 2019; Mouquet et al. 2015) but as far as I can determine to little effect.

I think the bottom line might be a recommendation for all predictive papers to state a strong prediction and a defined time frame so that there is hope of testing the predictive model in ecological time. Otherwise we ecologists begin to fall into the realm of science fiction.

Correia, R.A. et al. (2018). Pivotal 20th century contributions to the development of the Anthropocene concept: overview and implications. Current Science 115, 1871-1875. doi: 10.18520/cs/v115/i10/1871-1875.

Inkpen, S.A. (2017). Are humans disturbing conditions in ecology? Biology & Philosophy 32, 51-71. doi: 10.1007/s10539-016-9537-z.

La Marca, W. et al. (2019). The influence of data source and species distribution modelling method on spatial conservation priorities. Diversity & Distributions 25, 1060-1073. doi: 10.1111/ddi.12924.

Martin, D. et al. (2019). Long-distance influence of the Rhône River plume on the marine benthic ecosystem: Integrating descriptive ecology and predictive modelling. Science of The Total Environment 673, 790-809. doi: 10.1016/j.scitotenv.2019.04.010.

Mouquet, N. et al. (2015). Predictive ecology in a changing world. Journal of Applied Ecology 52, 1293-1310. doi: 10.1111/1365-2664.12482.

Yu, F., et al. (2019). Climate and land use changes will degrade the distribution of Rhododendrons in China. Science of The Total Environment 659, 515-528. doi: 10.1016/j.scitotenv.2018.12.223.

Zalasiewicz, J. et al. (2017). The Working Group on the Anthropocene: Summary of evidence and interim recommendations. Anthropocene 19, 55-60. doi: 10.1016/j.ancene.2017.09.001.

How Big an Area is Big Enough for Conservation?

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The larger the species, the more likely it is to be a species of conservation concern. Like many principles of conservation biology, this statement is a generalization with many exceptions. Often it has to be coupled with a statement of the geographic range size of the species of concern and the disturbances wrought by humans within this geographic range. And on top of these ecological issues, there are genetic concerns about population viability. The net result of all these issues is that conservation tends to focus on single species and to minimize the need to understand community and ecosystem dynamics. There is a limit on what we can achieve with limited funding and person-power. The public consensus at this time seems to be that we are losing the battle, that biodiversity is being lost on a global scale, even though we are winning the battle for some charismatic species (e.g. waterfowl, Anderson et al. 2018).

The scale issue is what has continued to defeat us. Take any group of species from your local area and try to determine what size of national park or protected area would be required for that group to survive for your great-grandchildren. No one knows the answer to this simple question, except for the negative finding that at present no protected area is large enough to prevent serious biodiversity loss of a 50-year time scale, no matter what its size.

One escape from this loss of biodiversity has been to call for establishing larger protected areas for conservation, and it leads directly into the critical question of how big a protected area is needed. This question can be analyzed at the level of the single species or an entire ecosystem, but the result is always the same – however big the protected area, it is not big enough. The only answer ecologists have to this challenge is to set up protected areas as large as is politically possible and then monitor them to see how they perform. The skeptic claims immediately that climate collapse will render the selected large protected areas unsuitable for many of the area’s fauna and flora as time progresses.

We cannot at present answer the simple question how big is big enough? The result of all this uncertainly is that we must set boundaries to our conservation goals, and that these will have to be on a local scale. We need to define a time limit for achieving our goals, perhaps 50 years is one we could cope with, and we need to monitor a defined subset of species so that we can track the resilience of the system under study over time and be able to use some feasible management tools if species are in long-term decline. Some national parks are now able to set these goals and keep track of how ecosystems are changing but in a majority of cases we do not have the monitoring data to define success or failure. This problem is not new (Newmark 1985, 1995).

Meanwhile we search for alternative approaches. In some cases, corridors between small protected areas are helpful, and in other cases fenced areas are sufficient for protecting threatened species, particularly when introduced predators are the major problem (Legge et al. 2018). More elaborate approaches must take account of climate change on protected areas (e.g. Rilov et al. 2019). Methods are being developed to deal with mosaic ecosystems in which conservation reserves are embedded in agricultural landscapes (Nowack et al. 2019). The conflict always remains whether to aim conservation at specific taxa or to try to maximize the number of species retained.

These issues of how big are most readily solvable in areas like northern Canada or Alaska, Russia, and in marine environments that are still relatively lightly used for human activities. Analyses of particular groups of taxa (e.g. trees, Médail et al. 2019) can also be usefully evaluated for conservation purposes for relatively large landscapes. The question of how big is big enough will continue to an important one for continuing efforts in conservation.

The assumption we should question is what size of area will protect the small species of insects and plants. It often seems to be assumed that our existing parks are too small for the larger species of the fauna and flora but are sufficiently large for small insects and plants. One should doubt that this simple principle is correct.

The related question of how long is long enough (for monitoring) is much simpler to deal with because in principle there should be no limit. In practice this limit is set by money and person-power, and in the end these decisions will rest on how much the world’s leaders are concerned about the loss of biodiversity. If the value of a species is directly related to its size, much could be lost with little public concern, and these questions of how big and how long will be “academic” in the worst sense of this word.

Anderson, M.G., et al. (2018) The migratory bird treaty and a century of waterfowl conservation. Journal of Wildlife Management, 82, 247-259. doi: 10.1002/jwmg.21326

Hewson, C.M., et al. (2018) Estimating national population sizes: Methodological challenges and applications illustrated in the common nightingale, a declining songbird in the UK. Journal of Applied Ecology, 55, 2008-2018. doi: 10.1111/1365-2664.13120

Legge, S., et al. (2018) Havens for threatened Australian mammals: the contributions of fenced areas and offshore islands to the protection of mammal species susceptible to introduced predators. Wildlife Research, 45, 627-644. doi: 10.1071/WR17172

Mason, C., et al. (2018) Telemetry reveals existing marine protected areas are worse than random for protecting the foraging habitat of threatened shy albatross (Thalassarche cauta). Diversity & Distributions, 24, 1744-1755. doi: 10.1111/ddi.12830

Médail, F., et al. (2019) What is a tree in the Mediterranean Basin hotspot? A critical analysis. Forest ecosystems, 6, 17. doi: 10.1186/s40663-019-0170-6

Newmark, W.D. (1985) Legal and biotic boundaries of Western North American National Parks: A problem of congruence. Biological Conservation, 33, 197-208. doi: 10.1016/0006-3207(85)90013-8

Newmark, W.D. (1995) Extinction of mammal populations in Western North American national parks. Conservation Biology, 9, 512-526. doi: 10.1046/j.1523-1739.1995.09030512.x

Nowack, S., Bauch, C.T. & Anand, M. (2019) A local optimization framework for addressing conservation conflicts in mosaic ecosystems. PLoS ONE, 14, e0217812. doi: 10.1371/journal.pone.0217812

Rilov, G., et al. (2019) Adaptive marine conservation planning in the face of climate change: What can we learn from physiological, ecological and genetic studies? Global Ecology and Conservation, 17, e00566. doi: 10.1016/j.gecco.2019.e00566

Big Science – Poor Data?

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The big global problems of our time are climate change, human population growth, and migration. From these emerge all the others that worry us from inequality leading to poverty, regional wars, emerging diseases, and biodiversity loss. As ecologists we typically worry about climate change and biodiversity loss. We can do little directly about climate change except to change our life style and replace our do-nothing-politicians. We can have some effect on biodiversity conservation, a subject of later discussions. But the elephant in the room is always climate change, and Bill McKibben (2019) has presented us with a synopsis of a positive evaluation from the viewpoint of fossil fuels and is currently bringing out a book on these issues (McKibben 2019a).

There is much discussion of these articles in reviews such as Diamond (2019) and in the social media. The negative concerns for the future have in recent years been getting more press than the positive possibilities and these negative views may cause the public to give up and say all efforts are hopeless. But these three references from McKibben and Diamond push the possibility of a positive outcome, premised partly on the growing concern of humans to the effects of climate change and the emerging technologies in energy capture that do not depend on oil and gas. I do not wish to question these statements but rather to raise the question of where ecological scientists should fit into this picture.

If natural capital is in decline and some to many species are at risk of extinction, what should be the reaction of a young ecologist just starting their ecological career? I can see two extreme responses to the current situation. One I will call the Carry-on-Regardless approach, and the other the Mad Panic approach. The Carry-on Regardless approach believes that we as one or a few scientists have little ability to change the global paradigm of environmental destruction. Certainly, we will use our own efforts to educate and give good environmental example to all we encounter. But as a scientist the most important achievement one can make is to do good ecological science, to understand in some small way how populations and communities of organisms interact and sustain themselves at the present time. In this way we can hopefully solve some immediate practical problems but more importantly collect some critical data for the next generations of ecologists to use in understanding the changes that will go on during the next several centuries. In a simple manner, future ecologists will be able to say, ‘so this is how system X was working in 2020”. We have no way to know now how much our hard-earned knowledge will be useful to our great-grandchildren, but we press on in the hope that it will be of some help in understanding the trace of the human footprint down the ages.

The Mad Panic approach at the other extreme argues that you should stop all the research that you are doing and become an advocate to try to convince the world to change course and prevent disaster. There is no time to do research, we ought to be out there shouting from the rooftops. If you wish to work at the research end of this school of thought you should perhaps be looking for an ecological disaster (e.g. plastics in the ocean) that you can investigate to beat politicians over the head about how we must change now to prevent further disaster. There is certainly a need for this sort of action.

The problem is how to advise ecologists starting their careers. There is no simple answer, and some are better at the first approach and others at the second. The key point is that we need both, and my concern (being a Carry-on phenotype) is that we need to have clear and precise data of how the planet is changing as a prerequisite for the second approach. We do not have this now except for a few species in a few locations. We have very little long-term data on biodiversity, and we only kid ourselves if we decide that a 3-year study can be classified as a long-term study, or that a list of species in a given area tells us something about ecosystem function. Consider how long it has taken to show clear trends in climate data, or in a more news-worthy area how little economic understanding has emerged from all the detailed minute-by-minute data on the stock market over the last 70 years.

So, we end up with big questions and poor data, and somehow hope that we can model the future changes in the world’s ecosystems to give the public guidance. To achieve this goal, we need more Carry-on Regardless ecologists doing good work and fewer, less strident Mad Panic environmentalists. Environmental warning bells are certainly going off, and we should listen to them and try to gather the data necessary to understand what is happening and how good management might counter negative environmental trends. It is good to be optimistic, but we must couple our optimism with strong ecological studies to understand how communities and ecosystems function. And we are a long way from having enough of these basic studies to be confident of future projections to guide the next generations.

Diamond, Jared. 2019. Striking a balance between fear and hope on climate change. New York Times, 15 April 2019.

McKibben, Bill. 2019. A Future Without Fossil Fuels? New York Review of Books, April 4, 2019, pp.

McKibben, Bill. 2019a. Falter: Has the Hunan Game Begun to Play Itself Out? Henry Holt and Company, 291 pp. ISBN:13: 9781250178268

Another Simple Problem in Ecology

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In 1951 Bill Ricker and his colleagues at the Pacific Biological Station became interested in the size of the salmon caught in the West Coast fishery (Ricker 1995). By 1975 they had observed that pink salmon (Oncorhynchus gorbuscha), coho (O. kisutch) and chinook (O. tshawytscha) had all declined in size, pink salmon by 40%, coho dropped 20-30%, and chinook from 9kg to 6kg. Since 1975 changes have become more complicated in different parts of the fishery (Ricker 1995). Why these changes? Ricker concluded:

“From the data available up to 1975, I suggested that a change in the genetic constitution of salmon stocks was mainly responsible for the observed decreases in size. After all, if you are raising beef cattle, for example, you select breeding stock with a proven history of fast growth. Our fisheries have been doing exactly the opposite.” (Ricker 1995 page 600).

Everyone had read Charles Darwin and knew about natural selection and here was more clear evidence in the natural world.

            About this time wildlife managers became interested in the same possibility that by hunters selecting the largest mammals in order to obtain a trophy catch, there might be changes in the genetics of large mammal populations that could be detrimental. Festa-Bianchet and Mysterud (2018) have now reviewed the literature on the evolutionary pressures from size-selective harvests of large mammals and have shown that a series of strong conditions must be present to determine if hunting is exerting evolutionary pressure within a harvested population. They point out that the problem is far from simple. For a start one must determine if the trait that hunters select for is heritable. Since often this is antler or horn size or other dominance traits, we need to know how heritable such a trait is. For those large mammals for which we have data, heritability is low to moderate (20-40%). Then we need data on the strength of hunting selection in relation to sexual selection for large antlers or horns or body size. In general, the detection of evolutionary changes in natural populations is difficult.

Festa-Bianchet and Mysterud (2018) review the strength of inference from the available data and point out that the gold standard of ‘experimental manipulation with identified genes that affect horn/antler size, and evidence of changes in both gene frequency and trait size after manipulation’ has not been achieved for any species at the present time. Weaker evidence is available from long-term monitoring studies of several populations of the same species that are subject to different hunting pressures, and even these weaker studies are available for only a handful of ungulate species. The bottom line is that we need much more research on this ‘simple problem’ to make sure that hunting is sustainable from both an ecological and an evolutionary viewpoint.

Back to the fisheries. There has been an explosion of interest in the potential effects of fishing methods on changes in fish stocks. Kuparinen and Festa-Bianchet (2017) provide a good overview while Tillotson and Quinn (2018) dig into the details of potential selection by fisheries on the timing of migration and breeding. Morita (2019) leads us back to the Pacific salmon and how we could be selecting for earlier migrations from ocean to fresh water breeding grounds. Clearly there is much left to do on this important ‘simple’ topic.

Festa-Bianchet, M. & Mysterud, A. (2018) Hunting and evolution: theory, evidence, and unknowns. Journal of Mammalogy, 99, 1281-1292. doi: 10.1093/jmammal/gyy138

Kuparinen, A. & Festa-Bianchet, M. (2017) Harvest-induced evolution: insights from aquatic and terrestrial systems. Philosophical Transactions of the Royal Society of London, B, 372, 20160036. doi: 10.1098/rstb.2016.0036

Morita, K. (2019) Earlier migration timing of salmonids: an adaptation to climate change or maladaptation to the fishery? Canadian Journal of Fisheries and Aquatic Sciences, 76, 475-479. doi: 10.1139/cjfas-2018-0078

Ricker, W.E. (1995) Trends in the average size of Pacific salmon in Canadian catches. Climate Change and Northern Fish Populations (ed. R.J. Beamish), pp. 593-602.Canadian Special Publication of Fisheries and Aquatic Sciences, Ottawa, Ontario.

Tillotson, M.D. & Quinn, T.P. (2018) Selection on the timing of migration and breeding: A neglected aspect of fishing-induced evolution and trait change. Fish and Fisheries, 19, 170-181. doi: 10.1111/faf.12248

Economics from a naïve non-economist

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If you spend time in the world of social media, you may already know about the University of California vs. Elsevier Publishers on the economics of publishing scientific journal papers. See: https://www.theatlantic.com/science/archive/2019/03/uc-elsevier-publisher/583909/ and the background information in https://www.theguardian.com/science/2017/jun/27/profitable-business-scientific-publishing-bad-for-science for a sample discussion. Now I know nothing in particular about economics but I can perhaps add a footnote to this discussion from the point of view of having published ecology textbooks and investigated their cost.

Perhaps 20 years ago I had a good conversation with an honest person in the know of a book company I have sometimes published with, regarding the costs of publishing textbooks. At that point in the Stone Age, biology texts were about $100 or slightly less, and often some publishers would put out a paperback version of the same text at a much cheaper price, perhaps $35 or $40 for sale outside of North America. I thought that perhaps they ought to allow students in North America to buy the cheaper paper version, so I enquired about costs. The bottom line is that it cost perhaps $0.25 more for publishing a copy of the hardback versus the cheaper soft paperback version. The quality of the paper was no different in the two versions, and thus the costs of production were very close while the prices to the buyer were greatly different. This could be explained by putting all the heavy costs on the hardback copy because it takes a lot of editing and printing to set up the book for a printing run. So, one could argue that the cost difference should not rest on the costs of the paper alone. This led into an interesting conversation that is now only a memory for me since the CIA did not yet at that time record all phone calls of suspicious academics like ecologists. I was told that the publisher who must remain nameless wished to achieve a profit of 35-40% per year of costs for any book. Not all books sell well, and after a few years sales drop off and the whole process begins again. But my naïve question was where can I invest my savings to get a return of even 25% per year? At the present time I can perhaps get 1% per year in the bank. The author of your textbook gets perhaps 2% to 3% of the money you pay for your text, so I do not think this problem rests with the author’s excess profits.

I found it insane that anyone could simply assume that such profits are reasonable in a world that is sustainable. Yet I think now that this is a typical economic viewpoint that underlies the problems of inequality in our world, and the general rule that the rich get richer and the poor get little. So Elsevier publishes research papers that rest in large part on research work paid for by the government, with the researchers being paid for by universities or public agencies, and virtually all the preparation of the published results being done by the researchers, and then as the final blow the publisher wishes to charge the research worker (or their university) for the actual published article. So, for the moment the University of California has set a halt to this profit charade. I am sure we will soon see a set of tearful articles from publishers that they are themselves in the poorhouse and do not make enough profit as, for example, comparable corporations such as Shell Oil or Facebook. So be it.

A cheer for those scientific journals that do not ride this profit bandwagon, and the editors that are not paid for all their work, and the scientists who review submitted papers to improve them and are paid nothing for their extra effort. Perhaps someday we can be finished with the modern economic theory that seems to treat the world as a large Ponzi Scheme, and return to a saner sustainable economic world.

Is Conservation Ecology Destroying Ecology?

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Ecology became a serious science some 100 years ago when the problems that it sought to understand were clear and simple: the reasons for the distribution and abundance of organisms on Earth. It subdivided fairly early into three parts, population, community, and ecosystem ecology. It was widely understood that to understand population ecology you needed to know a great deal about physiology and behaviour in relation to the environment, and to understand community ecology you had to know a great deal about population dynamics. Ecosystem ecology then moved into community ecology plus all the physical and chemical interactions with the whole environment. But the sciences are not static, and ecology in the past 60 years has come to include nearly everything from chemistry and geography to meteorological sciences, so if you tell someone you are an ‘ecologist’ now, they have only a vague idea of what you do.

The latest invader into the ecology sphere has been conservation biology so that in the last 20 years it has become a dominant driver of ecological concerns. This has brought ecology into the forefront of publicity and the resulting political areas of controversy, not necessarily bad but with some scientific consequences. ‘Bandwagons’ are for the most part good in science because it attracts good students and professors and brings public support on side. Bandwagons are detrimental when they draw too much of the available scientific funding away from critical basic research and champion scientific fads.

The question I wish to raise is whether conservation ecology has become the latest fad in the broad science of ecology and whether this has derailed important background research. Conservation science begins with the broad and desirable goal of preserving all life on Earth and thus thwarting extinctions. This is an impossible goal and the question then becomes how can we trim it down to an achievable scientific aim? We could argue that the most important goal is to describe all the species on Earth, so that we would then know what “money” we have in the “bank”. But if we look at the insects alone, we see that this is not an achievable goal in the short term. And the key to many of these issues is what we mean by “the short term”. If we are talking10 years, we may have very specific goals, if 100 years we may redesign the goal posts, and if 1000 years again our views might change.

This is a key point. As humans we design our goals in the time frames of months and a few years, not in general in geological time. Because of climate change we are now being forced to view many things in a shorter and shorter time frame. If you live in Miami, you should do something about sea level rise now. If you grow wheat in Australia, you should worry about decreasing annual rainfall. But science in general does not have a time frame. Technology does, and we need a new phone every year, but the understanding of cancer or the ecology of tropical rain forests does not have a deadline.

But conservation biology has a ticking clock called extinction. Now we can compound our concerns about climate change and conservation to capture more of the funding for biological research in order to prevent extinctions of rare and endangered species. 

Ecological science over the past 40 years has been progressing slowly through population ecology into community and ecosystem ecology while learning that the details of populations are critical to the understanding of community function and learning how communities operate is necessary for understanding ecosystem change. None of this has been linear progress but rather a halting progression with many deviations and false leads. In order to push this agenda forward more funding has clearly been needed because teams of researchers are needed to understand a community and even more people to study an ecosystem. At the same time the value of long-term studies has become evident and equipment has become more expensive.

We have now moved into the Anthropocene in which in my opinion the focus has shifted completely from trying to answer the primary problems of ecological science to the conservation of organisms. In practice this has too often resulted in research that could only be called poor population ecology. Poor in the sense of the need for immediate short-term answers for declining species populations with no proper understanding of the underlying problem. We are faced with calls for funding that are ‘crying wolf’ with inadequate data but heartfelt opinions. Recovery plans for single species or closely related groups focus on a set of unstudied opinions that may well be correct, but to test these ideas in a reliable scientific manner would take years. Triage on a large scale is practiced without discussing the issue, and money is thrown at problems based on the publicity generated. Populations of threatened species continue to decline in what can only be described as failed management. Blame is spread in all directions to developers or farmers or foresters or chemical companies. I do not think these are the signs of a good science which above all ought to work from the strength of evidence and prepare recovery plans based on empirical science.

Part of the problem I think lies in the modern need to ‘do something’, ‘do anything’ to show that you care about a particular problem. ‘We have now no time for slow-moving conventional science, we need immediate results now’. Fortunately, many ecologists are critical of these undesirable trends in our science and carry on (e.g. Amos et al. 2013). You will not likely read tweets about these people or read about them in your daily newspapers. Evidence-based science is rarely quick, and complaints like those that I give here are not new (Sutherland et al. 2004, Likens 2010, Nichols 2012).  

Amos, J.N., Balasubramaniam, S., Grootendorst, L. et al. (2013). Little evidence that condition, stress indicators, sex ratio, or homozygosity are related to landscape or habitat attributes in declining woodland birds. Journal of Avian Biology 44, 45-54. doi: 10.1111/j.1600-048X.2012.05746.x

Likens, G.E. (2010). The role of science in decision making: does evidence-based science drive environmental policy? Frontiers in Ecology and the Environment 8, e1-e9. doi: 10.1890/090132

Nichols, J.D. (2012). Evidence, models, conservation programs and limits to management. Animal Conservation 15, 331-333. doi: 10.1111/j.1469-1795.2012.00574.x

Sutherland, W.J., Pullin, A.S., Dolman, P.M., Knight, T.M. (2004). The need for evidence-based conservation. Trends in Ecology and Evolution 19, 305-308. doi: 10.1016/j.tree.2004.03.018

How to do Conservation Planning

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The biota of the Earth is in trouble because of human activities, and the question conservation people ask is what should we do about it? Conservation planning has become the key way to proceed, but its implementation has unleased an unholy row of the best way to proceed. In a sense conservation planning is like city planning in having to make decisions about what to do where. There are two broad approaches to conservation: focus on species-at-risk and their needs and plan accordingly to protect them. Alternatively focus on ecosystems and protect them without all the detailed knowledge that is required for protecting species-at-risk. This is the first source of conflict because the public at large falls in love with species, so polar bears and blue whales and tigers are an easy sell to obtain funding from private and government sources. This is at present the dominant force in conservation, and if there is enough information available the conservation of polar bears and tigers will act as “umbrella species” to protect many other species at possible risk. So single species conservation can perhaps impinge on ecosystem conservation if we designate national parks or protected areas for the charismatic species that we all admire.

But there are many other species out there that conservation biologists are concerned about, collectively labeled biodiversity. Perhaps we should conserve biodiversity instead of focusing on individual species. But right away we run into two problems. In any ecosystem many of the species present are undescribed so we cannot put a Latin name on them, or if they are described we know almost nothing about their function in the ecosystem. So, we have a key question: do we need to understand ecosystem dynamics before we can prioritize biodiversity conservation? Most ecologists believe that many of the species in any ecosystem could disappear with little effect on ecosystem functioning. The arguments are largely about which species can we dispense with, and true conservation advocates say that all must be saved.

The problem is that conservation planning is a resource allocation problem – where do we put our money (Gerber et al. 2018)? Ideas about how best to establish rules for setting aside critical areas for conservation go back to Pressey and Nicholls (1989) and in subsequent years the conservation planning literature has exploded (e.g. Margules and Pressey 2000). Techniques for conservation planning were first designed to maximize the number of species retained in the reserve, and this was the first of many problems. You had to have ‘empty’ land to set aside in the proposed reserve and you had to know the species that the reserve would protect. This was perhaps more possible in Australia or Canada but difficult to implement in the USA and Europe where much land was in private hands.

Conservation planning involves a set of difficult hurdles. If we concentrate on single species, we may well find that protected areas are in the wrong place (Mason et al. 2018). If we concentrate on ecosystems, we must decide on which ecosystems containing which species, and make this decision when the ecosystems are poorly documented and changing with climate change. All this planning must take place in the public arena where people and their elected politicians are trying to decide whether it is more important to protect large charismatic species like caribou or zebras rather than a few small butterflies. In general, all these decisions are made in a near-absence of ecological concerns about predator-prey interactions, competition, movements, or disease threats, the factors individual ecologists spend their lives studying. Much discussion focuses on critical habitat for a favoured species, and, given that we can define critical habitat for our favoured species, how much is needed and how much will it cost (Gerber et al. 2018). By 2015, critical habitat had been legally identified for only 45% of listed species in the United States, 13% in Canada and less than 1% in Australia (Martin et al. 2017, Bird and Hodges 2017). Once we have identified ‘critical habitats’ for a threatened species, we need to be sure it is not an ecological trap (Battin 2004, Camaclang et al. 2014, Lamb et al. 2017), or that the data we have is not related to the data we need for conservation planning (Dallas and Hastings 2018).

Given all these problems, many efforts are underway to plan conservation areas, particularly in the marine realm (Edgar et al. 2014, Mason et al. 2018). What is necessary now is follow up by careful monitoring the population and ecosystem changes in areas that are set aside for conservation. Without monitoring we will lack an early-warning system to pick up mistakes and try to correct them (Lindenmayer et al. 2018).  

Álvarez-Romero JG, Mills M, Adams VM, Gurney GG, Pressey RL (2018). Research advances and gaps in marine planning: towards a global database in systematic conservation planning. Biological Conservation 227, 369-382. Doi: 10.1016/j.biocon.2018.06.027

Battin J (2004). When good animals love bad habitats: ecological traps and the conservation of animal populations. Conservation Biology 18, 1482-1491. Doi: 10.1111/geb.12820

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

Camaclang AE, Maron M, Martin TG, Possingham HP (2015). Current practices in the identification of critical habitat for threatened species. Conservation Biology 29, 482-492. Doi: 10.1111/cobi.12428

Dallas, T.A. & Hastings, A. (2018) Habitat suitability estimated by niche models is largely unrelated to species abundance. Global Ecology and Biogeography, 27, 1448-1456. Doi: 10.1111/geb.12820

Edgar GJ, et al. (2014). Global conservation outcomes depend on marine protected areas with five key features. Nature 506, 216-220. Doi: 10.1038/nature13022

Gerber LR, et al. (2018). Endangered species recovery: A resource allocation problem. Science 362, 284-286. Doi: 10.1126/science.aat8434

Lamb CT, Mowat G, McLellan BN, Nielsen SE & 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 DB, Likens GE, Franklin JF (2018). Earth Observation Networks (EONs): Finding the Right Balance. Trends in Ecology & Evolution 33, 1-3. Doi: 10.1016/j.tree.2017.10.008

Margules CR, Pressey RL (2000). Systematic conservation planning. Nature 405, 243-253. Doi: 10.1038/35012251

Pressey RL, Nicholls AO (1989). Application of a numerical algorithm to the selection of reserves in semi-arid New South Wales. Biological Conservation 50, 263-278. Doi: 10.1016/0006-3207(89)90013-X

Martin TG, Camaclang AE, Possingham HP, Maguire LA, Chades I (2017). Timing of protection of critical habitat matters. Conservation Letters 10, 308-316. Doi: 10.1111/conl.12266

Mason C, et al. (2018). Telemetry reveals existing marine protected areas are worse than random for protecting the foraging habitat of threatened shy albatross (Thalassarche cauta). Diversity & Distributions 24, 1744-1755. Doi: 10.1111/ddi.12830

Why do Scientists Reinvent Wheels?

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

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

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

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

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

Blaming Climate Change for Ecological Changes

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The buzz word for all ecological applications for funding and for many submitted papers is climate change. Since the rate of climate change is not something ecologists can control, there are only two reasons to cite climate change as a reason to fund current ecological research. First, since change is continuous in communities and ecosystems, it would be desirable to determine how many of the observed changes might be caused by climate change. Second, it might be desirable to measure the rate of change in ecosystems, correlate these changes to some climate variable, and then use these data as a political and social tool to stimulate politicians to do something about greenhouse gas emissions. The second approach is that taken by climatologists who blame hurricanes and tornadoes on global warming. There is no experimental way to trace any particular hurricane to particular amounts of global warming, so it is easy for critics to say these are just examples of weather variation of which we have measured much over the last 150 years and paleo-ecologists have traced over tens of thousands of years using proxies from tree rings and sediment cores. If we are to use the statistical approach we need a large enough sample to argue that extreme events are becoming more frequent, and that might take 50 years by which time the argument would be made too late to request proper action.

The second approach to prediction in ecology is fraught with problems, as outlined in Berteaux et al. (2006) and Dietze (2017). The first approach has many statistical problems as well in selecting a biologically coherent model that can be tested by in a standard scientific manner. Since there are a very large number of climate variables, the possibility of spurious correlations is excessive, and the only way to avoid these kinds of results is to be predictive and to have a biological causal chain that is testable. Myers (1998) reviewed all the fishery data for predictive models of juvenile recruitment that used environmental variables as predictors and data was subsequently collected and tested with the published model. The vast majority of these aquatic models failed when retested but a few were very successful. The general problem is that model failures or successes might not be published so even this approach can be biased if only a literature survey is undertaken. The take home message from Myers (1998) was that almost none of the recruitment-environment correlations were being used in actual fishery management.

How much would this conclusion about the failure of environmental models in fishery management apply to other areas in ecology? Mouquet et al. (2014) pointed out that predictions could be classified as ‘explanatory’ or ‘anticipatory’ and that “While explanatory predictions are necessarily testable, anticipatory predictions need not be…….In summary, anticipatory predictions differ from explanatory predictions in that they do not aim at testing models and theory. They rely on the assumption that underlying hypotheses are valid while explanatory predictions are based on hypotheses to be tested. Anticipatory predictions are also not necessarily supposed to be true.” (page 1296). If we accept these distinctions, we have (I think) a major problem in that many of the predictive models put forward in the ecological literature are anticipatory, so they would be of little use to a natural resource manager who requires an explanatory model.

If we ignore this problem with anticipatory predictions, we can concentrate on explanatory predictions that are useful to managers. One major set of explanatory predictions in ecology are those associated with range changes in relation to climate change. Cahill et al. (2014) examined the conventional hypothesis that warm-edge range limits are set by biotic interactions rather than abiotic interactions. Contrary to expectations, they found in 125 studies that abiotic factors were more frequently supported as setting warm-edge range limits. Clearly a major paradigm about warm-edge range limits is of limited utility.

Explanatory predictions are not always explicit. Mauck et al. (2018) for example developed a climate model to predict reproductive success in Leach’s storm petrel on an island off New Brunswick in eastern Canada. From 56 years of hatching success they concluded that annual global mean temperature during the spring breeding season was the single most important predictor of breeding success. They considered only a few measures of temperature as predictor variables and found that a quadratic form of annual global mean temperature was the best variable to describe the changes in breeding success. The paper speculates about how global or regional mean temperature could possibly be an ecological predictor of breeding success, and no mechanisms are specified. The actual data on breeding success are not provided in the paper, even as a temporal plot. Since global temperatures were rising steadily from 1955 to 2010, any temporal trend in any population parameter that is rising would correlate with temperature records. The critical quadratic relationship in their analysis suggests that a tipping point was reached in 1988 when hatching success began to decline. Whether or not this is a biologically correct explanatory model can be determined by additional data gathered in future years. But it would be more useful to find out what the exact ecological mechanisms are.

If the ecological world is going to hell in a handbasket, and temperatures however measured are going up, we can certainly construct a plethora of models to describe the collapse of many species and the rise of others. But this is hardly progress and would appear to be anticipatory predictions of little use to advancing ecological science, as Guthery et al. (2005) pointed out long ago. Someone ought to review and evaluate the utility of AIC methods as they are currently being used in ecological and conservation science for predictions.

Berteaux, D., Humphries, M.M., Krebs, C.J., Lima, M., McAdam, A.G., Pettorelli, N., Reale, D., Saitoh, T., Tkadlec, E., Weladji, R.B., and Stenseth, N.C. (2006). Constraints to projecting the effects of climate change on mammals. Climate Research 32, 151-158. doi: 10.3354/cr032151.

Cahill, A.E., Aiello-Lammens, M.E., Fisher-Reid, M.C., Hua, X., and Karanewsky, C.J. (2014). Causes of warm-edge range limits: systematic review, proximate factors and implications for climate change. Journal of Biogeography 41, 429-442. doi: 10.1111/jbi.12231.

Dietze, M.C. (2017). Prediction in ecology: a first-principles framework. Ecological Applications 27, 2048-2060. doi: 10.1002/eap.1589.

Guthery, F.S., Brennan, L.A., Peterson, M.J., and Lusk, J.J. (2005). Information theory in wildlife science: Critique and viewpoint. Journal of Wildlife Management 69, 457-465. doi: 10.1890/04-0645.

Mauck, R.A., Dearborn, D.C., and Huntington, C.E. (2018). Annual global mean temperature explains reproductive success in a marine vertebrate from 1955 to 2010. Global Change Biology 24, 1599-1613. doi: 10.1111/gcb.13982.

Mouquet, N., Lagadeuc, Y., Devictor, V., Doyen, L., and Duputie, A. (2015). Predictive ecology in a changing world. Journal of Applied Ecology 52, 1293-1310. doi: 10.1111/1365-2664.12482.

Myers, R.A. (1998). When do environment-recruitment correlations work? Reviews in Fish Biology and Fisheries 8, 285-305. doi: 10.1023/A:1008828730759.