Tag Archives: progress in ecology

On the Use of “Density-dependent” in the Ecological Literature

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The words ‘density-dependent’ or ‘density dependence’ appear very frequently in the ecological literature, and I write this blog in a plea to never use these words unless you have a very strong definition attached to them. If you have a spare day, count how many times these words appear in a single recent issue of Ecology or the Journal of Animal Ecology and you will get a dose of my dismay. In the Web of Science a search for these words in a general ecology context gives about 1300 papers using these words since 2010, or approximately 1 paper per day.

There is an extensive literature on what density dependence means. In the modeling world, the definition is simple and can be found in every introductory ecology textbook. But it is the usage of the words ‘density-dependence’ in the real world that I want to discuss in this blog.

The concept can be quite meaningless, as Murray (1982) pointed out so many years ago. At its most modest extreme, it only says that, sooner or later, something happens when a population gets too large. Everyone could agree with that simple definition. But if you want to understand or manage population changes, you will need something much more specific. More specific might mean to plot a regression of some demographic variable with population density on the X axis. As Don Strong (1986) pointed out long ago a more typical result is density-vagueness. So if and when you write about a density-dependent relationship, at least determine how well the data fit a straight or curved line, and if the correlation coefficient is 0.3 or less you should get concerned that density has little to do with your demographic variable. If you wish to understand population dynamics, you will need to understand mechanisms and population density is not a mechanism.

Often the term density-dependent is used as a shorthand to indicate that some measured variable such as the amount of item X in the diet is related to population density. In most of these cases it is more appropriate to say that item X is statistically related to population density, and avoid all the baggage associated with the original term. Too often statements are made about mortality process X being ‘inversely density dependent’ or ‘directly density dependent’ with no data that supports such a strong conclusion.

So if there is a simple message here it is only that when you write ‘density-dependent’ in your manuscript, see if is related to the population regulation concept or if it is a simple statistical statement that is better described in simple statistical language. In both cases evaluate the strength of the evidence.

Ecology is plagued with imprecise words that can mean almost anything if they are not specified clearly, so statements about ‘biodiversity’, ‘ecosystems’, ‘resilience’, ‘diversity’, ‘metapopulations’, and ‘competition’ are fine to use so long as you indicate exactly what the operational meaning of the word entails. ‘Density-dependence’ is one of these slippery words best avoided unless you have some clear mechanism or process in mind.

Murray, B.G., Jr. (1982) On the meaning of density dependence. Oecologia, 53, 370-373.

Strong, D.R. (1986) Density-vague population change. Trends in Ecology and Evolution, 1, 39-42.

Was the Chitty Hypothesis of Population Regulation a ‘Big Idea’ in Ecology and was it successful?

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Jeremy Fox in his ‘Dynamic Ecology’ Blog has raised the eternal question of what have been the big ideas in ecology and were they successful, and this has stimulated me to write about the Chitty Hypothesis and its history since 1952. I will write this from my personal observations which can be faulty, and I will not bother to put in many references since this is a blog and not a formal paper.

In 1952 when Dennis Chitty at Oxford finished his thesis on vole cycles in Wales, he was considered a relatively young heretic because he did not see any evidence in favour of the two dominant paradigms of population dynamics – that populations rose and fell because of food shortage or predation. David Lack vetoed the publication of his Ph.D. paper because he did not agree with Chitty’s findings (Lack believed that food supplies explained all population changes). His 1952 thesis paper was published only because of the intervention of Peter Medawar. Chitty could see no evidence of these two factors in his vole populations and he began to suspect that social factors were involved in population cycles. He tested Jack Christian’s ideas that social stress was a possible cause, since it was well known that some rodents were territorial and highly aggressive, but stress as measured by adrenal gland size did not fit the population trends very well. He then began to suspect that there might be genetic changes in fluctuating vole populations, and that population processes that occurred in voles and lemmings may occur in a wide variety of species, not just in the relatively small group of rodent species, which everyone could ignore as a special case of no generality. This culminated in his 1960 paper in the Canadian Journal of Zoology. This paper stimulated many field ecologists to begin experiments on population regulation in small mammals.

Chitty’s early work contained a ‘big idea’ that population dynamics and population genetics might have something to contribute to each other, and that one could not assume that every individual had equal properties. These ideas of course were not just his, and Bill Wellington had many of the same ideas in studying tent caterpillar population fluctuations. When Chitty suggested these ideas during the late 1950s he was told by several eminent geneticists who must remain nameless that his ideas were impossible, and that ecologists should stay out of genetics because the speed of natural selection was so slow that nothing could be achieved in ecological time. Clearly thinking has now changed on this general idea.

So if one could recognize these early beginnings as a ‘big idea’ it might be stated simply as ‘study individual behaviour, physiology, and genetics to understand population changes’, and it was instrumental in adding another page to the many discussions of population changes that had previously mostly included only predators, food supplies, and potentially disease. All this happened before the rise of behavioural ecology in the 1970s.

I leave others to judge the longer term effects of Chitty’s early suggestions. At present the evidence is largely against any rapid genetic changes in fluctuating populations of mammals and birds, and maternal effects now seem a strong candidate for non-genetic inheritance of traits that affect fitness in a variety of vertebrate species. And in a turn of fate, stress seems to be a strong candidate for at least some maternal effects, and we are back to the early ideas of Jack Christian and Hans Selye of the 1940s, but with greatly improved techniques of measurement of stress in field populations.

Dennis Chitty was a stickler for field experiments in ecology, a trend now long established, and he made many predictions from his ideas, often rejected later but always leading to more insights of what might be happening in field populations. He was a champion of discussing mechanisms of population change, and found little use for the dominant paradigm of the density dependent regulation of populations. Was he successful? I think so, from my biased viewpoint. I note he had less recognition in his lifetime than he deserved because he offended the powers that be. For example, he was never elected to the Royal Society, a victim of the insularity and politics of British science. But that is another story.

Chitty, D. (1952) Mortality among voles (Microtus agrestis) at Lake Vyrnwy, Montgomeryshire in 1936-9. Philosophical Transactions of the Royal Society of London, 236, 505-552.

Chitty, D. (1960) Population processes in the vole and their relevance to general theory. Canadian Journal of Zoology, 38, 99-113.

On Tipping Points and Regime Shifts in Ecosystems

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A new important paper raises red flags about our preoccupation with tipping points, alternative stable states and regime shifts (I’ll call them collectively sharp transitions) in ecosystems (Capon et al. 2015). I do not usually call attention to papers but this paper and a previous review (Mac Nally et al. 2014) seem to me to be critical for how we think about ecosystem changes in both aquatic and terrestrial ecosystems.

Consider an oversimplified example of how a sharp transition might work. Suppose we dumped fertilizer into a temperate clear-water lake. The clear water soon turns into pea soup with a new batch of algal species, a clear shift in the ecosystem, and this change is not good for many of the invertebrates or fish that were living there. Now suppose we stop dumping fertilizer into the lake. In time, and this could be a few years, the lake can either go back to its original state of clear water or it could remain as a pea soup lake for a very long time even though the pressure of added fertilizer was stopped. This second outcome would be a sharp transition, “you cannot go back from here” and the question for ecologists is how often does this happen? Clearly the answer is of great interest to natural resource managers and restoration ecologists.

The history of this idea for me was from the 1970s at UBC when Buzz Holling and Carl Walters were modelling the spruce budworm outbreak problem in eastern Canadian coniferous forests. They produced a model with a manifold surface that tipped the budworm from a regime of high abundance to one of low abundance (Holling 1973). We were all suitably amazed and began to wonder if this kind of thinking might be helpful in understanding snowshoe hare population cycles and lemming cycles. The evidence was very thin for the spruce budworm, but the model was fascinating. Then by the 1980s the bandwagon started to roll, and alternative stable states and regime change seemed to be everywhere. Many ideas about ecosystem change got entangled with sharp transition, and the following two reviews help to unravel them.

Of the 135 papers reviewed by Capon et al. (2015) very few showed good evidence of alternative stable states in freshwater ecosystems. They highlighted the use and potential misuse of ecological theory in trying to predict future ecosystem trajectories by managers, and emphasized the need of a detailed analysis of the mechanisms causing ecosystem change. In a similar paper for estuaries and near inshore marine ecosystems, Mac Nally et al. (2014) showed that of 376 papers that suggested sharp transitions, only 8 seemed to have sufficient data to satisfy the criteria needed to conclude that a transition had occurred and was linkable to an identifiable pressure. Most of the changes described in these studies are examples of gradual ecosystem changes rather than a dramatic shift; indeed, the timescale against which changes are assessed is critical. As always the devil is in the details.

All of this is to recognize that strong ecosystem changes do occur in response to human actions but they are not often sharp transitions that are closely linked to human actions, as far as we can tell now. And the general message is clearly to increase rigor in our ecological publications, and to carry out the long-term studies that provide a background of natural variation in ecosystems so that we have a ruler to measure human induced changes. Reviews such as these two papers go a long way to helping ecologists lift our game.

Perhaps it is best to end with part of the abstract in Capon et al. (2015):

“We found limited understanding of the subtleties of the relevant theoretical concepts and encountered few mechanistic studies that investigated or identified cause-and-effect relationships between ecological responses and nominal pressures. Our results mirror those of reviews for estuarine, nearshore and marine aquatic ecosystems, demonstrating that although the concepts of regime shifts and alternative stable states have become prominent in the scientific and management literature, their empirical underpinning is weak outside of a specific environmental setting. The application of these concepts in future research and management applications should include evidence on the mechanistic links between pressures and consequent ecological change. Explicit consideration should also be given to whether observed temporal dynamics represent variation along a continuum rather than categorically different states.”

 

Capon, S.J., Lynch, A.J.J., Bond, N., Chessman, B.C., Davis, J., Davidson, N., Finlayson, M., Gell, P.A., Hohnberg, D., Humphrey, C., Kingsford, R.T., Nielsen, D., Thomson, J.R., Ward, K., and Mac Nally, R. 2015. Regime shifts, thresholds and multiple stable states in freshwater ecosystems; a critical appraisal of the evidence. Science of The Total Environment 517(0): in press. doi:10.1016/j.scitotenv.2015.02.045.

Holling, C.S. 1973. Resilience and stability of ecological systems. Annual Review of Ecology and Systematics 4: 1-23. doi:10.1146/annurev.es.04.110173.000245.

Mac Nally, R., Albano, C., and Fleishman, E. 2014. A scrutiny of the evidence for pressure-induced state shifts in estuarine and nearshore ecosystems. Austral Ecology 39: 898-906. doi:10.1111/aec.12162.

A Survey of Strong Inference in Ecology Papers: Platt’s Test and Medawar’s Fraud Model

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In 1897 Chamberlin wrote an article in the Journal of Geology on the method of multiple working hypotheses as a way of experimentally testing scientific ideas (Chamberlin 1897 reprinted in Science). Ecology was scarcely invented at that time and this has stimulated my quest here to see if current ecology journals subscribe to Chamberlin’s approach to science. Platt (1964) formalized this approach as “strong inference” and argued that it was the best way for science to progress rapidly. If this is the case (and some do not agree that this approach is suitable for ecology) then we might use this model to check now and then on the state of ecology via published papers.

I did a very small survey in the Journal of Animal Ecology for 2015. Most ecologists I hope would classify this as one of our leading journals. I asked the simple question of whether in the Introduction to each paper there were explicit hypotheses stated and explicit alternative hypotheses, and categorized each paper as ‘yes’ or ‘no’. There is certainly a problem here in that many papers stated a hypothesis or idea they wanted to investigate but never discussed what the alternative was, or indeed if there was an alternative hypothesis. As a potential set of covariates, I tallied how many times the word ‘hypothesis’ or ‘hypotheses’ occurred in each paper, as well as the word ‘test’, ‘prediction’, and ‘model’. Most ‘model’ and ‘test’ words were used in the context of statistical models or statistical tests of significance. Singular and plural forms of these words were all counted.

This is not a publication and I did not want to spend the rest of my life looking at all the other ecology journals and many issues, so I concentrated on the Journal of Animal Ecology, volume 84, issues 1 and 2 in 2015. I obtained these results for the 51 articles in these two issues: (number of times the word appeared per article, averaged over all articles)

Explicit hypothesis and alternative hypotheses

“Hypothesis”

“Test”

“Prediction”

“Model”

Yes

22%

Mean

3.1

7.9

6.5

32.5

No

78%

Median

1

6

4

20

No. articles

51

Range

0-23

0-37

0-27

0-163

There are lots of problems with a simple analysis like this and perhaps its utility may lie in stimulating a more sophisticated analysis of a wider variety of journals. It is certainly not a random sample of the ecology literature. But maybe it gives us a few insights into ecology 2015.

I found the results quite surprising in that many papers failed Platt’s Test for strong inference. Many papers stated hypotheses but failed to state alternative hypotheses. In some cases the implied alternative hypothesis is the now-discredited null hypothesis (Johnson 2002). One possible reason for the failure to state hypotheses clearly was discussed by Medawar many years ago (Howitt and Wilson 2014; Medawar 1963). He pointed out that most scientific papers were written backwards, analysing the data, finding out what it concluded, and then writing the introduction to the paper knowing the results to follow. A significant number of papers in these issues I have looked at here seem to have been written following Medawar’s “fraud model”.

But make of such data as you will, and I appreciate that many people write papers in a less formal style than Medawar or Platt would prefer. And many have alternative hypotheses in mind but do not write them down clearly. And perhaps many referees do not think we should be restricted to using the hypothetical deductive approach to science. All of these points of view should be discussed rather than ignored. I note that some ecological journals now turn back papers that have no clear statement of a hypothesis in the introduction to the submitted paper.

The word ‘model’ is the most common word to appear in this analysis, typically in the case of a statistical model evaluated by AIC kinds of statistics. And the word ‘test’ was most commonly used in statistical tests (‘t-test’) in a paper. Indeed virtually all of these paper overflow with statistical estimates of various kinds. Few however come back in the conclusions to state exactly what progress has been made by their paper and even less make statements about what should be done next. From this small survey there is considerable room for improvement in ecological publications.

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

Howitt, S.M., and Wilson, A.N. 2014. Revisiting “Is the scientific paper a fraud?”. EMBO reports 15(5): 481-484. doi:10.1002/embr.201338302

Johnson, D.H. (2002) The role of hypothesis testing in wildlife science. Journal of Wildlife Management 66(2): 272-276. doi: 10.2307/3803159

Medawar, P.B. 1963. Is the scientific paper a fraud? In “The Threat and the Glory”. Edited by P.B. Medawar. Harper Collins, New York. pp. 228-233. (Reprinted by Harper Collins in 1990. ISBN: 9780060391126.)

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

On Broad Issues in Ecology

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Any young ecologist wishing to get a grasp on the most important ecological questions of the century could find no better place to start than the thoughtful compilations of Bill Sutherland and his colleagues in the U.K. (Sutherland et al. 2006; Sutherland et al. 2010; Sutherland et al. 2013). In general none of these questions by itself could be the focus of a thesis which by definition must deal with something concrete in a 2-3 year time frame, but they can serve as an overarching goal for a life in science. In all of these exercises an attempt was made to canvass dozens to hundreds of ecologists mainly from Britain but including many from other parts of the world to suggest and then cull down questions into a feasible framework.

This whole approach is most useful, but the authors recognize there are some limitations on exercises of this type. A particularly crucial limitation is:

“…there was a tendency to pose broad questions rather than the more focussed question we were aiming for. There is a tension between posing broad unanswerable questions and those so narrow that they cease to be perceived as fundamental.” (Sutherland et al. 2013, p 60).

I want to focus here on the problems of decomposing broad unanswerable questions in ecology to guide our ecological research in the future. I will discuss here only two of the population ecology questions.

Begin with question 13 on page 61 of Sutherland et al. (2013):

13. How do species and population traits and landscape configuration interact to determine realized dispersal distances?

To translate this into a project we have first to decide on a species to study and specific populations of that species. This opens Pandora’s Box because there are many thousands of species and we have to pick. We do not pick the species at random, yet we wish to develop a general answer to this question, so right away we are lost in how to translate detailed species and area specific data on movements into a general conclusion. So just for illustration suppose we pick a convenient mammal like the red squirrel of North America. It is territorial and diurnal and can be fitted with GPS collars so that movements can be readily measured, so in a sense it would be considered an ideal species to study to answer question 13, even though it is not a random choice. It ranges from Alaska to Labrador down to Arizona and North Carolina. There are a variety of landscapes throughout this geographic range, some highly altered by humans, some not. I do not know how many intensive studies of red squirrels are being or have been carried out. I would wager that the entire NSF (or NSERC, or ARC) budget could be spent to set up a series of studies of duration 5-20 years to gather these data throughout the range of this species. Clearly this will never be done, and we can only hope that the results of a few specific studies in non-randomly chosen areas over shorter time periods will answer question 13 for this one species.

Landscape configuration alone boggles my mind. It is in many areas an historical artifact of fire or human occupation and land use, and yet we need principles to generalize about it. We can model it and pretend that our models mimic reality without the availability of an experimental test. Is this the ecology of the future?

Another way to answer question 13 is to use tiny organisms like insects that we can replicate readily in small areas at minimal cost. Such studies are useful but again I am not sure they will provide a general answer to question 13. These studies can provide insights about specific insects in specific communities and with a good number of such studies on a variety of systems perhaps we would be in a position to achieve some generality. Otherwise we could be accused of “stamp collecting”.

Question 14 (Sutherland et al. 2013 page 61) has similar problems to question 13 but is more tractable I think.

14 What is the heritability/genetic basis of dispersal and movement behaviour?

This is a simpler question, given modern genetics, and can be answered for a particular species in a particular ecosystem. It is restrictive, if it is a field study, in allowing only those species that do not disperse beyond the detection range of the equipment used, and in requiring long-term genetic paternity data to estimate heritability. The methods are available but have so far been used on few species in very specific areas (e.g. superb fairy wrens in a Botanical Garden, Double et al. 2005). It is an important question to ask and answer but again the generality of the results at the present time have to be assumed rather than measured by replicated studies.

The bottom line is that questions like these two have been with ecologists for some years now and have been answered in some detail only in a few vertebrate species in very specific locations. How we generalize these results is an open question even with modern technology.

Double, M.C., Peakall, R., Beck, N.R., and Cockburn, A. 2005. Dispersal, philopatry, and infidelity: dissecting local genetic structure in superb fairy-wrens (Malurus cyaneus). Evolution 59(3): 625-635.

Sutherland, W.J. et al. 2006. The identification of 100 ecological questions of high policy relevance in the UK. Journal of Applied Ecology 43(4): 617-627. doi:10.1111/j.1365-2664.2006.01188.x.

Sutherland, W.J.et al. 2010. A horizon scan of global conservation issues for 2010. Trends in Ecology & Evolution 25(1): 1-7.

Sutherland, W.J. 2013. Identification of 100 fundamental ecological questions. Journal of Ecology 101(1): 58-67. doi:10.1111/1365-2745.12025.

On Adaptive Management

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I was fortunate to be on the sidelines at UBC in the 1970s when Carl Walters, Ray Hilborn, and Buzz Holling developed and refined the ideas of adaptive management. Working mostly in a fisheries context in which management is both possible and essential, they developed a new paradigm of how to proceed in the management of natural resources to reduce or avoid the mistakes of the past (Walters & Hilborn 1978). Somehow it was one of those times in science where everything worked because these three ecologists were a near perfect fit to one another, full of new ideas and inspired guesses about how to put their ideas into action. Many other scientists joined in, and Holling (1978) put this collaboration together in a book that can still be downloaded from the website of the International Institute for Applied Systems Analysis (IASA) in Vienna:
(http://www.iiasa.ac.at/publication/more_XB-78-103.php

Adaptive management became the new paradigm, now taken up with gusto by many natural resources and conservation agencies (Westgate, Likens & Lindenmayer 2013). Adaptive management can be carried out in two different ways. Passive adaptive management involves having a model of the system being managed and manipulating it in a series of ways that improve the model fit over time. Active adaptive management takes several different models and uses different management manipulations to decide which model best describes how the system operates. Both approaches intend to reduce the uncertainty about how the system works so as to define the limits of management options.

The message was (as they argued) nothing more than common sense, to learn by doing. But common sense is uncommonly used, as we see too often even in the 21st century. Adaptive management became very popular in the 1990s, but while many took up the banner of adaptive management, relatively few cases have been successfully completed (Walters 2007; Westgate, Likens & Lindenmayer 2013). There are many different reasons for this (discussed well in these two papers), not the least of which is the communication gap between research scientists and resource managers. Research scientists typically wish to test an ecological hypothesis by a management manipulation, but the resource manager may not be able to use this particular management manipulation in practice because it costs too much. To be useful in the real world any management experiment needs to have careful, long-term monitoring to map its outcome, and management agencies do not often have the opportunity to carry out extensive monitoring. The underlying cause then is mainly financial, and resource agencies rarely have an adequate budget to cover the important wildlife and fisheries issues they are supposed to manage.

If anything, reading this ‘old’ literature should remind ecologists that the problems discussed are inherent in management and will not go away as we move into the era of climate change. Let me stop with a few of the guideposts from Holling’s book:

Treat assessment as an ongoing process…
Remember that uncertainties are inherent…
Involve decision makers early in the analysis…
Establish a degree of belief for each of your alternative models…
Avoid facile and narcotic compression of indicators such as cost/benefit ratios that are generally inappropriate for environmental problems….

And probably remind yourself that there can be wisdom in the elders….

The take-home message for me in re-reading these older papers on adaptive management is that it is similar to the problem we have with models in ecology. We can produce simple models or in this case solutions to management problems on paper, but getting them to work properly in the real world where social viewpoints, political power, and scientific information collide is extremely difficult. This is no reason to stop doing the best science and to try to weld it into management agencies. But it is easier said than done.

Holling, C.S. (1978) Adaptive Environmental Assessment and Management. John Wiley and Sons, Chichester, UK.

Walters, C.J. (2007) Is adaptive management helping to solve fisheries problems? Ambio, 36, 304-307.

Walters, C.J. & Hilborn, R. (1978) Ecological optimization and adaptive management. Annual Review of Ecology and Systematics, 9, 157-188.

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

On Repeatability in Ecology

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One of the elementary lessons of statistics is that every measurement must be repeatable so that differences or changes in some ecological variable can be interpreted with respect to some ecological or environmental mechanism. So if we count 40 elephants in one year and count 80 in the following year, we know that population abundance has changed and we do not have to consider the possibility that the repeatability of our counting method is so poor that 40 and 80 could refer to the same population size. Both precision and bias come into the discussion at this point. Much of the elaboration of ecological methods involves the attempt to improve the precision of methods such as those for estimating abundance or species richness. There is less discussion of the problem of bias.

The repeatability that is most crucial in forging a solid science is that associated with experiments. We should not simply do an important experiment in a single place and then assume the results apply world-wide. Of course we do this, but we should always remember that this is a gigantic leap of faith. Ecologists are often not willing to repeat critical experiments, in contrast to scientists in chemistry or molecular biology. Part of this reluctance is understandable because the costs associated with many important field experiments is large and funding committees must then judge whether to repeat the old or fund the new. But if we do not repeat the old, we never can discover the limits to our hypotheses or generalizations. Given a limited amount of money, experimental designs often limit the potential generality of the conclusions. Should you have 2 or 4 or 6 replicates? Should you have more replicates and fewer treatment sites or levels of manipulation? When we can, we try one way and then another to see if we get similar results.

A looming issue now is climate change which means that the ecosystem studied in 1980 is possibly rather different than the one you now study in 2014, or the place someone manipulated in 1970 is not the same community you manipulated this year. The worst case scenario would be to find out that you have to do the same experiment every ten years to check if the whole response system has changed. Impossible with current funding levels. How can we develop a robust set of generalizations or ‘theories’ in ecology if the world is changing so that the food webs we so carefully described have now broken down? I am not sure what the answers are to these difficult questions.

And then you pile evolution into this mix and wonder if organisms can change like Donelson et al.’s (2012) tropical reef fish, so that climate changes might be less significant than we currently think, at least for some species. The frustration that ecologists now face over these issues with respect to ecosystem management boils over in many verbal discussions like those on “novel ecosystems” (Hobbs et al. 2014, Aronson et al. 2014) that can be viewed as critical decisions about how to think about environmental change or a discussion about angels on pinheads.

Underlying all of this is the global issue of repeatability, and whether our current perceptions of how to manage ecosystems is sufficiently reliable to sidestep the adaptive management scenarios that seem so useful in theory (Conroy et al. 2011) but are at present rare in practice (Keith et al. 2011). The need for action in conservation biology seems to trump the need for repeatability to test the generalizations on which we base our management recommendations. This need is apparent in all our sciences that affect humans directly. In agriculture we release new varieties of crops with minimal long term studies of their effects on the ecosystem, or we introduce new methods such as no till agriculture without adequate studies of its impacts on soil structure and pest species. This kind of hubris does guarantee long term employment in mitigating adverse consequences, but is perhaps not an optimal way to proceed in environmental management. We cannot follow the Hippocratic Oath in applied ecology because all our management actions create winners and losers, and ‘harm’ then becomes an opinion about how we designate ‘winners’ and ‘losers’. Using social science is one way out of this dilemma, but history gives sparse support for the idea of ‘expert’ opinion for good environmental action.

Aronson, J., Murcia, C., Kattan, G.H., Moreno-Mateos, D., Dixon, K. & Simberloff, D. (2014) The road to confusion is paved with novel ecosystem labels: a reply to Hobbs et al. Trends in Ecology & Evolution, 29, 646-647.

Conroy, M.J., Runge, M.C., Nichols, J.D., Stodola, K.W. & Cooper, R.J. (2011) Conservation in the face of climate change: The roles of alternative models, monitoring, and adaptation in confronting and reducing uncertainty. Biological Conservation, 144, 1204-1213.

Donelson, J.M., Munday, P.L., McCormick, M.I. & Pitcher, C.R. (2012) Rapid transgenerational acclimation of a tropical reef fish to climate change. Nature Climate Change, 2, 30-32.

Hobbs, R.J., Higgs, E.S. & Harris, J.A. (2014) Novel ecosystems: concept or inconvenient reality? A response to Murcia et al. Trends in Ecology & Evolution, 29, 645-646.

Keith, D.A., Martin, T.G., McDonald-Madden, E. & Walters, C. (2011) Uncertainty and adaptive management for biodiversity conservation. Biological Conservation, 144, 1175-1178.

Is Ecology like Economics?

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One statement in Thomas Piketty’s book on economics struck me as a possible description of ecology’s development. On page 32 he states:

“To put it bluntly, the discipline of economics has yet to get over its childish passion for mathematics and for purely theoretical and often highly ideological speculation at the expense of historical research and collaboration with the other social sciences. Economists are all too often preoccupied with petty mathematical problems of interest only to themselves. This obsession with mathematics is an easy way of acquiring the appearance of scientificity without having to answer the far more complex questions posed by the world we live in.”

If this is at least a partially correct summary of ecology’s history, we could argue that finally in the last 20 years ecology has begun to analyze the far more complex questions posed by the ecological world. But it does so with a background of oversimplified models, whether verbal or mathematical, that we are continually trying to fit our data into. Square pegs into round holes.

Part of this problem arises from the hierarchy of science in which physics and in particular mathematics are ranked as the ideals of science to which we should all strive. It is another verbal model of the science world constructed after the fact with little attention to the details of how physics and the other hard sciences have actually progressed over the past three centuries.

Sciences also rank high in the public mind when they provide humans with more gadgets and better cars and airplanes, so that technology and science are always confused. Physics led to engineering which led to all our modern gadgets and progress. Biology has assisted medicine in continually improving human health, and natural history has enriched our lives by raising our appreciation of biodiversity. But ecology has provided a less clearly articulated vision for humans with a new list of commandments that seem to inhibit economic ‘progress’. Much of what we find in conservation biology and wildlife management simply states the obvious that humans have made a terrible mess of life on Earth – extinctions, overharvesting, pollution of lakes and the ocean, and invasive weeds among other things. In some sense ecologists are like the priests of old, warning us that God or some spiritual force will punish us if we violate some commandments or regulations. In our case it is the Earth that suffers from poorly thought out human alterations, and, in a nutshell, CO2 is the new god that will indeed guarantee that the end is near. No one really wants to hear or believe this, if we accept the polls taken in North America.

So the bottom line for ecologists should be to concentrate on the complex questions posed by the biological world, and try first to understand the problems and second to suggest some way to solve them. Much easier said than done, as we can see from the current economic mess in what might be a sister science.

Piketty, T. 2014. Capital in the Twenty-First Century. Belknap Press, Harvard University, Boston. 696 pp. ISBN 9780674430006

Back to p-Values

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Alas ecology has slipped lower on the totem-pole of serious sciences by an article that has captured the attention of the media:

Low-Décarie, E., Chivers, C., and Granados, M. 2014. Rising complexity and falling explanatory power in ecology. Frontiers in Ecology and the Environment 12(7): 412-418. doi: 10.1890/130230.

There is much that is positive in this paper, so you should read it if only to decide whether or not to use it in a graduate seminar in statistics or in ecology. Much of what is concluded is certainly true, that there are more p-values in papers now than there were some years ago. The question then comes down to what these kinds of statistics mean and how this would justify a conclusion captured by the media that explanatory power in ecology is declining over time, and the bottom line of what to do about falling p-values. Since as far as I can see most statisticians today seem to believe that p-values are meaningless (e.g. Ioannidis 2005), one wonders what the value of showing this trend is. A second item that most statisticians agree about is that R2 values are a poor measure of anything other than the items in a particular data set. Any ecological paper that contains data to be analysed and reported summarizes many tests providing p-values and R2 values of which only some are reported. It would be interesting to do a comparison with what is recognized as a mature science (like physics or genetics) by asking whether the past revolutions in understanding and prediction power in those sciences corresponded with increasing numbers of p-values or R2 values.

To ask these questions is to ask what is the metric of scientific progress? At the present time we confuse progress with some indicators that may have little to do with scientific advancement. As journal editors we race to increase their impact factor which is interpreted as a measure of importance. For appointments to university positions we ask how many citations a person has and how many papers they have produced. We confuse scientific value with some numbers which ironically might have a very low R2 value as predictors of potential progress in a science. These numbers make sense as metrics to tell publication houses how influential their journals are, or to tell Department Heads how fantastic their job choices are, but we fool ourselves if we accept them as indicators of value to science.

If you wish to judge scientific progress you might wish to look at books that have gathered together the most important papers of the time, and examine a sequence of these from the 1950s to the present time. What is striking is that papers that seemed critically important in the 1960s or 1970s are now thought to be concerned with relatively uninteresting side issues, and conversely papers that were ignored earlier are now thought to be critical to understanding. A list of these changes might be a useful accessory to anyone asking about how to judge importance or progress in a science.

A final comment would be to look at the reasons why a relatively mature science like geology has completely failed to be able to predict earthquakes in advance and even to specify the locations of some earthquakes (Steina et al. 2012; Uyeda 2013). Progress in understanding does not of necessity dictate progress in prediction. And we ought to be wary of confusing progress with p-and R2 values.

Ioannidis, J.P.A. 2005. Why most published research findings are false. PLoS Medicine 2(8): e124.

Steina, S., Gellerb, R.J., and Liuc, M. 2012. Why earthquake hazard maps often fail and what to do about it. Tectonophysics 562-563: 1-24. doi: 10.1016/j.tecto.2012.06.047.

Uyeda, S. 2013. On earthquake prediction in Japan. Proceedings of the Japan Academy, Series B 89(9): 391-400. doi: 10.2183/pjab.89.391.

The Snowshoe Hare 10-year Cycle – A Cautionary Tale

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We have been working on the ten-year cycle of snowshoe hares (Lepus americanus) in the southwest Yukon since 1975 trying to answer the simple question of what causes these cyclic fluctuations. I think that we now understand the causes of the cyclic dynamics, which is not to say all things are known but the broad picture is complete. But some misunderstanding persists, hence this one page summary. Some biology first.

The snowshoe hare cycle has been known from Canada lynx fur return data for more than 100 years, and of course known to First Nations people much before that. Hares are herbivores of small trees and shrubs, they reproduce at age 1 and rarely live more than 1-2 years. They have 2-4 litters in a summer, with litter size around 4-6. Juvenile losses are high and at best populations increase about three-to-four-fold per year. Almost everything eats them – lynx, coyotes, great-horned owls, goshawks, a long list of predators on the young. Reproduction collapses with rising density and females reduce their output from 4 litters to 2 in the peak and decline phase.

The obvious driving factors when Lloyd Keith and his students began working on the hare cycle in Alberta in the 1960s were winter food shortage and predation. When there is a high hare peak, damage to shrubs and small trees is obvious. But it was quite clear in Keith’s studies that the decline phase continued well after the vegetation recovered, and so he postulated a two-factor explanation, winter food shortage followed by high predation losses. He looked for disease and parasite problems in hares but found nothing.

Testing the winter food limitation would appear to be simple but is fraught with problems. Everyone believes that food is an ultimate limiting factor, so that it must be involved in the cyclic dynamics. We began testing food limitation in the mid-1970s and found that one could add natural food or artificial food (rabbit chow) and apparently have no effect on cyclic dynamics. Hares came to the food grids so the density increased by immigration, but the decline started at the same time and at the same rate as on control grids. So what is the role of food?

Our next attempt was to do a factorial experiment adding food, reducing predation, and doing both together. The details are important, replication was never enough for the manipulated treatments, we did it only for 10 years rather than 20 or 30. What we found was that there was an interaction between food addition and mammal predator exclusion so that the combined treatment increased to a much higher density than any single treatment. But this result came with a puzzle. What is the role of food? Hares showed no evidence of malnutrition in the peak or decline, fed hares did not increase their reproductive output. What produced the strong interaction between food addition and predator reduction?

The next breakthrough came when Rudy Boonstra suggested that predator-caused stress might underlie these strange dynamics. Because we could now measure stress with faecal cortisol measures we could test for stress directly in free-ranging hares. The surprise was that this idea worked and Michael Sheriff capped off the stress hypothesis by showing that not only does predator-induced stress reduce reproductive rates, but the stress effect is inherited maternally in the next generation.

The bottom line: the whole dynamics of the snowshoe hare cycle are predator-induced. All the changes in mortality and reproduction are direct and indirect effects of predators chasing and eating hares. The experimental food/predator interaction was mechanistically wrong in targeting food as a major limiting factor.

This of course does not mean that food is irrelevant as an important factor to study in hare cycles. In particular very high peak populations damage shrubs and small trees and we do not yet have the details of how this works out in time. Secondary chemicals are certainly involved here.

Why does all this matter? Two points. First, the hare cycle is often trumpeted as an example of a tri-trophic interaction of food – hares – predators, when in fact it seems to be a simple predator-prey system, as Lotka suggested in 1925. Models of the hare cycle have proliferated over time, and there are far more models of the cycle in existence than there are long-term field studies or field experiments. It is possible to model the hare cycle as a predator-prey oscillation, as a food plant-hare oscillation, as a parasite-hare interaction, as a cosmic particle – hare oscillation, as an intrinsic social – maternal effects interaction, and I have probably missed some other combinations of delayed-density dependent factors that have been discussed. That one can produce a formal mathematical model of the hare cycle does not mean that the chosen factor is the correct one.

The other point I would leave you with is the large amount of field work needed to sort out the mechanisms driving the population dynamics of hares. Ecology is not simple. This enigma of the ten-year cycle has always been a classic example in ecology and perhaps it is now solved. Or perhaps not?

Boonstra, R., D. Hik, G. R. Singleton, and A. Tinnikov. 1998. The impact of predator-induced stress on the snowshoe hare cycle. Ecological Monographs 68:371-394.

Boutin, S., C. J. Krebs, R. Boonstra, M. R. T. Dale, S. J. Hannon, K. Martin, A. R. E. Sinclair, J. N. M. Smith, R. Turkington, M. Blower, A. Byrom, F. I. Doyle, C. Doyle, D. Hik, L. Hofer, A. Hubbs, T. Karels, D. L. Murray, V. Nams, M. O’Donoghue, C. Rohner, and S. Schweiger. 1995. Population changes of the vertebrate community during a snowshoe hare cycle in Canada’s boreal forest. Oikos 74:69-80.

Keith, L. B., and L. A. Windberg. 1978. A demographic analysis of the snowshoe hare cycle. Wildlife Monographs 58:1-70.

Keith, L. B. 1990. Dynamics of snowshoe hare populations. Current Mammalogy 4:119-195.

Krebs, C. J., S. Boutin, R. Boonstra, A. R. E. Sinclair, J. N. M. Smith, M. R. T. Dale, K. Martin, and R. Turkington. 1995. Impact of food and predation on the snowshoe hare cycle. Science 269:1112-1115.

Krebs, C. J., S. Boutin, and R. Boonstra, editors. 2001. Ecosystem Dynamics of the Boreal Forest: the Kluane Project. Oxford University Press, New York.

Sheriff, M. J., C. J. Krebs, and R. Boonstra. 2009. The sensitive hare: sublethal effects of predator stress on reproduction in snowshoe hares. Journal of Animal Ecology 78:1249-1258.

Yan, C., N. C. Stenseth, C. J. Krebs, and Z. Zhang. 2013. Linking climate change to population cycles of hares and lynx. Global Change Biology 19:3263-3271.