Author Archives: Charles Krebs

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.

Is Conservation Ecology a Science?

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Now this is certainly a silly question. To be sure conservation ecologists collect much data, use rigorous statistical models, and do their best to achieve the general goal of protecting the Earth’s biodiversity, so clearly what they do must be the foundations of a science. But a look through some of the recent literature could give you second thoughts.

Consider for example – what are the hallmarks of science? Collecting data is one hallmark of science but is clearly not a distinguishing feature. Collecting data on the prices of breakfast cereals in several supermarkets may be useful for some purposes but it would not be confused with science. The newspapers are full of economic statistics about this and that and again no one would confuse that with science. We commonly remark that ‘this is a good scientific way to go about doing things” without thinking too much about what this means.

Back to basics. Science is a way of knowing, of accumulating knowledge to answer questions or problems in an independently verifiable way. Science deals with questions or problems that require some explanation, and the explanation is a hypothesis that needs to be tested. If the test is retrospective, the explanation may be useful for understanding the past. But science at its best is predictive about what will happen in the future, given a set of assumptions. And science always has alternative explanations or hypotheses in case the first one fails. So much everyone knows.

Conservation ecology is akin to history in having a great deal of information about the past but wishing to use that information to inform the future. In a certain sense it has a lot of the problems of history. History, according to many historians (Spinney 2012) is “just one damn thing after another”, so that there can be no science of history. But Turchin disagrees (2003, 2012) and claims that general laws can be recognized in history and general mathematical models developed. He predicts from these historical models that unrest will break out in the USA around 2020 as cycles of violence have broken out in the past every 30-50 years in this country (Spinney 2012). This is a testable prediction in a reasonable time frame.

If we look at the literature of conservation ecology and conservation genetics, we can find many observations of species declines, of geographical range shifts, and many predictions of general deterioration in the Earth’s biota. Virtually all of these predictions are not testable in any realistic time frame. We can extrapolate linear trends in population size to zero but there are so many assumptions that have to be incorporated to make these predictions, few would put money on them. For the most part the concern is rather to do something now to prevent these losses and that is very useful research. But since the major drivers of potential extinctions are habitat loss and climate change, two forces that conservation biologists have no direct control over, it is not at all clear how optimistic or pessimistic we should be when we see negative trends. Are we becoming biological historians?

There are unfortunately too few general ‘laws’ in conservation ecology to make specific predictions about the protection of biodiversity. Every one of the “ecological theory predicts…” statements I have seen in conservation papers refer to theory with so many exceptions that it ought not to be called theory at all. There are some certain predictions – if we eliminate all the habitat a species occupies, it will certainly go extinct. But exactly how much can we get rid of is an open question that there are no general rules about. “Protect genetic diversity” is another general rule of conservation biology, but the consequences of the loss of genetic diversity cannot be estimated except for controlled laboratory populations that bear little relationship to the real world.

The problems of conservation genetics are even more severe. I am amazed that conservation geneticists think they can decide what species are most ‘important’ for future evolution so that we should protect certain clades (Vane-Wright et al. 1991, Redding et al. 2014 and much additional literature). Again this is largely a guess based on so many assumptions that who knows what we would have chosen if we were in the time of the dinosaurs. The overarching problem of conservation biology is the temptation to play God. We should do this, we should do that. Who will be around to pick up the pieces when the assumptions are all wrong? Who should play God?

Redding, D.W., Mazel, F. & Mooers, A.Ø. (2014) Measuring evolutionary isolation for conservation. PLoS ONE, 9, e113490.

Spinney, L. (2012) History as science. Nature, 488, 24-26.

Turchin, P. (2003) Historical dynamics : why states rise and fall. Princeton University Press, Princeton, New Jersey.

Turchin, P. (2012) Dynamics of political instability in the United States, 1780–2010. Journal of Peace Research, 49, 577-591.

Vane-Wright, R.I., Humphries, C.J. & Williams, P.H. (1991) What to protect?—Systematics and the agony of choice. Biological Conservation, 55, 235-254.

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.

The Anatomy of an Ecological Controversy – Dingos and Conservation in Australia

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Conservation is a most contentious discipline, partly because it is ecology plus a moral stance. As such you might compare it to discussions about religious truths in the last several centuries but it is a discussion among scientists who accept the priority of scientific evidence. In Australia for the past few years there has been much discussion of the role of the dingo in protecting biodiversity via mesopredator release of foxes and cats (Allen et al. 2013; Colman et al. 2014; Hayward and Marlow 2014; Letnic et al. 2011, and many more papers). I do not propose here to declare a winner in this controversy but I want to dissect it as an example of an ecological issue with so many dimensions it could continue for a long time.

Dingos in Australia are viewed like wolves in North America – the ultimate enemy that must be reduced or eradicated if possible. When in doubt about what to do, killing dingos or wolves has become the first commandment of wildlife management and conservation. The ecologist would like to know, given this socially determined goal, what are the ecological consequences of reduction or eradication of dingos or wolves. How do we determine that?

The experimentalist suggests doing a removal experiment (or conversely a re-introduction experiment) so we have ecosystems with and without dingos (Newsome et al. 2015). This would have to be carried out on a large scale dependent on the home range size of the dingo and for a number of years so that the benefits or the costs of the removal would be clear. Here is the first hurdle, this kind of experiment cannot be done, and only a quasi-experiment is possible by finding areas that have dingos and others that do not have any (or a reduced population) and comparing ecosystems. This decision immediately introduces 5 problems:

  1. The areas with- and without- the dingo are not comparable in many respects. Areas with dingos for example may be national parks placed in the mountains or in areas that humans cannot use for agriculture, while areas with dingo control are in fertile agricultural landscapes with farming subsidies.
  2. Even given areas with and without dingos there is the problem of validating the usual dingo reduction carried out by poison baits or shooting. This is an important methodological issue.
  3. One has to census the mesopredators, in Australia foxes and cats, with further methodological issues of how to achieve that with accuracy.
  4. In addition one has to census the smaller vertebrates presumed to be possibly affected by the mesopredator offtake.
  5. Finally one has to do this for several years, possibly 5-10 years, particularly in variable environments, and in several pairs of areas chosen to represent the range of ecosystems of interest.

All in all this is a formidable research program, and one that has been carried out in part by the researchers working on dingos. And we owe them our congratulations for their hard work. The major part of the current controversy has been how one measures population abundance of all the species involved. The larger the organism, paradoxically the more difficult and expensive the methods of estimating abundance. Indirect measures, often from predator tracks in sand plots, are forced on researchers because of a lack of funding and the landscape scale of the problem. The essence of the problem is that tracks in sand or mud measure both abundance and activity. If movements increase in the breeding season, tracks may indicate activity more than abundance. If old roads are the main sampling sites, the measurements are not a random sample of the landscape.

This monumental sampling headache can be eliminated by the bold stroke of concluding with Nimmo et al. (2015) and Stephens et al. (2015) that indirect measures of abundance are sufficient for guiding actions in conservation management. They may be, they may not be, and we fall back into the ecological dilemma that different ecosystems may give different answers. And the background question is what level of accuracy do you need in your study? We are all in a hurry now and want action for conservation. If you need to know only whether you have “few” or “many” dingos or tigers in your area, indirect methods may well serve the purpose. We are rushing now into the “Era of the Camera” in wildlife management because the cost is low and the volume of data is large. Camera ecology may be sufficient for occupancy questions, but may not be enough for demographic analysis without detailed studies.

The moral issue that emerges from this particular dingo controversy is similar to the one that bedevils wolf control in North America and Eurasia – should we remove large predators from ecosystems? The ecologist’s job is to determine the biodiversity costs and benefits of such actions. But in the end we are moral beings as well as ecologists, and for the record, not the scientific record but the moral one, I think it is poor policy to remove dingos, wolves, and all large predators from ecosystems. Society however seems to disagree.

 

Allen, B.L., Allen, L.R., Engeman, R.M., and Leung, L.K.P. 2013. Intraguild relationships between sympatric predators exposed to lethal control: predator manipulation experiments. Frontiers in Zoology 10(39): 1-18. doi:10.1186/1742-9994-10-39.

Colman, N.J., Gordon, C.E., Crowther, M.S., and Letnic, M. 2014. Lethal control of an apex predator has unintended cascading effects on forest mammal assemblages. Proceedings of the Royal Society of London, Series B 281(1803): 20133094. doi:DOI: 10.1098/rspb.2013.3094.

Hayward, M.W., and Marlow, N. 2014. Will dingoes really conserve wildlife and can our methods tell? Journal of Applied Ecology 51(4): 835-838. doi:10.1111/1365-2664.12250.

Letnic, M., Greenville, A., Denny, E., Dickman, C.R., Tischler, M., Gordon, C., and Koch, F. 2011. Does a top predator suppress the abundance of an invasive mesopredator at a continental scale? Global Ecology and Biogeography 20(2): 343-353. doi:10.1111/j.1466-8238.2010.00600.x.

Newsome, T.M., et al. (2015) Resolving the value of the dingo in ecological restoration. Restoration Ecology, 23 (in press). doi: 10.1111/rec.12186

Nimmo, D.G., Watson, S.J., Forsyth, D.M., and Bradshaw, C.J.A. 2015. Dingoes can help conserve wildlife and our methods can tell. Journal of Applied Ecology 52. (in press, 27 Jan. 2015). doi:10.1111/1365-2664.12369.

Stephens, P.A., Pettorelli, N., Barlow, J., Whittingham, M.J., and Cadotte, M.W. 2015. Management by proxy? The use of indices in applied ecology. Journal of Applied Ecology 52(1): 1-6. doi:10.1111/1365-2664.12383.

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

Demography Made Simple

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I have grown weary of listening to radio and TV new announcers discuss the human population problem. I think a primer of a few principles of population arithmetic might be useful to remind us where we ecologists sit in these discussions. The problem centres on the issue of eternal growth and then the transition of any population from a growing one to a stable one. I concentrate here on human populations but the results apply to any long-lived species.

I list four empirical principles of demography.

  1. No population can continue growing without limit. This generalization is rock solid, so it would be good to keep mentioning it to sceptics of the following generalizations.
  2. Populations grow when births and immigration exceed deaths and emigration. If we consider the entire global human population, emigration and immigration disappear since we have not yet colonized space. Populations stabilize when births equal deaths.
  3. A population that moves from a growth phase to a stable phase must change in age structure. Every stable population must contain fewer young persons and more older persons.
  4. These changes in age structure have enormous implications for our requirements for hospitals, doctors, schools, teachers, and social support agencies. These changes are almost completely predicable for humans and should not come as a surprise to politicians.
  5. Pushing the panic button because a particular population like that of Japan is stabilizing and could even decline slightly may be useful for economists wishing for infinite growth but should be recognized as an expected event for every country in the future.

The bottom line is that we have the knowledge and the ability to plan for the cessation of human population growth. Many good books have been written to make these points and we need to keep repeating them. That many people do not understand the simple arithmetic of population change is a worry, and we should all try to communicate these 5 simple principles to all who will listen.

Cafaro, P., and Crist, E. 2012. Life on the Brink: Environmentalists Confront Overpopulation. University of Georgia Press, Athens, Georgia. 342 pp. ISBN: 978-0-8203-4385-3

Daly, H.E., and Farley, J. 2011. Ecological Economics: Principles and Applications. 2nd ed. Island Press, Washington, D.C. 509 pp. ISBN: 978-1-5972-6681-9

Washington, H. 2015. Demystifying Sustainability: Towards Real Solutions. Routledge, New York. 222 pp. ISBN: 978-1138812697

Why Do Physical Scientists Run Off with the Budget Pie?

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Take any developed country on Earth and analyse their science budget. Break it down into the amounts governments devote to physical science, biological science, and social science to keep the categories simple. You will find that the physical sciences gather the largest fraction of the budget-for-science pie, the biological sciences much less, and the social sciences even less. We can take Canada as an example. From the data released by the research councils, it is difficult to construct an exact comparison but within the Natural Sciences and Engineering Research Council of Canada the average research grant in Chemistry and Physics is 70% larger than the average in Ecology and Evolution, and this does not include supplementary funding for various infrastructure. By contrast the Social Sciences and Humanities Research Council reports research grants that appear to be approximately one-half those of Ecology and Evolution, on average. It seems clear in science in developed countries that the rank order is physical sciences > biological sciences > social sciences.

We might take two messages from this analysis. If you listen to the news or read the newspapers you will note that most of the problems discussed are social problems. Then you might wonder why social science funding is so low on our funding agenda in science. You might also note that environmental problems are growing in importance and yet funding for environmental research is also at the low end of our spending priority.

The second message you may wish to ask is: why should this be? In particular, why do physical scientists run off with the funding pie while ecologists and environmental scientists scratch through the crumbs? I do not know the answer to this question. I do know that it has been this way for at least the last 50 years, so it is not a recent trend. I can suggest several partial answers to this question.

  1. Physical scientists produce along with engineers the materials for war in splendid guns and aircraft and submarines that our governments believe will keep us safe.
  2. Physical scientists produce economic growth by their research so clearly they should be more important.
  3. Physical sciences produce scientific progress on a time scale of months while ecologists and environmental scientists produce research progress on a time scale of years and decades.
  4. Physical scientists do the research that produce good things like iPhones and computers while ecologists and environmental scientists produce mostly bad news about the deterioration in the earth’s ecosystem services.
  5. Physical scientists and engineers run the government and all the major corporations so they propagate the present system.

Clearly there are specific issues that are lost in this general analysis. Medical science produces progress in diagnosis and treatment as a result of the research of biochemists, molecular biologists, and engineers. Pharmaceutical companies produce compounds to control diseases with the help of molecular biologists and physiologists. So research in these specific areas must be supported well because they affect humans directly. Medical sciences are the recipient of much private money in the quest to avoid illness.

Lost in this are a whole other set of lessons. Why were multi-billions of dollars devoted to the Large Hadron Collider Project which had no practical value at all and has only led to the need for a Very Large Hadron Collider in future to waste even more money? The answer seems to lie somewhere in the interface of three points of view – it may be needed for military purposes, it is a technological marvel, and it is part of physics which is the only science that is important. The same kind of thinking seems to apply to space research which is wildly successful burning up large amounts of money while generating more military competition via satellites and in addition providing good movie images for the taxpayers.

While many people now support efforts on the conservation of biodiversity and the need for action on climate change, the funding is not given to achieve these goals either from public or private sources. One explanation is that these are long-term problems and so are difficult to get excited about when the lifespan of the people in power will not extend long enough to face the consequences of current decision making. Finally, many people are convinced that technological fixes will solve all environmental problems so that the problems environmental scientists worry about are trivial (National Research Council 2015, 2015a). Physics will fix climate change by putting chemicals into the stratosphere, endangered species will be resurrected by DNA, and fossil fuels will never run out. And as a bonus Canada and Scandinavia will be warmer and what is wrong with that?

An important adjunct to this discussion is the question of why economics has risen to the top of the heap along with physical sciences. As such the close triumvirate of physical sciences-engineering-economics seems to run the world. We should keep trying to change that if we have concern for the generations that follow.

 

National Research Council. 2015. Climate Intervention: Carbon Dioxide Removal and Reliable Sequestration. The National Academies Press, Washington, DC. 140 pp. ISBN: 978-0-309-36818-6.

National Research Council. 2015a. Climate Intervention: Reflecting Sunlight to Cool Earth. The National Academies Press, Washington, DC. 234 pp. ISBN: 978-0-309-36821-6.

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 Graphics in Ecological Presentations

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In the greater scheme of things, how you plot your data in a paper or in a PowerPoint presentation may not be the most important thing to worry about. But if you believe that small things matter, perhaps you should read on. The standard of presentation of data in graphs in ecological presentations is often less good than is desirable. Many authors have tried to help and for more instructions please read Cleveland (1993, 1994).

Begin with a few elementary rules that I should not have to state but are often ignored:

  1. Label the axes and give the units of measure
  2. Do not use a font size that requires a microscope to read.
  3. Do not present point data without some measure of possible error.

Beyond these general rules there are many that become more specific. I want to call attention here to two rules that are often violated even in our best ecological journals. The first and simplest is never to plot in logs. It is bad enough to plot an axis in log-10 units (most people can work out that 2 in log-10 means 100 in real units), but I have never met anyone who can decipher log-e units (what does 4.38 in log-e units mean in real units?). The solution is simple. Label the scales in real units so that for example the scale may read 1-10-100-1000 with equal spacing so the axis is scaled in logs but the units are given in real measurements. In this way the reader has some idea of the scale of changes shown on the graph.

The second and perhaps more controversial problem I find with ecological graphics is the use of histograms for data that should be illustrated as point estimates (with confidence limits). If we take the advice of Cleveland (1993, page 8) histograms would be rare in scientific publications:

“The histogram is a widely used graphical method that is at least a century old. But maturity and ubiquity do not guarantee the efficacy of a tool……The venerable histogram, an old favourite, but a weak competitor, will not be encountered again [in this book].” (Cleveland 1993, p. 8)

He goes on to evaluate a whole array of graphical methods most of which are rarely seen in ecological papers. The box plot is perhaps the most common example he recommends and is available in many graphing packages. But note that EXCEL is not a very good standard for graphics, and while some if its graphics might be useful, caution is recommended. Many graphics options are available in R (http://www.r-project.org/ ) and some in SIGMAPLOT. Discussions about graphics packages on the web are extensive and everyone has their favourite package along with complaints about other packages. The general point is to think carefully about the graphics you use to convey your message to make it as clear as possible.

What exactly is wrong with histograms? They are misleading if the scale of the axis does not start at zero. The width of the bars is misleading if the scales are categories or precise values. The information in each histogram bar is entirely concentrated in the top of the bar and the included error bars. The amount of replication is difficult to evaluate, and distributions of data that are skewed are not presented. Finally, outliers are not identified. Perhaps the message is that if you have data that you think should be presented as a histogram, check Cleveland (1994) to see if there is not a better way to present it to your audience.

A final observation on graphics. I realize that at the present time in movies and games 3-D images and animations are quite incredible. But remember these are for entertainment not for communication. If you think your PowerPoint requires 3-D graphs with animations, be sure to check whether you are aiming more for entertainment than clear communication.

Cleveland, W.S. 1993. Visualizing Data. Hobart Press, Summit, New Jersey.

Cleveland, W.S. 1994. The Elements of Graphing Data. AT&T Bell Laboratories, Murray Hill, New Jersey.