Author Archives: Charles Krebs

University Conundrums

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Universities in Canada and the United States and probably in Australia as well are bedeviled by not knowing what they should be doing. In general, they all want to be ‘excellent’ but this is largely an advertising gimmick unless one wishes to be more specific about excellent in what? Excellent in French literature? Probably not. Excellent in the engineering that facilitates the military-industrial complex? Probably yes, but with little thought of the consequences for universities or for Planet Earth (Smart 2016). Excellence in medicine? Certainly, yes. But much of the advertisement about excellence is self aggrandisement, and one can only hope that underneath the adverts there is some good planning and thinking of what a university should be (Lanahan et al. 2016).

There are serious problems in the world today and the question is what should the universities be doing about these long-term, difficult problems. There are two polar views on this question. At one extreme, universities can say it is our mandate to educate students and not our mandate to solve environmental or social problems. At the other extreme, universities can devote their resources to solving problems, and thereby educate students in problem analysis and problem solving. But these universities will not be very popular since for any serious issue like climate change, many voters are at odds over what can and should be done, Governments do not like universities that produce scholarship that challenges their policies. So we must always remember the golden rule – “she that has the gold, makes the rules”.

But there are constraints no matter what policies a university adopts, and there is an extensive literature on these constraints. I want to focus on one overarching constraint for biodiversity research in universities – graduate students have a very short time to complete their degrees. Given a 2-year or 3-year time horizon, the students must focus on a short-term issue with a very narrow focus. This is good for the students and cannot be changed. But it is potentially lethal for ecological studies that are long-term and do not fit into the demands of thesis writing. A basic assumption I make is that the most important ecological issues of our day are long-term problems, at least in the 20-year time frame and more likely in the 50 to 100-year time frame. The solution most prevalent in the ecology literature now is to use short term data to produce a model to extrapolate short term data into the indefinite future by use of a climate model or any other model that will allow extrapolation. The result of this conundrum is that the literature is full of studies making claims about ecological processes that are based on completely inadequate time frames (Morrison 2012). If this is correct, at least we ought to have the humility to point out the potential errors of extrapolation into the future. We make a joke about this situation in our comical advice to graduate students: “If you get an exciting result from your thesis research in year 1, stop and do no more work and write your thesis lest you get a different result if you continue in year 2.”

The best solution for graduate students is to work within a long-term project, so that your 2-3 years of work can build on past progress. But long-term projects are difficult to carry forward in universities now because research money is in short supply (Rivero and Villasante 2016). University faculty can piggy-back on to government studies that are well funded and long-term, but again this is not always possible. Conservation ecology is not often well funded by governments either, so we keep passing the buck. Collaboration here between governments and universities is essential, but is not always strong at the level of individual projects. Some long-term ecological studies are led by federal and regional government research departments directly, but more seem to be led by university faculty. And the limiting resource is typically money. There are a set of long-term problems in ecology that are ignored by governments for ideological reasons. Some politicians work hard to avoid the many ecological problems that are ‘hot potatoes’ and are best left unstudied. Any competent ecologist can list for you 5 or more long-term issues in conservation biology that are not being addressed now for lack of money. I doubt that ideas are the limiting resource in ecology, as compared with funding.

And this leads us back in a circle to the universities quest for ‘excellence’. Much here depends on the wisdom of the university’s leaders and the controls on university funding provided by governments for research. In Canada for example, funding constraints for research excellence exist based on university size (Murray et al. 2016). How then can we link the universities’ quest for excellence to the provision of adequate funding for long-term ecological issues? As one recommendation to the directors of funding programs within the universities, I suggest listing the major problems of your area and of the world at large, and then fund the research within your jurisdiction by how well the proposed research matches the major problems we face today.

Lanahan, L., Graddy-Reed, A. & Feldman, M.P. (2016) The Domino Effects of Federal Research Funding. PLoS ONE, 11, e0157325. doi: 10.1371/journal.pone.0157325

Morrison, M.L. (2012) The habitat sampling and analysis paradigm has limited value in animal conservation: A prequel. Journal of Wildlife Management, 76, 438-450. doi: 10.1002/jwmg.333

Murray, D.L., Morris, D., Lavoie, C., Leavitt, P.R. & MacIsaac, H. (2016) Bias in research grant evaluation has dire consequences for small universities. PLoS ONE, 11, e0155876.doi: 10.1371/journal.pone.0155876

Rivero, S. & Villasante, S. (2016) What are the research priorities for marine ecosystem services? Marine policy, 66, 104-113. doi: 10.1016/j.marpol.2016.01.020

Smart, B. (2016) Military-industrial complexities, university research and neoliberal economy. Journal of Sociology, 52, 455-481. doi: 10.1177/1440783316654258

Biodiversity Conundrums

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Conservation ecologists face a conundrum, as many have pointed out before. As scientists we do not make policy. Most conservation problems are essentially a moral issue of dealing with conflicts in goals and allowable actions. Both the United States and Canada have endangered species legislation in which action plans are written for species of concern. In the USA species of concern are allotted some funding and more legal protection than in Canada, where much good material is written but funding for action or research is typically absent. What is interesting from an ecological perspective is the list of species that are designated as endangered or threatened. Most of them can be described colloquially as the “charismatic megafauna”, species that are either large or beautiful or both. There are exceptions of course for some amphibians and rare plants, but by and large the list of species of concern is a completely non-random collection of organisms that people see in their environment. Birds and butterflies and large mammals are at the head of the list.

All of this is fine and useful because it is largely political ecology, but it raises the question of what will happen should these rescue plans for threatened or endangered species fail. This question lands ecologists in a rather murky area of ecosystem function, which leads to the key question: how is ecosystem function affected by the loss of species X? The answer to this question depends very much on how you define ecosystem function. If species X is a plant and the ecosystem function measured is the uptake of CO2 by the plant community, the answer could be a loss of function, no change, or indeed an increase in CO2 uptake if species X for example is replaced by a weed that is more productive that species X. The answer to this simple question is thus very complicated and requires much research. For a hypothetical example, plant X may be replaced by a weed that fixes more CO2, and thus ecosystem function is improved as measured by carbon uptake from the atmosphere. But the weed may deplete soil nitrogen which could adversely affect other plants and soil quality. Again more data are needed to decide this. If the effect size is small, much research could provide an ambiguous answer to the original question, since all measurement involves errors.

So now we are in a box, a biodiversity conundrum. The simplest escape is to say that all species loss is undesirable in any ecosystem, a pontification that is more political than scientific. And, for a contrary view, if the species lost is a disease organism, or an insect that spreads human diseases, we will not mourn its passing. In practice we seem to agree with the public that the species under concern are not all of equal value for conservation. The most serious outcome of this consideration is that where the money goes for conservation is highly idiosyncratic. There are two major calls for funding that perhaps should not be questioned: first, for land (and water) acquisition and protection, and second, for providing compensation for the people whose livelihoods are affected by protected areas with jobs and skills that improve their lives. The remaining funds need to be used for scientific research that will further the cause of conservation in the broad sense. The most useful principle at this stage is that all research has a clear objective and a clear list of what outcomes can be used to judge its success. For conservation outcomes this judgement should be clear cut. Currently they are not.

When Caughley (1994) described the declining population paradigm and the small population paradigm he clearly felt that the small population paradigm, while theoretically interesting, had little to contribute to most of the real world problems of biodiversity conservation. He could not have imagined at the time how genetics would develop into a powerful set of methods of analysis of genomes. But with a few exceptions the small population paradigm and all the elegant genetic work that has sprung from it has delivered a mountain of descriptive information with only a molehill of useful management options for real world problems. Many will disagree with my conclusion, and it is clear that conservation genetics is a major growth industry. That is all well and good but my question remains as to its influence on the solution of current conservation problems (Caro 2008; Hutchings 2015; Mattsson et al. 2008). Conservation genetic papers predicting extinctions in 100 years or more based on low levels of genetic variation are not scientifically testable and rely on a law of conservation genetics that is riddled with exceptions (Nathan et al. 2015; Robinson et al. 2016). Do we need more untestable hypotheses in conservation biology?

Caro, T. 2008. Decline of large mammals in the Katavi-Rukwa ecosystem of western Tanzania. African Zoology 43(1): 99-116. doi:10.3377/1562-7020(2008)43[99:dolmit]2.0.co;2.

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

Hutchings, J.A. 2015. Thresholds for impaired species recovery. Proceedings of the Royal Society. B, Biological sciences 282(1809): 20150654. doi:10.1098/rspb.2015.0654.

Mattsson, B.J., Mordecai, R.S., Conroy, M.J., Peterson, J.T., Cooper, R.J., and Christensen, H. 2008. Evaluating the small population paradigm for rare large-bodied woodpeckers, with Implications for the Ivory-billed Woodpecker. Avian Conservation and Ecology 3(2): 5. http://www.ace-eco.org/vol3/iss2/art5/

Nathan, H.W., Clout, M.N., MacKay, J.W.B., Murphy, E.C., and Russell, J.C. 2015. Experimental island invasion of house mice. Population Ecology 57(2): 363-371. doi:10.1007/s10144-015-0477-2.

Robinson, J.A., Ortega-Del Vecchyo, D., Fan, Z., Kim, B.Y., and vonHoldt, B.M. 2016. Genomic flatlining in the endangered Island Fox. Current Biology 26(9): 1183-1189. doi:10.1016/j.cub.2016.02.062.

What Can Ecologists Do?

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For about 40 years many ecologists as well as other scientists have reported on the consequences of climate change. In recent years there has been more and more public awareness of the problems associated with changing climate. But there it all seems to stop. Jobs and dollars trump everything in the western world. I sit today listening to the Federal Government in Canada approving a very large export agreement for liquefied natural gas (LNG) on the central west coast of British Columbia. The gas will be largely obtained by fracking and in spite of the fact that the shipping point is near the mouth of one of the largest salmon rivers on the west coast, and requires a long pipeline to deliver the gas with all its problems, the report of the government states that this development will have no harmful effects on the environment. The perception that burning natural gas is somehow good for the environment boggles my mind. You have heard all of this kind of discussion many times before I am sure.

Yet as far as we can tell these are not evil people who are approving these developments but their decisions are so far away from scientific reality that one can only wonder what drives this current economic system. There are several competing hypotheses. (1) Climate change is not a problem and is not caused by human actions releasing greenhouse gases. This is not believable if scientific evidence is given any credibility. So we need a better excuse for our current myopia. (2) The problems of climate change are so uncertain and far into the distant future so that it is not our job to be concerned about action now. (3) We should take action now but if we do it will disrupt the global economy too much to contemplate. Taxes will have to increase. (4) Much money can be made by these enterprises and this will allow western countries to develop technologies that will remove carbon from the atmosphere, so all will be well in the future. (5) A price can be set on carbon so that business as usual under a carbon price will take care of the problem. The market will take care of us.

Take your pick on these last 4 excuses, but as an ecologist I cannot buy any of them. Clearly I am not a social scientist or an economist, and consequently have little understanding of how all of this proceeds and how the continued nonsense of business as usual is reported on much of the media as though this is the only way forward. The disconnect between what the educated public believes and what the government and business economists push has never been more serious. Perhaps the dominant view of many people is that we have always managed to muddle through in the past, and so this is a minor issue that we will overcome as usual by some kind of technological fix. And it is a long term problem, and I will not be here in the long term.

What can we ecologists do? Teach, report, communicate to the wider public via social media or traditional media, and hope that progress in understanding will finally take hold. Set an example, and hope that we can turn this juggernaut around. David Suzuki and Bill McKibben and many others are doing this. As an army dedicated to peace we can move forward and hope for wisdom to prevail.

Ehrlich, P.R., and Ehrlich, A.H. 2013. Can a collapse of global civilization be avoided? Proceedings of the Royal Society B: Biological Sciences 280(1754): 20122845. doi: 10.1098/rspb.2012.2845.

Ehrlich, P.R., and Ehrlich, A.H. 2013. Future collapse: how optimistic should we be? Proceedings of the Royal Society B: Biological Sciences 280(1767): 20131373. doi: 10.1098/rspb.2013.1373.

Kelly, M.J. 2013. Why a collapse of global civilization will be avoided: a comment on Ehrlich & Ehrlich. Proceedings of the Royal Society B: Biological Sciences 280(1767). doi: 10.1098/rspb.2013.1193.

McKibben, B. 2013. Oil and Honey: The Education of an Unlikely Activist. Henry Holt and Company, New York. 257 pp.  ISBN: 978-08050-9284-4

A Modest Proposal for a New Ecology Journal

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I read the occasional ecology paper and ask myself how this particular paper ever got published when it is full of elementary mistakes and shows no understanding of the literature. But alas we can rarely do anything about this as individuals. If you object to what a particular paper has concluded because of its methods or analysis, it is usually impossible to submit a critique that the relevant journal will publish. After all, which editor would like to admit that he or she let a hopeless paper through the publication screen. There are some exceptions to this rule, and I list two examples below in the papers by Barraquand (2014) and Clarke (2014). But if you search the Web of Science you will find few such critiques for published ecology papers.

One solution jumped to mind for this dilemma: start a new ecology journal perhaps entitled Misleading Ecology Papers: Critical Commentary Unfurled. Papers submitted to this new journal would be restricted to a total of 5 pages and 10 references, and all polemics and personal attacks would be forbidden. The key for submissions would be to state a critique succinctly, and suggest a better way to construct the experiment or study, a new method of analysis that is more rigorous, or key papers that were missed because they were published before 2000. These rules would potentially leave a large gap for some very poor papers to avoid criticism, papers that would require a critique longer than the original paper. Perhaps one very long critique could be distinguished as a Review of the Year paper. Alternatively, some long critiques could be published in book form (Peters 1991), and not require this new journal. The Editor of the journal would require all critiques to be signed by the authors, but would permit in exceptional circumstances to have the authors be anonymous to prevent job losses or in more extreme cases execution by the Mafia. Critiques of earlier critiques would be permitted in the new journal, but an infinite regress will be discouraged. Book reviews could be the subject of a critique, and the great shortage of critical book reviews in the current publication blitz is another aspect of ecological science that is largely missing in the current journals. This new journal would of course be electronic, so there would be no page charges, and all articles would be open access. All the major bibliographic databases like the Web of Science would be encouraged to catalog the publications, and a doi: would be assigned to each paper from CrossRef.

If this new journal became highly successful, it would no doubt be purchased by Wiley-Blackwell or Springer for several million dollars, and if this occurred, the profits would accrue proportionally to all the authors who had published papers to make this journal popular. The sale of course would be contingent on the purchaser guaranteeing not to cancel the entire journal to prevent any criticism of their own published papers.

At the moment criticism of ecological science does not occur for several years after a poor paper is published and by that time the Donald Rumsfeld Effect would have occurred to apply the concept of truth to the conclusions of this poor work. For one example, most of the papers critiqued by Clarke (2014) were more than 10 years old. By making the feedback loop much tighter, certainly within one year of a poor paper appearing, budding ecologists could be intercepted before being led off course.

This journal would not be popular with everyone. Older ecologists often strive mightily to prevent any criticism of their prior conclusions, and some young ecologists make their career by pointing out how misleading some of the papers of the older generation are. This new journal would assist in creating a more egalitarian ecological world by producing humility in older ecologists and more feelings of achievements in young ecologists who must build up their status in the science. Finally, the new journal would be a focal point for graduate seminars in ecology by bringing together and identifying the worst of the current crop of poor papers in ecology. Progress would be achieved.

 

Barraquand, F. 2014. Functional responses and predator–prey models: a critique of ratio dependence. Theoretical Ecology 7(1): 3-20. doi: 10.1007/s12080-013-0201-9.

Clarke, P.J. 2014. Seeking global generality: a critique for mangrove modellers. Marine and Freshwater Research 65(10): 930-933. doi: 10.1071/MF13326.

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

 

Climate Change and Ecological Science

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One dominant paradigm of the ecological literature at the present time is what I would like to call the Climate Change Paradigm. Stated in its clearest form, it states that all temporal ecological changes now observed are explicable by climate change. The test of this hypothesis is typically a correlation between some event like a population decline, an invasion of a new species into a community, or the outbreak of a pest species and some measure of climate. Given clever statistics and sufficient searching of many climatic measurements with and without time lags, these correlations are often sanctified by p< 0.05. Should we consider this progress in ecological understanding?

An early confusion in relating climate fluctuations to population changes was begun by labelling climate as a density independent factor within the density-dependent model of population dynamics. Fortunately, this massive confusion was sorted out by Enright (1976) but alas I still see this error repeated in recent papers about population changes. I think that much of the early confusion of climatic impacts on populations was due to this classifying all climatic impacts as density-independent factors.

One’s first response perhaps might be that indeed many of the changes we see in populations and communities are indeed related to climate change. But the key here is to validate this conclusion, and to do this we need to talk about the mechanisms by which climate change is acting on our particular species or species group. The search for these mechanisms is much more difficult than the demonstration of a correlation. To become more convincing one might predict that the observed correlation will continue for the next 5 (10, 20?) years and then gather the data to validate the correlation. Many of these published correlations are so weak as to preclude any possibility of validation in the lifetime of a research scientist. So the gold standard must be the deciphering of the mechanisms involved.

And a major concern is that many of the validations of the climate change paradigm on short time scales are likely to be spurious correlations. Those who need a good laugh over the issue of spurious correlation should look at Vigen (2015), a book which illustrates all too well the fun of looking for silly correlations. Climate is a very complex variable and a nearly infinite number of measurements can be concocted with temperature (mean, minimum, maximum), rainfall, snowfall, or wind, analyzed over any number of time periods throughout the year. We are always warned about data dredging, but it is often difficult to know exactly what authors of any particular paper have done. The most extreme examples are possible to spot, and my favorite is this quotation from a paper a few years ago:

“A total of 864 correlations in 72 calendar weather periods were examined; 71 (eight percent) were significant at the p< 0.05 level. …There were 12 negative correlations, p< 0.05, between the number of days with (precipitation) and (a demographic measure). A total of 45- positive correlations, p<0.05, between temperatures and (the same demographic measure) were disclosed…..”

The climate change paradigm is well established in biogeography and the major shifts in vegetation that have occurred in geological time are well correlated with climatic changes. But it is a large leap of faith to scale this well established framework down to the local scale of space and a short-term time scale. There is no question that local short term climate changes can explain many changes in populations and communities, but any analysis of these kinds of effects must consider alternative hypotheses and mechanisms of change. Berteaux et al. (2006) pointed out the differences between forecasting and prediction in climate models. We desire predictive models if we are to improve ecological understanding, and Berteaux et al. (2006) suggested that predictive models are successful if they follow three rules:

(1) Initial conditions of the system are well described (inherent noise is small);

(2) No important variable is excluded from the model (boundary conditions are defined adequately);

(3) Variables used to build the model are related to each other in the proper way (aggregation/representation is adequate).

Like most rules for models, whether these conditions are met is rarely known when the model is published, and we need subsequent data from the real world to see if the predictions are correct.

I am much less convinced that forecasting models are useful in climate research. Forecasting models describe an ecological situation based on correlations among the measurements available with no clear mechanistic model of the ecological interactions involved. My concern was highlighted in a paper by Myers (1998) who investigated for fish populations the success of published juvenile recruitment-environmental factor (typically temperature) correlations and found that very few forecasting models were reliable when tested against additional data obtained after publication. It would be useful for someone to carry out a similar analysis for bird and mammal population models.

Small mammals show some promise for predictive models in some ecosystems. The analysis by Kausrud et al. (2008) illustrates a good approach to incorporating climate into predictive explanations of population change in Norwegian lemmings that involve interactions between climate and predation. The best approach in developing these kinds of explanations and formulating them into models is to determine how the model performs when additional data are obtained in the years to follow publication.

The bottom line is to avoid spurious climatic correlations by describing and evaluating mechanistic models that are based on observable biological factors. And then make predictions that can be tested in a realistic time frame. If we cannot do this, we risk publishing fairy tales rather than science.

Berteaux, D., et al. (2006) Constraints to projecting the effects of climate change on mammals. Climate Research, 32, 151-158. doi: 10.3354/cr032151

Enright, J. T. (1976) Climate and population regulation: the biogeographer’s dilemma. Oecologia, 24, 295-310.

Kausrud, K. L., et al. (2008) Linking climate change to lemming cycles. Nature, 456, 93-97. doi: 10.1038/nature07442

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

Vigen, T. (2015) Spurious Correlations, Hyperion, New York City. ISBN: 978-031-633-9438

On Indices of Population Abundance

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A discussion with Murray Efford last week stimulated me to raise again this issue of using indices to measure population changes. One could argue that this issue has already been fully aired by Anderson (2003) and Engemann (2003) and I discussed it briefly in a blog about 2 years ago. The general agreement appears to be that mark-recapture estimation of population size is highly desirable if the capture procedure is clearly understood in relation to the assumption of the model of estimation. McKelvey and Pearson (2001) made this point with some elegant simulations. The best procedure then, if one wishes to replace mark-recapture methods with some index of abundance (track counts, songs, fecal pellets, etc.), is to calibrate the index with absolute abundance information of some type and show that the index and absolute abundance are very highly correlated. This calibration is difficult because there are few natural populations on which we know absolute abundance with high accuracy. We are left hanging with no clear path forward, particularly for monitoring programs that have little time or money to do extensive counting of any one species.

McKelvey and Pearson (2001) laid out a good guide for the use of indices in small mammal trapping, and showed that for many sampling programs the use of the number of unique individuals caught in a sampling session was a good index of population abundance, even though it is negatively biased. The key variable in all these discussions of mark-recapture models is the probability of capture of an individual animal living on the trapping area per session. Many years ago Leslie et al. (1953) considered this issue and the practical result was the recommendation that all subsequent work with small rodents should aim for a maximum probability of capture of individuals. The simplest way to do this was with highly efficient traps and large numbers of traps (single catch traps) so that there was always an excess of traps available for the population being censused. Krebs and Boonstra (1984) presented an analysis of trappability for several Microtus populations in which these recommendations were typically followed (Longworth traps in excess), and they found that the average per session detection probability ranged from about 0.6 to 0.9 for the four Microtus species studied. In all these studies live traps were present year round in the field, locked open when not in use, so the traps became part of the local environment for the voles. Clean live traps were much less likely to catch Microtus townsendii than dirty traps soiled with urine and feces (Boonstra and Krebs 1976). It is clear that minor behavioural quirks of the species under study may have significant effects on the capture data obtained. Individual heterogeneity in the probability of capture is a major problem in all mark-recapture work. But in the end natural history is as important as statistics.

There are at least two take home messages that can come from all these considerations. First, there are many statistical decisions that have to be made before population size can be estimated from mark-recapture data or any kind of quadrat based data. Second, there is also much biological information that must be well known before starting out with some kind of sampling design. Detectability may vary greatly with observers, with types of traps used, and observer skills so that again the devil is in the details. A third take home message given to me by someone who must remain nameless is that mark-recapture is hopeless as an ecological method because even after much work, the elusive population size that one wishes to know is lost in a pile of assumptions. But we cannot accept such a negative view without trying very hard to overcome the problems of sampling and estimation.

One way out of the box we find ourselves in (if we want to estimate population size) is to use an index of abundance and recognize its limitations. We cannot use quantitative population modelling on indices but we may find that indices are the best we can do for now. In particular, monitoring with little money must rely on indices of many populations of both plants and animals. Some data are better than no data for the management of populations and communities.

For the present time spatially explicit capture-recapture (SECR) methods of population estimation have provided a most useful approach to estimating density (Efford et al. 2009, 2013) and much future work will be needed to tell us how useful this relatively new approach is for accurately estimating population density (Broekhuis and Gopalaswamy 2016).

And a final reminder that even if you study community or ecosystem ecology, you must rely on getting measures of abundance for many quantitative models of system performance. So methods that provide accuracy for population sizes are just as essential for the vast array of ecological studies.

Anderson, D.R. 2003. Index values rarely constitute reliable information. Wildlife Society Bulletin 31(1): 288-291.

Boonstra, R. and Krebs, C.J. 1976. The effect of odour on trap response in Microtus townsendii. Journal of Zoology (London) 180(4): 467-476. Doi: 10.1111/j.1469-7998.1976.tb04692.x.

Broekhuis, F. and Gopalaswamy, A.M. 2016. Counting cats: Spatially explicit population estimates of cheetah (Acinonyx jubatus) using unstructured sampling data. PLoS ONE 11(5): e0153875. Doi: 10.1371/journal.pone.0153875.

Efford, M.G. and Fewster, R.M. 2013. Estimating population size by spatially explicit capture–recapture. Oikos 122(6): 918-928. Doi: 10.1111/j.1600-0706.2012.20440.x.

Efford, M.G., Dawson, D.K., and Borchers, D.L. 2009. Population density estimated from locations of individuals on a passive detector array. Ecology 90(10): 2676-2682. Doi: 10.1890/08-1735.1

Engeman, R.M. 2003. More on the need to get the basics right: population indices. Wildlife Society Bulletin 31(1): 286-287.

Krebs, C.J. and Boonstra, R. 1984. Trappability estimates for mark-recapture data. Canadian Journal of Zoology 62 (12): 2440-2444. Doi: 10.1139/z84-360

Leslie, P.H., Chitty, D., and Chitty, H. 1953. The estimation of population parameters from data obtained by means of the capture-recapture method. III. An example of the practical applications of the method. Biometrika 40 (1-2): 137-169. Doi:10.1093/biomet/40.1-2.137

McKelvey, K.S. & Pearson, D.E. (2001) Population estimation with sparse data: the role of estimators versus indices revisited. Canadian Journal of Zoology, 79(10): 1754-1765. Doi: 10.1139/cjz-79-10-1754

Does Forestry Make Money – Part 2

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About 2 years ago I wrote a blog asking the simple question of whether the forest industry in British Columbia makes money or whether it is operational only because of subsidies and the failure to recognize that biodiversity and ecosystem services could be valuable. A recent report from the research group in the Fenner School of the Australian National University has put the spotlight on the mountain ash forests of the Central Highlands of Victoria to answer this question for one region of southern Australia. I summarize their findings from their report (Keith et al. 2016) that you can access from the web address given below.

The ANU research group chose the Central Highlands study area because it included areas with controversial land use activities. The study area of 7370 sq km contains a range of landscapes including human settlements, agricultural land, forests, and waterways, and is used for a variety of activities including timber production, agriculture, water supply and recreation. It is also home to a range of species, including the endemic and critically endangered Leadbeater’s Possum. These activities and their use of ecosystems can be either complementary or conflicting. Managing the various activities within the region is therefore complex and requires evaluation of the trade-offs between different land uses and users, an issue common to forestry areas around the world.

The accounting structure (System of Environmental-Economic Accounting) which is used by the United Nations is described in more detail in the report. Both economic and ecological data are needed to produce ecosystem accounts and these sources of data must be integrated to gain an overall picture of the system. This integration of ecosystem services with traditional cash crops is the key to evaluating an area for all of its values to humans. In this particular area the provisioning of water to cities is a key economic benefit provided by this particular area. The following table from their report puts all these accounts together for the Central Highlands of Victoria:

Table 5. Economic information for industries within the study region in 2013-14
Agriculture Native Forestry Water supply Tourism
Area of land used (ha) 96,041a 324,380b 115,149c 737,072d
Sale of products ($m) 474 49 911 485
Industry valued added ($m) 257 9 233 260
Ecosystem services ($m) 121 15 101 42
Sale of products ($ ha-1) 4918 151 7911 659
Industry value added ($ ha-1) 2667 29 2023 353
Ecosystem services ($ ha-1) 1255 46 877 57

a area of agricultural land use
b area of native forest timber production
c area of water catchments
d total area of study region

The key point in this table is that the value-added per ha of forestry is $29 per ha per year. The equivalent value for water is $2033 per ha per year – or 70 times more, and the value added for agriculture is about 90 time more than that of forestry. The value-added value for tourism is $350 per ha per year, about 12 times more than that of forestry. None of this takes into account any potential government subsidies to these industries, and none involves directly the endangered species in the landscape. Three main points emerge from this analysis:

  1. In 2013-14, the most valuable industries in the region were tourism ($260 million), agriculture ($257 million), water supply ($233 million) and forestry ($9 million). This is as measured by the estimated industry value added (the contribution to GDP).
  2. In 2013-14, the most valuable ecosystem services in the region were food provisioning ($121 million), water provisioning ($101 million), cultural and recreation services ($42 million).
  3. At a carbon price of $12.25 per ton (the average price paid by the Commonwealth in 2015), the potential ecosystem service of carbon sequestration ($20 million) was more valuable than the service of timber provisioning ($15 million).

The main implications from the report for this large geographical area are three:

  • The benefits from tourism, agriculture, and water supply are large, while those from forestry are comparatively small. There is a potential for income from carbon sequestration.
  • The activities of tourism, agricultural and water supply industries are complimentary and may be combined with biodiversity conservation and carbon sequestration.
  • Timber harvesting in native forests needs to better account for the occurrence of fires and can be incompatible with species requirements for conservation.

The recent global interest in both climate change and species conservation has pushed this type of analysis to uncover the complementary and conflicting activities of all major global industries. Replacing the conventional GDP of a country or a region with a measure that takes into account the changes in the natural capital including gains and losses is a necessary step for sustainability (Dasgupta 2015, Guerry et al. 2015). This report from Australia shows how this goal of replacing the current GDP calculation with a green GDP can be done in specific areas. Much of biodiversity conservation hinges on these developments.

Dasgupta, P. 2015. Disregarded capitals: what national accounting ignores. Accounting and Business Research 45(4): 447-464. doi: 10.1080/00014788.2015.1033851.

Guerry, A.D., et al. 2015. Natural capital and ecosystem services informing decisions: From promise to practice. Proceedings of the National Academy of Sciences 112(24): 7348-7355. doi: 10.1073/pnas.1503751112.

Keith, H., Vardon, M., Stein, J., Stein, J., and Lindenmayer, D. 2016. Exzperimental Ecosystem Accounts for the Central Highlands of Victoria. Australian National University, Fenner School of Environment and Society. 22 pp. Available from:
http://fennerschool-associated.anu.edu.au/documents/CLE/VCH_Accounts_Summary_FINAL_for_pdf_distribution.pdf

On Disease Ecology

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One of the sleepers in population dynamics has always been the role of disease in population limitation and population fluctuations. Part of the reason for this is that disease studies need cooperation between skilled ecologists and skilled microbiologists. Another problem is the possibility of infinite regress in looking for disease agents as a cause of population change in natural populations – e.g. if it is not virus X, there are hundreds of other viruses that might be the culprit. In both North America and Europe one focus of concern has been on the hantavirus group (Luis et al. 2010; Mills et al. 2010, Davis et al. 2005, Mills et al. 1999). Hantaviruses come in many different forms and are typically carried by rodent species. Some varieties produce hemorrhagic fever with renal syndrome in Europe, Asia and Africa, but in the Americas the main disease of concern is HPS (hantavirus pulmonary syndrome). It is no surprise that often emerging diseases are studied only because some humans die from them. As of 2016, 690 cases of hantavirus pulmonary syndrome have been recorded in the USA, and 36% of these cases resulted in death. The reverse question of what the disease is doing to the animal population gets rather less attention typically than the human disease problem. The example I want to discuss here is the Sin Nombre virus (SNV) in deer mice (Peromyscus spp.), widespread rodents in North America.

The hantavirus outbreak in the Southwestern USA in the 1990s caused numerous human deaths and produced a number of field studies that showed a patchy pattern of infection among deer mice in Arizona and Colorado (Mills et al. 1999). Male mice were infected more than females and the suggestion was that males fighting for territories were infecting one another directly when population densities were high. The call for long-term studies went out and several studies from 3-5 years were carried out in the late 1990s until the problem of infection in the human population became less of an issue compared with other diseases such as Ebola in other parts of the world. The shift in concern resulted in reduced funding for field studies in North America.

In 1994 Rick Douglass and his research team began long term studies on the Sin Nombre virus in deer mice using 18 live trapping areas of 1 ha each spread across Montana and placed in a variety of habitats (Douglass et al. 2001). Long-term for their study was 15 years, all this at a time when 2-3 year studies were thought to be sufficient to unravel the nexus of infection and transmission. The idea was to complement in Montana similar rodent research in Arizona, New Mexico, and Colorado. The results are fascinating and important because they illustrate the importance of long term research and the understanding of what a well designed field study can produce.

Rightfully many of the hantavirus studies were focused on the human connection, but what I want to emphasize here is the impact of this virus on the rodent populations. Luis et al. (2012) estimated that male Peromyscus had their monthly survival rate reduced from 0.67 to 0.58 if they were seropositive, a 13% reduction, but females showed no effect of hantavirus on survival so that infected and uninfected females survived equally well. Hantavirus does reduce body growth rates of infected male mice. One consequence of these findings should be that the growth rate of Peromyscus populations in Montana should be only slightly affected by hantavirus infections, since it is the female component of the population that drives numbers. There are limitations to these conclusions since juveniles too young to live trap could suffer mortality that at present cannot be measured. The threshold for hantavirus transmission in these Peromyscus populations was about 17 individuals per ha (Luis et al. 2015), implying that hantavirus would disappear in populations smaller than this because it would not transmit. The consequence for us is that human hantavirus infections in North America are much more likely when deer mouse populations are high, and by monitoring deer mice ecologists can broadcast warnings when there are increased possibilities of infection with this lethal disease.

The details about the Sin Nombre hantavirus in North America are well covered in these and other papers. The most important general message from this research has been the need for long term studies to get at what might initially seem to be a simple population problem (Carver et al. 2015). There are a host of other viruses that infect rodent species and many other mammals and birds about which we know very little. The path to understanding the effects of these viruses on the animals they infect and their potential for human transmission will require much detailed work over a longer time period than what is now the funding horizon of our granting agencies. The Montana studies on the Sin Nombre virus required ecologists to trap for 20 years with more than 851,000 trap nights to catch 16,608 deer mice, and collect 10,572 blood samples to assess infections and gain an understanding of this virus disease. The problem too often is that it is easy to find ecologists and virologists keen to cooperate in these studies of disease, but it is not easy to find the long term funding that looks at these ecological problems in the time scale of 10-20 years or more. We need much more long term thinking about ecological problems and the funding to support team efforts on difficult problems that are not soluble in a 3-year time frame.

Carver, S., Mills, J.N., Parmenter, C.A., Parmenter, R.R., Richardson, K.S., Harris, R.L., Douglass, R.J., Kuenzi, A.J., and Luis, A.D. 2015. Toward a mechanistic understanding of environmentally forced zoonotic disease emergence: Sin Nombre hantavirus. BioScience 65(7): 651-666. doi: 10.1093/biosci/biv047.

Davis, S., Calvet, E., and Leirs, H. 2005. Fluctuating rodent populations and risk to humans from rodent-borne zoonoses. Vector-Borne and Zoonotic Diseases 5(4): 305-314.

Douglass, R.J., Wilson, T., Semmens, W.J., Zanto, S.N., Bond, C.W., Van Horn, R.C., and Mills, J.N. 2001. Longitudinal studies of Sin Nombre virus in deer mouse-dominated ecosystems of Montana. American Journal of Tropical Medicine and Hygiene 65(1): 33-41.

Luis, A.D., Douglass, R.J., Hudson, P.J., Mills, J.N., and Bjørnstad, O.N. 2012. Sin Nombre hantavirus decreases survival of male deer mice. Oecologia 169(2): 431-439. doi: 10.1007/s00442-011-2219-2.

Luis, A.D., Douglass, R.J., Mills, J.N., and Bjørnstad, O.N. 2010. The effect of seasonality, density and climate on the population dynamics of Montana deer mice, important reservoir hosts for Sin Nombre hantavirus. Journal of Animal Ecology 79(2): 462-470. doi: 10.1111/j.1365-2656.2009.01646.x.

Luis, A.D., Douglass, R.J., Mills, J.N., and Bjørnstad, O.N. 2015. Environmental fluctuations lead to predictability in Sin Nombre hantavirus outbreaks. Ecology 96(6): 1691-1701. doi: 10.1890/14-1910.1.

Mills, J.N., Amman, B.R., and Glass, G.E. 2010. Ecology of hantaviruses and their hosts in North America. Vector-Borne and Zoonotic Diseases 10(6): 563-574. doi: 10.1089/vbz.2009.0018.

Mills, J.N., Ksiazek, T.G., Peters, C.J., and Childs, J.E. 1999. Long-term studies of hantavirus reservoir populations in the southwestern United States: a synthesis. Emerging Infectious Diseases 5(1): 135-142.

Fishery Models and Ecological Understanding

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Anyone interested in population dynamics, fisheries management, or ecological understanding in general will be interested to read the exchanges in Science, 23 April 2016 on the problem of understanding stock changes in the northern cod (Gadus morhua) fishery in the Gulf of Maine. I think this exchange is important to read because it illustrates two general problems with ecological science – how to understand ecological changes with incomplete data, and how to extrapolate what is happening into taking some management action.

What we have here are sets of experts promoting a management view and others contradicting the suggested view. There is no question but that ecologists have made much progress in understanding both marine and freshwater fisheries. Probably the total number of person-years of research on marine fishes like the northern cod would dwarf that on all other ecological studies combined. Yet we are still arguing about fundamental processes in major marine fisheries. You will remember that the northern cod in particular was one of the largest fisheries in the world when it began to be exploited in the 16th century, and by the 1990s it was driven to about 1% of its prior abundance, almost to the status of a threatened species.

Pershing et al. (2015) suggested, based on data on a rise in sea surface temperature in the Gulf of Maine, that cod mortality had increased with temperature and this was causing the fishery management model to overestimate the allowable catch. Palmer et al. (2016) and Swain et al. (2016) disputed their conclusions, and Pershing et al. (2016) responded. The details are in these papers and I do not pretend to know whose views are closest to be correct.

But I’m interested in two facts. First, Science clearly thought this controversy was important and worth publishing, even in the face of a 99% rejection rate for all submissions to that journal. Second, it illustrates that ecology faces a lot of questions when it makes conclusions that natural resource managers should act upon. Perhaps it is akin to medicine in being controversial, even though it is all supposed to be evidence based. It is hard to imagine physical scientists or engineers arguing so publically over the design of a bridge or a hydroelectric dam. Why is it that ecologists so often spend time arguing with one another over this or that theory or research finding? If we admit that our conclusions about the world’s ecosystems are so meager and uncertain, does it mean we have a very long way to go before we can claim to be a hard science? We would hope not but what is the evidence?

One problem so well illustrated here in these papers is the difficulty of measuring the parameters of change in marine fish populations and then tying these estimates to models that are predictive of changes required for management actions. The combination of less than precise data and models that are overly precise in their assumptions could be a deadly combination in the ecological management of natural resources.

Palmer, M.C., Deroba, J.J., Legault, C.M., and Brooks, E.N. 2016. Comment on “Slow adaptation in the face of rapid warming leads to collapse of the Gulf of Maine cod fishery”. Science 352(6284): 423-423. doi:10.1126/science.aad9674.

Pershing, A.J., Alexander, M.A., Hernandez, C.M., Kerr, L.A., Le Bris, A., Mills, K.E., Nye, J.A., Record, N.R., Scannell, H.A., Scott, J.D., Sherwood, G.D., and Thomas, A.C. 2016. Response to Comments on “Slow adaptation in the face of rapid warming leads to collapse of the Gulf of Maine cod fishery”. Science 352(6284): 423-423. doi:10.1126/science.aae0463.

Pershing, A.J., Alexander, M.A., Hernandez, C.M., Kerr, L.A., Le Bris, A., Mills, K.E., Nye, J.A., Record, N.R., Scannell, H.A., Scott, J.D., Sherwood, G.D., and Thomas, A.C. 2015. Slow adaptation in the face of rapid warming leads to collapse of the Gulf of Maine cod fishery. Science 350(6262): 809-812. doi:10.1126/science.aac9819.

Swain, D.P., Benoît, H.P., Cox, S.P., and Cadigan, N.G. 2016. Comment on “Slow adaptation in the face of rapid warming leads to collapse of the Gulf of Maine cod fishery”. Science 352(6284): 423-423. doi:10.1126/science.aad9346.

On Statistical Progress in Ecology

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There is a general belief that science progresses over time and given that the number of scientists is increasing, this is a reasonable first approximation. The use of statistics in ecology has been one of ever increasing improvements of methods of analysis, accompanied by bandwagons. It is one of these bandwagons that I want to discuss here by raising the general question:

Has the introduction of new methods of analysis in biological statistics led to advances in ecological understanding?

This is a very general question and could be discussed at many levels, but I want to concentrate on the top levels of statistical inference by means of old-style frequentist statistics, Bayesian methods, and information theoretic methods. I am prompted to ask this question because of my reviewing of many papers submitted to ecological journals in which the data are so buried by the statistical analysis that the reader is left in a state of confusion whether or not any progress has been made. Being amazed by the methodology is not the same as being impressed by the advance in ecological understanding.

Old style frequentist statistics (read Sokal and Rohlf textbook) has been criticized for concentrating on null hypothesis testing when everyone knows the null hypothesis is not correct. This has led to refinements in methods of inference that rely on effect size and predictive power that is now the standard in new statistical texts. Information-theoretic methods came in to fill the gap by making the data primary (rather than the null hypothesis) and asking the question which of several hypotheses best fit the data (Anderson et al. 2000). The key here was to recognize that one should have prior expectations or several alternative hypotheses in any investigation, as recommended in 1897 by Chamberlin. Bayesian analysis furthered the discussion not only by having several alternative hypotheses but by the ability to use prior information in the analysis (McCarthy and Masters 2006). Implicit in both information theoretic and Bayesian analysis is the recognition that all of the alternative hypotheses might be incorrect, and that the hypothesis selected as ‘best’ might have very low predictive power.

Two problems have arisen as a result of this change of focus in model selection. The first is the problem of testability. There is an implicit disregard for the old idea that models or conclusions from an analysis should be tested with further data, preferably with data obtained independently from the original data used to find the ‘best’ model. The assumption might be made that if we get further data, we should add it to the prior data and update the model so that it somehow begins to approach the ‘perfect’ model. This was the original definition of passive adaptive management, which is now suggested to be a poor model for natural resource management. The second problem is that the model selected as ‘best’ may be of little use for natural resource management because it has little predictability. In management issues for conservation or exploitation of wildlife there may be many variables that affect population changes and it may not be possible to conduct active adaptive management for all of these variables.

The take home message is that we need in the conclusions of our papers to have a measure of progress in ecological insight whatever statistical methods we use. The significance of our research will not be measured by the number of p-values, AIC values, BIC values, or complicated tables. The key question must be: What new ecological insights have been achieved by these methods?

Anderson, D.R., Burnham, K.P., and Thompson, W.L. 2000. Null hypothesis testing: problems, prevalence, and an alternative. Journal of Wildlife Management 64(4): 912-923.

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.

McCarthy, M.A., and Masters, P.I.P. 2005. Profiting from prior information in Bayesian analyses of ecological data. Journal of Applied Ecology 42(6): 1012-1019. doi:10.1111/j.1365-2664.2005.01101.x.

Walters, C. 1986. Adaptive Management of Renewable Resources. Macmillan, New York.