Tag Archives: wildlife management

Blaming Climate Change for Ecological Changes

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

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 The general problem is that model failures or successes might not be published so even this approach can be biased if only a literature survey is undertaken.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

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

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

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

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

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

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

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

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

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

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

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

 

On A Global Agenda for Ecology

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Reading the ecology literature now I am excited by the papers that are filling in small gaps in our understanding of population and community ecology. Good work indeed. But I am concerned more about the big picture – what would we like ecological science to show to the world in 50 years as our achievements? There are two aspects of this question. At present the findings of ecological research are presented in the media mostly as what could be coarsely described as ecological trivia, light entertainment. We must continue to do this as it is an important part of keeping the public aware of environmental issues. The second aspect of our public face is the bigger issue of how we can make the future world a better place. This part is a global agenda for ecology that should be the background focus of all our research. So what should be our global agenda?

We could call it global change. Specifically, how will our ecological systems change as a joint consequence of climate change and human disturbances? So look out the window to any natural landscape where you live and ask how much we now know that will allow you to predict what that scene will be like in a century or so. We should be able to make this prediction more easily with human disturbed landscapes that with those driven by environmental change, but I am not sure everyone would agree with this hypothesis. We will probably know that if we continue to overgraze a grassland, we will end with a weed infested wasteland or even bare soil. Consequently, a rational management agency should be able to prevent this degradation. These kinds of change should be easy to manage yet we as a society continue to degrade ecosystems all over the globe. Is there an general index for degradation for the countries of the world, so we could add it to Greenhouse Gas Emissions, freshwater contamination, overharvesting of fish and timber, and a host of other environmental indicators that are useful to the public?

The consequences of climate change are the most difficult to understand and possibly manage. We have lived in a dream world of a stable environment, and the mathematical gurus focus on stability as a sine qua non. Change in a system that is well understood should be predictable both in the short term of 50 years and in the long term of 500 years. But we are not there yet. We work hard on the pieces – is the bird population of this particular national park going up or down?, how rapidly are peat bogs releasing CO2 under current changing climate? – but these details while important do not allow one to predict whole ecosystem shifts. more rapidly. What do we need to do as ecologists to achieve a broad consensus on global issues?

Sutherland et al. (2013, 2018) have made a heroic attempt both to recognize fundamental ecological questions and to identify emerging issues in a broader societal framework. This helps us to focus on both specific ecological issues as well as emerging global problems. One useful recommendation that could proceed from these reviews would be a specific journal that would review each year a small number of these questions or issues that would serve as a progress bar on increasing understanding of ecological unknowns.

A personal example might focus the problem. My colleagues, students, and I have been working in the Yukon boreal forest at Kluane for 46 years now, trying to understand community dynamics. The ecosystem moves slowly because of the cold climate, so in the short term of 50 years we cannot see there will be much significant change. But this is more of a guess than a solid prediction because a catastrophe – fire, insect attacks – could reset the system on a different pathway. The long term (500 year) trajectory for this ecosystem is much harder to predict, except to say that it will be driven largely by the climate-vegetation axis, and this is the link in ecosystem dynamics that we understand least. We cannot assume stability or equilibrium dynamics in boreal forests, and while paleo-ecologists have given us a good understanding of past changes in similar ecosystems, the past is not necessarily a good guide to future long-term changes. So I think a critic could well say that we have failed our attempt to understand our boreal forest ecosystem and be able to predict its trajectory, even though we have more than 300 papers describing how parts of this system interact.

My concern is that as we make progress with the pieces of the ecology puzzle we more and more lose sight of the final goals, and we are lost in the details of local ecosystems. Does this simply mean that we have an ecological ‘Red Queen’ that we will forever be chasing? Perhaps that is both the fundamental joy and the fundamental frustration of working on changing ecological systems. In the meantime, enjoy slaying the unknowns of local, specific ecosystems and on occasion look back to see how far we have come.

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

Sutherland, W.J.et al. (2018). A 2018 Horizon Scan of Emerging Issues for Global Conservation and Biological Diversity. Trends in Ecology & Evolution 33(1): 47-58. doi: 10.1016/j.tree.2017.11.006.

 

On Culling Overabundant Wildlife

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Ecologists have written much about the culling of wildlife from an ecological and conservation perspective (Caughley 1981, Jewell et al. 1981, Bradford and Hobbs 2008, Hampton and Forsyth 2016). The recommendations for culling as a method for reducing overabundant wildlife populations are typically scientifically well established and sensitive to animal welfare. The populations chosen for culling are classified as ‘overabundant’. But overabundant is a human-defined concept, and thus requires some form of social license to agree about what species, in which conditions, should be classified as ‘overabundant’. The problem of overabundance usually arises when humans make changes that permit a species to become so numerous locally that it is having an adverse effect on its food supply, its competitors, or the integrity of the ecosystem it occupies. Once overabundance is recognized, the management issue is to determine which methods should be used to reduce abundance to a suitable level. Culling is only one option for removing wildlife, and animals may be captured and moved elsewhere if that is possible or sterilized to prevent reproduction and further increase (Liu et al. 2012, Massei and Cowan 2014).

All these policy issues are subject to open public debate and these debates are often heated because of different belief systems. Animal rights advocates may push the assumption that we humans have no rights to kill any wildlife at all. News media often concentrate on the most stringent views on controlling populations that are overabundant, and public discussion becomes impossible. Two aspects need to be noted that are often lost in any discussion. First is the cost of alternatives in dollars and cents. As an example, most ecologists would agree that wild horses are overabundant on open range in western United States (Davies et al. 2014, Rutberg et al. 2017) but the question is what to do about this. Costs to reduce horse populations by capturing horses and penning them and feeding them are astronomical (the current situation in western USA, estimated at $25,000 per animal) but this method of control could be done if society wishes to spend money to achieve this goal. Culling would be much cheaper, but the killing of large animals is anathema to many people who speak loudly to politicians. Fertility control methods are improving with time and may be more acceptable socially, but costs are high and results in population reduction can be slow in coming (Hobbs and Hinds 2018). Models are essential to sort out many of these issues, whether it be the projected costs of various options (including doing nothing), the expected population trajectory, or the consequences for other species in the ecosystem.

The bottom line is that if overabundant wildlife populations are not reduced by some means, the result must be death by starvation or disease coupled with extensive damage to other species in these ecosystems. This type of “Plan B” is the second aspect not often considered in discussions of policies on overabundant species. In the present political scene in North America opposition to culling overabundant wildlife is strong, coherent discussion is rarely possible, and Plan B problems are rarely heard. Most overabundant wildlife result from human actions in changing the vegetation, introducing new species, and reducing and fragmenting wildlife habitats. Wishing the problems will go away without doing anything is not a feasible course of action.

These kinds of problems in wildlife management are soluble in an objective manner with careful planning of research and management actions (Hone et al. 2017). Ecologists have a moral duty to present all scientific sides of the management of overabundant species, and to bring evidence into the resulting social and political discussions of management issues. It is not an easy job.

Bradford, J.B., and N.T. Hobbs. 2008. Regulating overabundant ungulate populations: An example for elk in Rocky Mountain National Park, Colorado. Journal of Environmental Management 86:520-528. doi: 10.1016/j.jenvman.2006.12.005

Caughley, G. 1981. Overpopulation. Pages 7-19 in P.A. Jewell S. Holt, and D. Hart, editors. Problems in Management of Locally Abundant Wild Mammals. Academic Press, New York. ISBN: 978-0-12-385280-9

Davies, K. W., Collins, G. & Boyd, C. S. (2014) Effects of feral free-roaming horses on semi-arid rangeland ecosystems: an example from the sagebrush steppe. Ecosphere, 5, 127. doi: 10.1890/ES14-00171.1

Hampton, J. O., and D. M. Forsyth. 2016. An assessment of animal welfare for the culling of peri-urban kangaroos. Wildlife Research 43:261-266. doi: 10.1071/WR16023

Hobbs, R.J. and Hinds, L.A. (2018). Could current fertility control methods be effective for landscape-scale management of populations of wild horses (Equus caballus) in Australia? Wildlife Research 45, 195-207. doi: 10.1071/WR17136.

Hone, J., Drake, V.A. & Krebs, C.J. (2017) The effort–outcomes relationship in applied ecology: Evaluation and implications BioScience, 67, 845-852. doi: 10.1093/biosci/bix091

Jewell, P. A., Holt, S. & Hart, D. (1982) Problems in Management of Locally Abundant Wild Mammals. Academic Press, New York. 360 pp. ISBN: 978-0-12-385280-9

Liu, M., Qu, J., Yang, M., Wang, Z., Wang, Y., Zhang, Y. & Zhang, Z. (2012) Effects of quinestrol and levonorgestrel on populations of plateau pikas, Ochotona curzoniae, in the Qinghai-Tibetan Plateau. Pest Management Science, 68, 592-601. doi: 10.1002/ps.2302

Massei, G. & Cowan, D. (2014) Fertility control to mitigate human–wildlife conflicts: a review. Wildlife Research, 41, 1-21. doi: 10.1071/WR13141

Rutberg, A., Grams, K., Turner, J.W. & Hopkins, H. (2017) Contraceptive efficacy of priming and boosting doses of controlled-release PZP in wild horses. Wildlife Research, 44, 174-181. doi: 10.1071/WR16123

On Detecting Rare Species with Camera Trapping

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If you are a conservation biologist and you wish to save all or as many species as possible, your first problem is detectability. Does the species of concern live in this habitat? If it is present how many are there, and is their abundance changing from year to year? These are fundamental questions in conservation science and there is accordingly a very large literature on how to answer these simple questions for animals in different taxonomic groups. I want to deal briefly here with rare species in which the issue of detectability is most critical.

There is a large array of papers on detection methods in the conservation literature (e.g. Brodie et al. 2018; Crates et al. 2017; Steenweg et al. 2016; Clement et al. 2016, Trolliet et al. 2014). Detection methods vary from live trapping marked individuals, visual sighting of unmarked individuals, camera photos of marked or unmarked individuals, sign data such as tracks or scats in snow, mud or sand, DNA fingerprinting, and many clever natural-history- derived methods to measure detection. These methods are well developed for common animals (Williams et al. 2002).

Rare species are the first problem faced by all these detection methods. Rare species range from those virtually impossible to detect with current technology to those that turn up infrequently in the designated detection device. The conservation challenge of rare species is difficult if they are hard to detect and difficult to study so that we have few natural history parameters to guide conservation actions. For these we can only set aside what we think are suitable areas and conserve them.

The technology of monitoring rare species that can be detected at some reasonable level has greatly improved with the advent of passive-infrared-cameras that can be deployed 24-7 to capture images of whomever walks or swims by. But this technology raises a whole set of methodological issues that must be addressed. The first and most obvious one is the skill of the observer both in setting up the cameras and in looking at the photos to identify correctly the species present. The second and more difficult question is what to count as a detection or ‘hit’. If your question is simply ‘occupancy’ seeing one photograph in the time period of the study provides a + for occupancy. But many ecologists wish to connect the dots from occupancy scores to abundance so that some index of population numbers can arise from these camera data. To make this leap of faith relies heavily on the experimental design of the camera placements, the number of cameras, the make of the cameras (Meek et al. 2014), and the exact placement of cameras on trees or stakes to cover a specific area of habitat. Clearly if cameras are placed too close to one another, the photos from the different cameras are not independent, as most of the models of occupancy assume (Brodie et al. 2018). If bait is used with the cameras the situation becomes even more complex because some species may be attracted while others are repelled by the bait. In general camera detections or ‘hits’ for a particular species are a measure of activity rather than a direct measure of abundance, and so often the assumption is made that activity = abundance, which must be justified. In the extreme case in which a density estimate is needed from camera data, the problem of ‘edge effects’ of the sampled area must be considered just as it does with grid trapping (e.g Thornton and Pekins 2015). New approaches for estimating density from camera data appear almost daily and must be evaluated for accuracy (Nakashima et al. 2018).

We are now in the exponential phase of camera trapping with cameras put up in all sorts of spatial designs for different lengths of time with the hope that someone will have time to look at the photos and some clever statistician can factor out all the potential biases and non-independence of the resulting data. So in a nutshell my simple advice is to use cameras to gather wildlife information but think carefully about what exactly you wish to achieve: occupancy?, an index of abundance?, actual numerical abundance? population density? Or simply beautiful photos of interesting animals? And in the end you may be envious of plant ecologists whose plants do not walk away when you census them.

 

Brodie, J.F., et al. (2018). Models for assessing local-scale co-abundance of animal species while accounting for differential detectability and varied responses to the environment. Biotropica 50, 5-15. doi: 10.1111/btp.12500.

Clement, M. J., J. E. Hines, J. D. Nichols, K. L. Pardieck, and D. J. Ziolkowski. 2016. Estimating indices of range shifts in birds using dynamic models when detection is imperfect. Global Change Biology 22:3273-3285. doi: 10.1111/gcb.13283

Crates, R., L. Rayner, D. Stojanovic, M. Webb, and R. Heinsohn. 2017. Undetected Allee effects in Australia’s threatened birds: implications for conservation. Emu 117:207-221. doi: 10.1080/01584197.2017.1333392

Meek, P.D., et al. (2014). Camera traps can be heard and seen by animals. PLoS ONE 9, e110832. doi: 10.1371/journal.pone.0110832.

Nakashima, Y., Fukasawa, K., and Samejima, H. (2018). Estimating animal density without individual recognition using information derivable exclusively from camera traps. Journal of Applied Ecology 55, 735-744. doi: 10.1111/1365-2664.13059.

Smith, D.H.V. and Weston, K.A. (2017). Capturing the cryptic: a comparison of detection methods for stoats (Mustela erminea) in alpine habitats. Wildlife Research 44, 418-426. doi: 10.1071/WR16159.

Steenweg, R., et al. (2016). Camera-based occupancy monitoring at large scales: Power to detect trends in grizzly bears across the Canadian Rockies. Biological Conservation 201:192-200. doi: 10.1016/j.biocon.2016.06.020

Thornton, D.H. and Pekins, C.E. (2015). Spatially explicit capture-recapture analysis of bobcat (Lynx rufus) density: implications for mesocarnivore monitoring Wildlife Research 42, 394-404. doi: 10.1071/WR15092.

Trolliet, F., et al. (2014). Use of camera traps for wildlife studies. A review. Biotechnology, Agronomy, Society and Environment (BASE) 18, 446-454.

Williams, B.K., Nichols, J.D., and Conroy, M.J. (2002) ‘Analysis and Management of Animal Populations.’ (Academic Press: New York.). 817 pp.

 

On Caribou and Hypothesis Testing

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Mountain caribou populations in western Canada have been declining for the past 10-20 years and concern has mounted to the point where extinction of many populations could be imminent, and the Canadian federal government is asking why this has occurred. This conservation issue has supported a host of field studies to determine what the threatening processes are and what we can do about them. A recent excellent summary of experimental studies in British Columbia (Serrouya et al. 2017) has stimulated me to examine this caribou crisis as an illustration of the art of hypothesis testing in field ecology. We teach all our students to specify hypotheses and alternative hypotheses as the first step to solving problems in population ecology, so here is a good example to start with.

From the abstract of this paper, here is a statement of the problem and the major hypothesis:

“The expansion of moose into southern British Columbia caused the decline and extirpation of woodland caribou due to their shared predators, a process commonly referred to as apparent competition. Using an adaptive management experiment, we tested the hypothesis that reducing moose to historic levels would reduce apparent competition and therefore recover caribou populations. “

So the first observation we might make is that much is left out of this approach to the problem. Populations can decline because of habitat loss, food shortage, excessive hunting, predation, parasitism, disease, severe weather, or inbreeding depression. In this case much background research has narrowed the field to focus on predation as a major limitation, so we can begin our search by focusing on the predation factor (review in Boutin and Merrill 2016). In particular Serrouya et al. (2017) focused their studies on the nexus of moose, wolves, and caribou and the supposition that wolves feed preferentially on moose and only secondarily on caribou, so that if moose numbers are lower, wolf numbers will be lower and incidental kills of caribou will be reduced. So they proposed two very specific hypotheses – that wolves are limited by moose abundance, and that caribou are limited by wolf predation. The experiment proposed and carried out was relatively simple in concept: kill moose by allowing more hunting in certain areas and measure the changes in wolf numbers and caribou numbers.

The experimental area contained 3 small herds of caribou (50 to 150) and the unmanipulated area contained 2 herds (20 and 120 animals) when the study began in 2003. The extended hunting worked well, and moose in the experimental area were reduced from about 1600 animals down to about 500 over the period from 2003 to 2014. Wolf numbers in the experimental area declined by about half over the experimental period because of dispersal out of the area and some starvation within the area. So the two necessary conditions of the experiment were satisfied – moose numbers declined by about two-thirds from additional hunting and wolf numbers declined by about half on the experimental area. But the caribou population on the experimental area showed mixed results with one population showing a slight increase in numbers but the other two showing a slight loss. On the unmanipulated area both caribou populations showed a continuing slow decline. On the positive side the survival rate of adult caribou was higher on the experimental area, suggesting that the treatment hypothesis was correct.

From the viewpoint of caribou conservation, the experiment failed to change the caribou population from continuous slow declines to the rapid increase needed to recover these populations to their former greater abundance. At best it could be argued that this particular experiment slowed the rate of caribou decline. Why might this be? We can make a list of possibilities:

  1. Moose numbers on the experimental area were not reduced enough (to 300 instead of to 500 achieved). Lower moose would have meant much lower wolf numbers.
  2. Small caribou populations are nearly impossible to recover because of chance events that affect small numbers. A few wolves or bears or cougars could be making all the difference to populations numbering 10-20 individuals.
  3. The experimental area and the unmanipulated area were not assigned treatments at random. This would mean to a pure statistician that you cannot make statistical comparisons between these two areas.
  4. The general hypothesis being tested is wrong, and predation by wolves is not the major limiting factor to mountain caribou populations. Many factors are involved in caribou declines and we cannot determine what they are because they change for area to area, year to year.
  5. It is impossible to do these landscape experiments because for large landscapes it is impossible to find 2 or more areas that can be considered replicates.
  6. The experimental manipulation was not carried out long enough. Ten years of manipulation is not long for caribou who have a generation time of 15-25 years.

Let us evaluate these 6 points.

#1 is fair enough, hard to achieve a population of moose this low but possible in a second experiment.

#2 is a worry because it is difficult to deal experimentally with small populations, but we have to take the populations as a given at the time we do a manipulation.

#3 is true if you are a purist but is silly in the real world where treatments can never be assigned at random in landscape experiments.

#4 is a concern and it would be nice to include bears and other predators in the studies but there is a limit to people and money. Almost all previous studies in mountain caribou declines have pointed the finger at wolves so it is only reasonable to start with this idea. The multiple factor idea is hopeless to investigate or indeed even to study without infinite time and resources.

#5 is like #3 and it is an impossible constraint on field studies. It is a common statistical fallacy to assume that replicates must be identical in every conceivable way. If this were true, no one could do any science, lab or field.

#6 is correct but was impossible in this case because the management agencies forced this study to end in 2014 so that they could conduct another different experiment. There is always a problem deciding how long a study is sufficient, and the universal problem is that the scientists or (more likely) the money and the landscape managers run out of energy if the time exceeds about 10 years or more. The result is that one must qualify the conclusions to state that this is what happened in the 10 years available for study.

This study involved a heroic amount of field work over 10 years, and is a landmark in showing what needs to be done and the scale involved. It is a far cry from sitting at a computer designing the perfect field experiment on a theoretical landscape to actually carrying out the field work to get the data summarized in this paper. The next step is to continue to monitor some of these small caribou populations, the wolves and moose to determine how this food chain continues to adjust to changes in prey levels. The next experiment needed is not yet clear, and the eternal problem is to find the high levels of funding needed to study both predators and prey in any ecosystem in the detail needed to understand why prey numbers change. Perhaps a study of all the major predators – wolves, bears, cougars – in this system should be next. We now have the radio telemetry advances that allow satellite locations, activity levels, timing of mortality, proximity sensors when predators are near their prey, and even video and sound recording so that more details of predation events can be recorded. But all this costs money that is not yet here because governments and people have other priorities and value the natural world rather less than we ecologists would prefer. There is not yet a Nobel Prize for ecological field research, and yet here is a study on an iconic Canadian species that would be high up in the running.

What would I add to this paper? My curiosity would be satisfied by the number of person-years and the budget needed to collect and analyze these results. These statistics should be on every scientific paper. And perhaps a discussion of what to do next. In much of ecology these kinds of discussions are done informally over coffee and students who want to know how science works would benefit from listening to how these informal discussions evolve. Ecology is far from simple. Physics and chemistry are simple, genetics is simple, and ecology is really a difficult science.

Boutin, S. and Merrill, E. 2016. A review of population-based management of Southern Mountain caribou in BC. {Unpublished review available at: http://cmiae.org/wp-content/uploads/Mountain-Caribou-review-final.pdf

Serrouya, R., McLellan, B.N., van Oort, H., Mowat, G., and Boutin, S. 2017. Experimental moose reduction lowers wolf density and stops decline of endangered caribou. PeerJ  5: e3736. doi: 10.7717/peerj.3736.

 

On Wildlife Management

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There are two global views about wildlife management that are echoed in conservation biology. The first view is that we manage wildlife for the sake of wildlife so that future generations have the ability to see what we see when we go out into the woods and fields. The second view is that we manage wildlife and indeed all of nature for humans to exploit. The second view was elegantly summarized many years ago by White (1967):

“Our science and technology have grown out of Christian attitudes toward man’s relation to nature which are almost universally held not only by Christians and neo-Christians but also by those who fondly regard themselves as post-Christians. Despite Copernicus, all the cosmos rotates around our little globe. Despite Darwin, we are not, in our hearts, part of the natural process. We are superior to nature, contemptuous of it, willing to use it for our slightest whim. The newly elected Governor of California, like myself a churchman but less troubled than I, spoke for the Christian tradition when he said (as is alleged), “when you’ve seen one redwood tree, you’ve seen them all.” (p.1206)

The first view of wildlife is now for ecologists the dominant conservation ethic of our time, the recognition that wildlife and nature in general has intrinsic value (Vucetich et al. 2015). Yet when there are conflicts in environmental management, the second view that humans trump all comes to the fore. Think of examples in your region. When caribou and moose are declining, the shout goes up to shoot the wolves. The golden example of this is perhaps Norway where wolves are nearly all gone and moose are superabundant and fed in winter so that there are plenty for hunters to shoot in the following year. Where domestic and feral cats threaten bird populations, the view typically expressed is that cats are our pets and quite cute, and certainly cannot be regulated or controlled as feral pests.

One of the main defenses of biodiversity conservation during the last 20 years has been the role of ecosystem services. The utilitarian view that ecosystems do things for humans that you can then calculate in dollars has been used to carry conservation forward for those who subscribe to the second global view of nature as something that exists only for our exploitation. Two recent reviews are critical of this approach. Silvertown (2015) argues that the ecosystem services paradigm has been oversold and suggests alternatives. An important critical overview of the conundrum of biodiversity research is presented very clearly in Vellend (2017) and is essential reading for all those interested in environmental management issues and the collision of science and human values expressed in our two global views of biodiversity conservation.

Wildlife managers must operate with the first view in mind to manage wildlife for wildlife but at the same time must act in ways determined by their political masters to adopt the second view of human values over wildlife. Ecologists walk a thin line in this dilemma. A good example is the book by Woinarski et al. (2007) which details the disastrous state of environmental management in northern Australia. There are courageous attempts to resolve these management problems and to bridge the two global views by bringing ecological knowledge into policy development and environmental management (e.g. Morton et al. 2009, Lindenmayer et al. 2015). Many others beginning with Aldo Leopold in North America and many others in Europe have made elegant pleas for the first global view of wildlife conservation. The attempts now to bridge this gap between exploitation and preservation are to bring social sciences into environmental research programs, and these efforts can be increasingly effective. But there is a large contingent of the public that support the second view that humans are the most important species on earth. The increasing collision of rising human populations, resource shortages, and climate change produce a perfect storm of events that place wildlife management and environmental sustainability in a difficult position. Everyone who is able must speak up for the first global view in order to achieve a sustainable society on earth and for wildlife and biodiversity in general to be protected for future generations.

Lindenmayer, D.B.,et al. 2015. Contemplating the future: Acting now on long-term monitoring to answer 2050’s questions. Austral Ecology 40(3): 213-224. doi: 10.1111/aec.12207.

Morton, S.R., et al. 2009. The big ecological questions inhibiting effective environmental management in Australia. Austral Ecology 34(1): 1-9. doi: 10.1111/j.1442-9993.2008.01938.x.

Silvertown, J. 2015. Have Ecosystem Services been oversold? Trends in Ecology & Evolution 30(11): 641-648. doi: 10.1016/j.tree.2015.08.007.

Vellend, M. 2017. The biodiversity conservation paradox. American Scientist 105(2): 94-101.

Vucetich, J.A., Bruskotter, J.T., and Nelson, M.P. 2015. Evaluating whether nature’s intrinsic value is an axiom of or anathema to conservation. Conservation Biology 29(2): 321-332. doi: 10.1111/cobi.12464.

White, L., Jr. 1967. The historical roots of our ecologic crisis. Science 155(3767): 1203-1207.

Woinarski, J., Mackey, B., Nix, H., and Traill, B. 2007. The Nature of Northern Australia: Natural values, ecological processes and future prospects. Australian National University E Press, Canberra. (available at: http://press.anu.edu.au/publications/nature-northern-australia)

On Conservation

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The question of how ecology can guide decisions about conservation actions is a vexed one of which much has already been written with respect to conservation triage (Bottrill et al. 2009, Gerber 2016). The global question – what should we do now? – produces two extreme answers: (1) do nothing. The biodiversity on earth has gone through many climatic fluctuations imposed by geology and planetary physics and these forces are out of our hands. Or (2) we must protect all species because we do not know if they are important for ecosystem function. The government recognizes that (2) is impossible, and either reflects back to answer (1) or politely asks scientists to suggest what is possible to achieve with limited funding. John Wiens (2016) in an interesting discussion in the British Ecological Society Bulletin (December 2016, pp 38-39) suggests that two possible solutions to this conundrum are to get more funding for conservation to reduce this clear financial limitation, or secondly to move from the conservation of individual species to that of ecosystems. The problem he and many others recognize is that the public at large fall in love with individual species much more readily than with ecosystems. It is the same problem medical science often faces with contributions from wealthy people – attack individual diseases with my funding, not public health in general.

Ecologists face this dilemma with respect to their research agenda and research grants in general – what exactly can you achieve in 3-5 years with a small amount of money? If your research is species-specific, something useful can often be studied particularly if the threatening processes are partly understood and you adopt an experimental approach. If your research is ecosystem oriented and your funds are limited you must generally go to the computer and satellite ecology to make any short term research possible. This problem of larger scale = larger costs can be alleviated if you work in a group of scientists all addressing the same ecosystem issue. This still requires large scale funding which is not as easily obtained as ecologists might like. The government by contrast wishes more and more to see results even after only a few years, and asks whether you have answered your original question. The result is a patchwork of ecological data which too often makes no one happy.

If you want a concrete example, consider the woodland caribou of western Canada (Schneider et al. 2010). For these caribou Hebblewhite (2017) has clearly outlined a case in which the outcomes of any particular action are difficult to predict with the certainty that governments and business would be happy with. Many small herds are decreasing in size, and one path is to triage them, leaving many small herds to go extinct and trying to focus financial resources to save larger herds in larger blocks of habitat for future generations. The problem is the oil and gas industry in western Canada, and hence the battle between resources that are worth billions of dollars and a few caribou. Wolf control can serve as a short term solution, but it is expensive and temporary. Governments like action even if it is of no use in the long term; it makes good media coverage. None of these kinds of conservation decisions are scientific in nature, and must be policy decisions by governments. It flips us back into the continuum between options (1) and (2) in the opening paragraph above. And for governments policy decisions are more about jobs and money than about conservation.

The list of threatened and endangered species that make our newspapers are a tiny fraction of the diversity of species in any ecosystem. There is no question but that many of these charismatic species are declining in numbers, but the two larger questions are: will this particular species go extinct? And if this happens will this make any difference to ecosystem function? There is scarcely a single species of all that are listed as threatened and endangered for which ecologists have a good answer to either of these questions. So the fallback position to option (1) is that we have a moral obligation to protect all species. But this fallback position leads us even further out of science.

In the end we must ask as scientists what we can do with the understanding we have, and what more needs to be done to improve this understanding. Behind all this scientific research looms the elephant of climate change which we either ignore or build untestable computer models to make ‘predictions’ which may or may not occur, if only because of the time scales involved.

None of these problems prevents us from taking actions on conservation on the ground (Wiens 2016a). We know that, if we take away all the habitat, species abundances will decline and some will go extinct. Protecting habitat is the best course of action now because it needs little research to guide action. There is much to know yet about the scale of habitats that need preservation, and about how the present scale of climate change is affecting protected areas now. Short term research can be most useful for these issues. Long-term research needs to follow.

Bottrill, M.C., et al. (2009) Finite conservation funds mean triage is unavoidable. Trends in Ecology & Evolution, 24, 183-184. doi: 10.1016/j.tree.2008.11.007

Gerber, L.R. (2016) Conservation triage or injurious neglect in endangered species recovery. Proceedings of the National Academy of Sciences USA, 113, 3563-3566. doi: 10.1073/pnas.1525085113

Hebblewhite, M. (2017) Billion dollar boreal woodland caribou and the biodiversity impacts of the global oil and gas industry. Biological Conservation, 206, 102-111. doi: 10.1016/j.biocon.2016.12.014

Schneider, R.R., Hauer, G., Adamowicz, W.L. & Boutin, S. (2010) Triage for conserving populations of threatened species: The case of woodland caribou in Alberta. Biological Conservation, 143, 1603-1611. doi: 10.1016/j.biocon.2010.04.002

Wiens, J.A. (2016) Is conservation a zero-sum game? British Ecological Society Bulletin 47(4): 38-39.

Wiens, J.A. (2016a) Ecological Challenges and Conservation Conundrums: Essays and Reflections for a Changing World. John Wiley and Sons, Hoboken, New Jersey. 344 pp. ISBN: 9781118895108

Predator Free New Zealand

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The New Zealand Government announced in July 2016 the adoption of Predator Free New Zealand 2050, a program for the control and eradication of introduced pests. It is setting up a new public-private partnership company by the beginning of 2017 to help fund regional large-scale predator eradication programs with the anticipated funding ratio of 1 government dollar to 2 private dollars. This is a bold new program grounded in the fundamental research of an excellent array of conservation biologists that have carried out the field research underpinning what needs to be done to protect native biodiversity in New Zealand.

Because of its isolation and the complete absence of endemic terrestrial vertebrate predators, New Zealand has become a basket case for the conservation of native species after the introduction of four species of rodents – Norway rat, black rat, house mouse, and Pacific rat (kiore) – as well as the possum (introduced for fur), the stoat (to “control rodents”) and the hedgehog (Goldson et al. 2015). The initial focus in this program will be on rats, stoats, and possums. Rat control on islands has already been a major success story for New Zealand scientists (Russell et al. 2016).

Four short-term goals have been set for 2025 for the Predator Free New Zealand project:

  • An additional 1 million hectares of land where pests have been supressed or removed through Predator Free New Zealand partnerships
  • Development of a scientific breakthrough capable of removing at least one small mammal predator from New Zealand entirely
  • Demonstration areas of more than 20,000 hectares that are predator free without the use of fences
  • Complete removal of all introduced predators from offshore island nature reserves

This is a striking vision, and it puts New Zealand at the forefront of global conservation efforts and goals. Everyone appreciates that it will not be easy. In particular there has to be careful attention to the order in which pests are removed. Competition between invasive species as well as predation among them often has counterintuitive results. In New Zealand when rats were removed from experimental plots, house mice increased, and when possums were removed rats increased (Ruscoe et al. 2011). When stoats (Mustela erminea) were removed, there was no effect on rat or mouse abundance, contrary to what a model predicted (Tompkins and Veltman 2006). At the moment there is no clear way to do a total removal of these pest mammals all at once rather than sequentially.

One of the major stimuli for this program has been stopping bovine TB transmission from possums to cattle. The brushtail possum (introduced from Australia) is a disease reservoir and vector of bovine tuberculosis to cattle. Extensive control programs for possums are applied over about 10 million ha in New Zealand by the spreading of 1080 poison baits and trapping, and this program has reduced possum populations to low numbers but not eliminated this pest (Byrom et al. 2016). Poisoning for possum control also reduces stoats and rats, and so has secondary benefits for native biodiversity. A total of approximately NZ$55 million is spent each year on this control program, and if possums could be eradicated, the financial benefits would be great for the cattle industry. Byrom et al. (2016) showed that possum reduction by poisoning had benefits not only for TB transmission but also for increases in vegetation (reduced herbivory), invertebrate, frog and bird abundance.

Two worries are that the social license to continue widespread use of deadly poisons will erode in the future and secondly that the pest species will eventually evolve resistance to the poisons. For these reasons much research is needed on more clever ways of achieving pest reduction and elimination.

The success of island eradications in the past 20 years has emboldened ecologists to wish for successes on larger and larger scales. But eradication is a complex problem and there is a long history of success and failures, particularly in insect populations (Myers et al. 2000). But by reaching out with a direct challenge to applied ecologists, molecular biologists, chemists, and other clever scientists, New Zealand has moved the standard forward in ways that bode well for understanding more why ecology matters.

And then it is on to the feral cats.

Byrom, A.E., Innes, J. & Binny, R.N. (2016) A review of biodiversity outcomes from possum-focused pest control in New Zealand. Wildlife Research, 43, 228-253. doi: 10.1071/WR15132

Campbell, K.J., et al. (2015) The next generation of rodent eradications: Innovative technologies and tools to improve species specificity and increase their feasibility on islands. Biological Conservation, 185, 47-58. doi: 10.1016/j.biocon.2014.10.016

Goldson, S.L., et al. (2015) New Zealand pest management: current and future challenges. Journal of the Royal Society of New Zealand, 45, 31-58. doi: 10.1080/03036758.2014.1000343

Myers, J.H., Simberloff, D., Kuris, A.M. & Carey, J.R. (2000) Eradication revisited: dealing with exotic species. Trends in Ecology and Evolution, 15, 316-320.

Ruscoe, W.A. et al. (2011) Unexpected consequences of control: competitive vs. predator release in a four-species assemblage of invasive mammals. Ecology Letters, 14, 1035-1042. doi: 10.1111/j.1461-0248.2011.01673.x

Russell, J.C. & Broome, K.G. (2016) Fifty years of rodent eradications in New Zealand: another decade of advances. New Zealand Journal of Ecology, 40, 197-204. doi: 10.20417/nzjecol.40.22.

Tompkins, D.M. & Veltman, C.J. (2006) Unexpected consequences of vertebrate pest control: predictions from a four-species community model. Ecological Applications, 16, 1050-1061. doi: 10.1890/1051-0761(2006)016[1050:UCOVPC]2.0.CO;2

 

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 Caribou and the Conservation Conundrum

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The central conundrum of conservation is the conflict between industrial development and the protection of biodiversity. And the classic example of this in Canada is the conservation of caribou. Caribou in the millions have ranged over almost all of Canada in the past. They are now retreating in much of the southern part of their range, have nearly gone extinct in the High Arctic, and are extinct on Haida Gwaii (Queen Charlotte Islands). The majority of populations with adequate data are dropping in numbers rapidly. The causes of their demise point to human habitat destruction from forestry, mining, oil and gas developments and roads (Festa-Bianchet et al. 2011). We march on with economic development, and caribou are in the way of progress.

The nexus of interactions underlying this crisis is reasonably well understood for boreal caribou and there is an extensive literature on the topic (Bergerud et al. 2007; Hervieux et al. 2013; Hervieux et al. 2014; Schaefer and Mahoney 2013; Wittmer et al. 2007). Caribou avoid human constructions like pipelines, mines, forestry operations, and roads. Forestry in particular opens up habitat that tends to favor deer and moose. Climate change makes winters less severe for deer. More prey makes more predators, and caribou are typically accidental, secondary prey from wolves that live largely off moose and deer. The habitats that humans open up with roads, seismic lines, and wellheads provide superhighways for wolves and other predators, so that predator access is greatly improved. Such access roads also allow hunters to access ungulates and potentially increase the harvest rate.

If predators are the key immediate factor reducing caribou populations, there seem to be two general solutions. Killing wolves is the most obvious management action, and much of wildlife management in North America has historically been based on the simple paradigm: “killing wolves is the answer, now what is the question?” But two problems arise. There are more predators than wolves (e.g. bears) and secondly killing wolves does not work very well (Hayes 2010). At best it seems to slow down the caribou decline at great expense, and it has to be continuous year after year because killing wolves increases the reproductive rate of those left behind and migration of wolves into the “control” area is rapid. So this management action becomes too expensive in the long run to work well and most people don’t want to see bears killed wholesale either. So the next option is to use fencing to protect caribou from contact with all predators. These fences could be on small areas into which pregnant female caribou are put in the spring to have their calves, and then released when the calves are a few months old and have a better chance of avoiding predators. Or the ultimate fence would be around hundreds of square kilometers to enclose a permanent caribou population with all the predators removed inside the fenced area. This would require continuous maintenance and is very costly. It turns caribou into a zoo animal, albeit on a large scale.

There is one other solution and that is to set aside very large areas of habitat that are not invaded by the forestry, mining, and oil industries, and to monitor the dynamics of caribou in these large reserves. Manitoba is apparently doing this, with reported success in stopping caribou declines.

Beyond these southern populations of caribou in the boreal forest zone, the problems of caribou population trends on the tundra are difficult to unravel, partly because of a lack of data arising from a shortage of funds (Gunn et al. 2011). Climate change is happening and the exact effects on tundra populations is unclear. Many barren-ground caribou herds show fluctuations in abundance with a period of about 50 years. Food supply exhaustion may be one factor in the fluctuations but harvesting is also involved. Local harvest data are often not recorded and with poor population data and poor harvest data we can rarely determine the trajectories of the herds or explain why they are changing in abundance. Peary caribou in the far north are suffering from climate change, rain events in winter that freezes their food supply of lichens under ice so they starve. No one knows how to alleviate the weather, and we only add to the problem with our greenhouse gas emissions. Peary caribou now survive in very low numbers but we cannot be sure that will continue.

All in all, we work hard to conserve large mammal ecosystems in tropical countries but seem far too unconcerned about our Canadian caribou heritage. To inform conservation actions, serious long-term population studies are sorely needed, including more frequent aerial census estimates for all the caribou herds, radio-collaring individuals for demographic data and movements, and complete harvesting data from all sources.

 

Bergerud, A.T., Dalton, W.J., Butler, H., Camps, L., and Ferguson, R. 2007. Woodland caribou persistence and extirpation in relic populations on Lake Superior. Rangifer 27(4): 57-78 (Special Issue No. 17). doi: http://dx.doi.org/10.7557/2.27.4.321

Festa-Bianchet, M., Ray, J.C., Boutin, S., Côté, S.D., and Gunn, A. 2011. Conservation of caribou (Rangifer tarandus) in Canada: an uncertain future. Canadian Journal of Zoology 89(5): 419-434. doi:10.1139/z11-025 .

Gunn, A., Russell, D., and Eamer, J. 2011. Northern caribou population trends in Canada. Canadian Biodiversity: Ecosystem Status and Trends 2010, Technical Thematic Report No. 10. Canadian Councils of Resource Ministers. Ottawa, ON. iv + 71 p. http://www.biodivcanada.ca/default.asp?lang=En&n=137E1147-1

Hayes, B. (2010) Wolves of the Yukon. Wolves of the Yukon Publishing, Smithers, B.C. ISBN: 978-1-4566-1047-0

Hervieux, D., Hebblewhite, M., DeCesare, N.J., Russell, M., Smith, K., Robertson, S., and Boutin, S. 2013. Widespread declines in woodland caribou (Rangifer tarandus caribou) continue in Alberta. Canadian Journal of Zoology 91(12): 872-882. doi:10.1139/cjz-2013-0123.

Hervieux, D., Hebblewhite, M., Stepnisky, D., Bacon, M., and Boutin, S. 2014. Managing wolves (Canis lupus) to recover threatened woodland caribou (Rangifer tarandus caribou) in Alberta. Canadian Journal of Zoology 92(12): 1029-1037. doi:10.1139/cjz-2014-0142 .

Schaefer, J.A., and Mahoney, S.P. 2013. Spatial dynamics of the rise and fall of caribou (Rangifer tarandus) in Newfoundland. Canadian Journal of Zoology 91(11): 767-774. doi:10.1139/cjz-2013-0132 .

Wittmer, H.U., McLennan, B.N., Serrouya, R., and Apps, C.D. 2007. Changes in landscape composition influence the decline of a threatened caribou population. Journal of Animal Ecology 76: 568-579. doi: 10.1111/j.1365-2656.2007.01220.x