Category Archives: General Ecology

On Biodiversity and Ecosystem Function

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I begin with a quote from Seddon et al. (2016):

“By 2012, the consensus view based on 20 years of research was that (i) experimental reduction in species richness, at any trophic level, negatively impacts both the magnitude and stability of ecosystem functioning [12,52], and (ii) the impact of biodiversity loss on ecosystem functioning is comparable in magnitude to other major drivers of global change [13,54].”

The references are to Cardinale et al. (2012), Naeem et al. (2012), Hooper et al. (2012), and Tilman et al. (2012).

The basic conclusion of the literature cited here is that with very extensive biodiversity loss, ecosystem function such as primary productivity will be reduced. I first of all wonder which set of ecologists would doubt this. Secondly, I would like to see these papers analysed for problems of data analysis and interpretation. A good project for a graduate class in experimental design and analysis. Many of the studies I suspect are so artificial in design as to be useless for telling us what will really happen as natural biodiversity is lost. At best perhaps we can view them as political ecology to try to convince politicians and the public to do something about the true drivers of the mess, climate change and overpopulation.

Too many of the graphs I see in published papers on biodiversity and ecosystem function look like this (from Maestre et al. (2012): data from 224 global dryland plots)

There is a trend in these data but zero predictability. And even if you feel that showing trends are good enough in ecology, the trend is very weak.

Many of these analyses utilize meta-analysis. I am a critic of the philosophy of meta-analysis and not alone in wondering how useful many of these are in guiding ecological research (Vetter et al. 2013, Koricheva, and Gurevitch 2014). Perhaps the strongest division in deciding the utility of these meta-analyses is whether one is interested in general trends across ecosystems or predictability which depends largely on understanding the mechanisms behind particular trends.

Another interesting aspect of many of these analyses lies in the preoccupation with stability as a critical ecosystem function maintained by species richness. In contrast to this belief, Jacquet et al. (2016) have argued that in empirical food webs there is no simple relationship between species richness and stability, contrary to conventional theory.

Finally, another quotation from Naeem et al. (2012) which raises a critical issue on which ecologists need to focus more:

“In much of experimental ecological research, nature is seen as the complex, species-rich reference against which treatment effects are measured. In contrast, biodiversity and ecosystem functioning experiments often simply compare replicate ecosystems that differ in biodiversity, without any replicate serving as a reference to nature. Consequently, it has often been difficult to evaluate the external validity of biodiversity and ecosystem functioning research, or how its findings map onto the “real” worlds of conservation and decision making. Put another way, what light can be shed on the stewardship of nature by microbial microcosms that have no analogs in nature, or by experimental grassland studies in which some plots have, by design, no grass species? “ (page 1403)

And for those of you who are animal ecologists, the vast bulk of these studies were done on plants with none of the vertebrate browsers and grazers present. Perhaps some problems here.

Whatever one’s view of these research paradigms, no questions will be answered if we lose too much biodiversity.

Cardinale, B.J., Duffy, J.E., Gonzalez, A., Hooper, D.U., Perrings, C., Venail, P., Narwani, A., Mace, G.M., Tilman, D., Wardle, D.A., Kinzig, A.P., Daily, G.C., Loreau, M., Grace, J.B., Larigauderie, A., Srivastava, D.S. & Naeem, S. (2012) Biodiversity loss and its impact on humanity. Nature, 486, 59-67. doi: 10.1038/nature11148

Hooper, D.U., Adair, E.C., Cardinale, B.J., Byrnes, J.E.K., Hungate, B.A., Matulich, K.L., Gonzalez, A., Duffy, J.E., Gamfeldt, L. & O/’Connor, M.I. (2012) A global synthesis reveals biodiversity loss as a major driver of ecosystem change. Nature, 486, 105-108. doi: 10.1038/nature11118

Jacquet, C., Moritz, C., Morissette, L., Legagneux, P., Massol, F., Archambault, P. & Gravel, D. (2016) No complexity–stability relationship in empirical ecosystems. Nature Communications, 7, 12573. doi: 10.1038/ncomms12573

Koricheva, J. & Gurevitch, J. (2014) Uses and misuses of meta-analysis in plant ecology. Journal of Ecology, 102, 828-844. doi: 10.1111/1365-2745.12224

Maestre, F.T. et al. (2012) Plant species richness and ecosystem multifunctionality in global drylands. Science, 335, 214-218. doi: 10.1126/science.1215442

Naeem, S., Duffy, J.E. & Zavaleta, E. (2012) The functions of biological diversity in an Age of Extinction. Science, 336, 1401.

Seddon, N., Mace, G.M., Naeem, S., Tobias, J.A., Pigot, A.L., Cavanagh, R., Mouillot, D., Vause, J. & Walpole, M. (2016) Biodiversity in the Anthropocene: prospects and policy. Proceedings of the Royal Society B: Biological Sciences, 283, 20162094. doi: 10.1098/rspb.2016.2094

Tilman, D., Reich, P.B. & Isbell, F. (2012) Biodiversity impacts ecosystem productivity as much as resources, disturbance, or herbivory. Proceedings of the National Academy of Sciences 109, 10394-10397. doi: 10.1073/pnas.1208240109

Vetter, D., Rücker, G. & Storch, I. (2013) Meta-analysis: A need for well-defined usage in ecology and conservation biology. Ecosphere, 4, art74. doi: 10.1890/ES13-00062.1

On Ecological Predictions

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The gold standard of ecological studies is the understanding of a particular ecological issue or system and the ability to predict the operation of that system in the future. A simple example is the masting of trees (Pearse et al. 2016). Mast seeding is synchronous and highly variable seed production among years by a population of perennial plants. One ecological question is what environmental drivers cause these masting years and what factors can be used to predict mast years. Weather cues and plant resource states presumably interact to determine mast years. The question I wish to raise here, given this widely observed natural history event, is how good our predictive models can be on a spatial and temporal scale.

On a spatial scale masting events can be widespread or localized, and this provides some cues to the important weather variables that might be important. Assuming we can derive weather models for prediction, we face two often unknown constraints – space and time. If we can derive a weather model for trees in New Zealand, will it also apply to trees in Australia or California? Or on a more constrained geographical view, if it applied on the South Island of New Zealand will it also apply on the North Island? At the other extreme, must we derive models for every population of particular plants in different areas, so that predictability is spatially limited? We hope not and work on the assumption of more spatial generality than what we can measure on our particular small study areas.

The temporal stability of our explanations is now particularly worrisome because of climate change. If we have a good model of masting for a particular tree species in 2017, will it still be working in 2030, 2050 or 2100? A physicist would never ask such a question since a “scientific law” is independent of time. But biology in general and ecology in particular is not time independent both because of evolution and now in particular because of changing climate. But we have not faced up to whether or not we must check our “ecological laws” over and over again as the environment changes, and if we have to do this what must the time scale of rechecking be? Perhaps this question can be answered by determining the speed of potential evolutionary change in species groups. If virus diseases can evolve quickly in terms of months or years, we must be eternally vigilant to consider if the flu virus of 2017 is going to be the same as that of 2016. We should not stop virus research and say that we have sorted out some universal model that will become an equivalent of the laws of physics.

The consequences of these simple observations are not simple. One consequence is the implication that monitoring is an essential ecological activity. But in most ecological funding agencies monitoring is thought to be unscientific, not leading to progress, and more stamp collecting. So we have to establish that, like the Weather Bureau every country supports, we must have an equivalent ecological monitoring bureau. We do have these bureaus for some ecological systems that make money, like marine fisheries, but most other ecosystems are left in limbo with little or no funding on the generalized assumption that “mother or father nature will take care of itself” or expressed more elegantly by a cabinet minister who must be nameless, “there is no need for more forestry research, as we know everything we need to know already”. The urge by politicians to cut research funding lives too much in environmental research.

But ecologists are not just ‘stamp collectors’ as some might think. We need to develop generality but at a time scale and a spatial scale that is reliable and useful for the resolution of the problem that gave rise to the research. Typically for ecological issues this time scale would be 10-25 years, and a rule of thumb might be for 10 generations of the organisms being studied. For many of our questions an annual scale might be most useful, but for long-lived plants and animals we must be thinking of decades or even centuries. Some practical examples from Pacifici et al. (2013): If you study field voles (Microtus spp.) typically you can complete your studies of 10 generations in 3.5 years (on average). If you study red squirrels (Tamiasciurus hudsonicus), the same 10 generations will cost you 39 years, and if red foxes (Vulpes vulpes) 58 years. If wildebeest (Connochaetes taurinus) in the Serengeti, 10 generations will take you 80 years, and if you prefer red kangaroos (Macropus rufus) it will take about 90 years. All these estimates are very approximate but they give you an idea of what the time scale of a long-term study might be. Except for the rodent example, all these study durations are nearly impossible to achieve, and the question for ecologists is this: Should we be concerned about these time scales, or should we scale everything to the human research time scale?

The spatial scale has expanded greatly for ecologists with the advent of radio transmitters and the possibility of satellite tracking. These technological advances allow many conservation questions regarding bird migration to be investigated (e.g. Oppel et al. 2015). But no matter what the spatial scale of interest in a research or management program, variation among individuals and sites must be analyzed by means of the replication of measurements or manipulations at several sites. The spatial scale is dictated by the question under investigation, and the issue of fragmentation has focused attention on the importance of spatial movements both for ecological and evolutionary questions (Betts et al. 2014).

And the major question remains: can we construct an adequate theory of ecology from a series of short-term, small area or small container studies?

Betts, M.G., Fahrig, L., Hadley, A.S., Halstead, K.E., Bowman, J., Robinson, W.D., Wiens, J.A. & Lindenmayer, D.B. (2014) A species-centered approach for uncovering generalities in organism responses to habitat loss and fragmentation. Ecography, 37, 517-527. doi: 10.1111/ecog.00740

Oppel, S., Dobrev, V., Arkumarev, V., Saravia, V., Bounas, A., Kret, E., Velevski, M., Stoychev, S. & Nikolov, S.C. (2015) High juvenile mortality during migration in a declining population of a long-distance migratory raptor. Ibis, 157, 545-557. doi: 10.1111/ibi.12258

Pacifici, M., Santini, L., Di Marco, M., Baisero, D., Francucci, L., Grottolo Marasini, G., Visconti, P. & Rondinini, C. (2013) Database on generation length of mammals. Nature Conservation, 5, 87-94. doi: 10.3897/natureconservation.5.5734

Pearse, I.S., Koenig, W.D. & Kelly, D. (2016) Mechanisms of mast seeding: resources, weather, cues, and selection. New Phytologist, 212 (3), 546-562. doi: 10.1111/nph.14114

Ecological Alternative Facts

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It has become necessary to revise my recent ecological thinking about the principles of ecology along the lines now required in the New World Order. I list here the thirteen cardinal principles of the new ecology 2017:

  1. Population growth is unlimited and is no longer subject to regulation.
  2. Communities undergo succession to the final equilibrium state of the 1%.
  3. Communities and ecosystems are resilient to any and all disturbances and operate best when challenged most strongly, for example with oil spills.
  4. Resources are never limiting under any conditions for the 1% and heavy exploitation helps them to trickle down readily to assist the other 99%.
  5. Overexploiting populations is good for the global ecosystem because it gets rid of the species that are wimps.
  6. Mixing of faunas and floras have been shown over the last 300 years to contribute to the increasing ecological health of Earth.
  7. Recycling is unnecessary in view of recent advances in mining technology.
  8. Carbon dioxide is a valuable resource for plants and we must increase its contribution to atmospheric chemistry.
  9. Climate change is common and advantageous since it occurs from night to day, and has always been with us for many millions of years.
  10. Evolution maximizes wisdom and foresight, especially in mammals.
  11. Conservation of less fit species is an affront to alternative natural laws that were recognized during the 18th century and are now mathematically defined in the new synthetic theory of economic and ecological fitness.
  12. Scientific experiments are no longer necessary because we have computers and technological superiority.
  13. Truth in science is no longer necessary and must be balanced against equally valid post-truth beliefs.

The old ecology, now superseded, was illustrated in Krebs (2016), and is already out of date. Recommendations for other alternative ecological facts will be welcome. Please use the comments.

Krebs, C.J. (2016) Why Ecology Matters. University of Chicago Press, Chicago. 208 pp.

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

On Mushrooms, Monitoring, and Prediction

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Mushrooms probably run the world but we do not know this yet. My old friend Jim Trappe from Oregon State told me this long ago, and partly as a result of this interaction we began counting mushrooms at our boreal forest sites near Kluane, Yukon in 1993, long ago and even before the iPhone was invented. Being zoologists, we never perhaps appreciated mushrooms in the forest, but we began counting and measuring mushrooms appearing above ground on circular plots of 28m2. With the help of many students, we have counted about 12,000 plots over 24 years, even after being told by one Parks Canada staff member that they could not assist us because “real men do not count mushrooms”. At least we know our position in life.

At any rate the simple question we wanted to ask is whether we can predict mushroom crops one year ahead. We know that many species eat these mushrooms, from red squirrels (who dry mushrooms on spruce tree branches so they can be stored for later consumption), to moose (Alice Kenney has photographed them kneeling down to munch mushrooms), to caribou (Art Rodgers has videoed) to small rodents and insects, not to mention Yukon residents. We know from natural history observations that mushroom crops in the boreal forest are highly variable from year to year, ranging from 0.1 to 110 g/10m2 wet weight, for a CV of 138% (Krebs et al. 2008). The question is how best to predict what the crop will be next year.  Why do we want to know next year’s crop? Two reasons are that large crops provide food for many animals and thus affect overall ecosystem dynamics, and secondly that the essence of understanding in science is the ability to understand why changes occur and if possible to be able to predict them.

We assume it has to be driven by climate, so we can gather together climate data and it is here that the questions arise as to how to proceed. At one extreme we can gather annual temperatures and annual rainfall, and at the other extreme we can gather daily rainfall. We first make the assumption that it is only the weather during the summer from May to August that is relevant for our statistical model, so annual data are not useful. But then we are faced with a nearly infinite number of possible weather variables. We have chosen months as the relevant weather grouping and so we tally May temperature averages, May rainfall totals, growing degree days above 5°C, etc. for all the years involved. This leads us into a statistical nightmare of having far more independent variables than measurements of mushroom crops. If we have, for example, 15 possible measures of temperature and rainfall we can generate 32,768 models ignoring all the interactive models. There are several standard ways of dealing with this statistical dilemma, with stepwise regression being the old fashioned approach. But new methods and advice continue to appear (e.g. Elith et al. 2008, Ives 2015). The ability to compare different regression models with the AIC approach helps (Anderson 2008) as long as there is some biological basis to the models.

We adopted a natural history approach, given that many people believe that large mushroom crops are associated with above average rainfall. We are blessed in the Yukon with only one possible crop of mushrooms per year (at least for the present), so that also simplifies the kinds of models one might use. At any rate (as of 2016) the simplest regression model to predict mushroom biomass in a particular year turned out to involve only rainfall from May (early spring) of the previous year, with R2 = 0.55. But this success has just led us into more questions of why we cannot find a model that will explain the remaining 45% of the variance in annual crops. Should one just give up at this point and be happy that we can explain a large part of the annual variation, or should one press on doing more modelling and looking for other variables? Data dredging is more and more becoming an issue in the ecological literature, and in particular in ecological events likely to be at least partly associated with climate (Norman 2014).

Another ecological problem has been that we do not identify the species of mushrooms involved and deal only in biomass. It may be that species identification would help us to improve predictability. But there are perhaps 40 or more species of mushrooms in our part of the boreal forest, and so we now have to become mycologists. And then as Jim Trappe would tell me, all of this ignores the important questions of what is going on with these fungi underground, so we have only scratched the surface.

The next question is how long a predictive model based on weather will continue to hold in an area subject to rapid climate change. Climate change in the southern Yukon is relatively rapid but highly variable from year to year, and only continuing monitoring will keep us informed about how the physical measurements of temperature and rainfall translate into events in the biological world.

All of this is to say that counting and measuring mushrooms is enjoyable and keeps one connected to the real world. It is also a free type of good exercise, and part of citizen science. Continued monitoring is necessary to see how the boreal ecosystem responds to changing climate and to see if good years for mushroom crops become more frequent. And in good years, many kinds of mushrooms are good to eat if you can beat the squirrels to them.

Anderson, D.R. (2008) Model Based Inference in the Life Sciences: A Primer on Evidence. Springer, New York. ISBN: 978-0-387-74073-7

Elith, J., Leathwick, J.R. & Hastie, T. (2008) A working guide to boosted regression trees. Journal of Animal Ecology, 77, 802-813. doi: 10.1111/j.1365-2656.2008.01390.x

Ives, A.R. (2015) For testing the significance of regression coefficients, go ahead and log-transform count data. Methods in Ecology and Evolution, 6, 828-835. doi: 10.1111/2041-210X.12386

Krebs, C.J., Carrier, P., Boutin, S., Boonstra, R. & Hofer, E.J. (2008) Mushroom crops in relation to weather in the southwestern Yukon. Botany, 86, 1497-1502. doi: 10.1139/B08-094

Norman, G.G. (2014) Data dredging, salami-slicing, and other successful strategies to ensure rejection: twelve tips on how to not get your paper published. Advances in Health Sciences Education, 19, 1-5. doi: 10.1007/s10459-014-9494-8

Technology Can Lead Us Astray

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Our iPhones teach us very subtly to have great faith in technology. This leads the public at large to think that technology will solve large issues like greenhouse gases and climate change. But for scientists we should remember that technology must be looked at very carefully when it tells us we have a shortcut to ecological measurement and understanding. For the past 35 years satellite data has been available to calculate an index of greening for vegetation from large landscapes. The available index is called NDVI, normalized difference vegetation index, and is calculated as a ratio of near infrared light to red light reflected from the vegetation being surveyed. I am suspicious that NDVI measurements tell ecologists anything that is useful for the understanding of vegetation dynamics and ecosystem stability. Probably this is because I am focused on local scale events and landscapes of hundreds of km2 and in particular what is happening in the forest understory. The key to one’s evaluation of these satellite technologies most certainly lies in the questions under investigation.

A whole array of different satellites have been used to measure NDVI and since the more recent satellites have different precision and slightly different physical characteristics, there is some problem of comparing results from different satellites in different years if one wishes to study long-term trends (Guay et al. 2014). It is assumed that NDVI measurements can be translated into aboveground net primary production and can be used to start to answer ecological questions about seasonal and annual changes in primary production and to address general issues about the impact of rising CO2 levels on ecosystems.

All inferences about changes in primary production on a broad scale hinge on the reliability of NDVI as an accurate measure of net primary production. Much has been written about the use of NDVI measures and the need for ground truthing. Community ecologists may be concerned about specific components of the vegetation rather than an overall green index, and the question arises whether NDVI measures in a forest community are able to capture changes in both the trees and the understory, or for that matter in the ground vegetation. For overall carbon capture estimates, a greenness index may be accurate enough, but if one wishes to determine whether deciduous trees are replacing evergreen trees, NDVI may not be very useful.

How can we best validate satellite based estimates of primary productivity? To do this on a landscape scale we need to have large areas with ground truthing. Field crops are one potential source of such data. Kang et al. (2016) used crops to quantify the relationship between remotely sensed leaf-area index and other satellite measures such as NDVI. The relationships are clear in a broad sense but highly variable in particular, so that the ability to predict crop yields from satellite data at local levels is subject to considerable error. Johnson (2016, Fig. 6, p. 75) found the same problem with crops such as barley and cotton (see sample data set below). So there is good news and bad news from these kinds of analyses. The good news is that we can have extensive global coverage of trends in vegetation parameters and crop production, but the bad news is that at the local level this information may not be helpful for studies that require high precision for example in local values of net primary production. Simply to assume that satellite measures are accurate measures of ecological variables like net aboveground primary production is too optimistic at present, and work continues on possible improvements.

Many of the critical questions about community changes associated with climate change cannot in my opinion be answered by remote sensing unless there is a much higher correlation of ground-based research that is concurrent with satellite imagery. We must look critically at the available data. Blanco et al. (2016) for example compared NDVI estimates from MODIS satellite data with primary production monitored on the ground in harvested plots in western Argentina. The regression between NDVI and estimated primary production had R2 values of 0.35 for the overall annual values and 0.54 for the data restricted to the peak of annual growth. Whether this is a satisfactory statistical association is up to plant ecologists to decide. I think it is not, and the substitution of p values for the utility of such relationships is poor ecology. Many more of these kind of studies need to be carried out.

The advent of using drones for very detailed spectral data on local study areas will open new opportunities to derive estimates of primary production. For the present I think we should be aware that NDVI and its associated measures of ‘greenness’ from satellites may not be a very reliable measure for local or landscape values of net primary production. Perhaps it is time to move back to the field and away from the computer to find out what is happening to global plant growth.

Blanco, L.J., Paruelo, J.M., Oesterheld, M., and Biurrun, F.N. 2016. Spatial and temporal patterns of herbaceous primary production in semi-arid shrublands: a remote sensing approach. Journal of Vegetation Science 27(4): 716-727. doi: 10.1111/jvs.12398.

Guay, K.C., Beck, P.S.A., Berner, L.T., Goetz, S.J., Baccini, A., and Buermann, W. 2014. Vegetation productivity patterns at high northern latitudes: a multi-sensor satellite data assessment. Global Change Biology 20(10): 3147-3158. doi: 10.1111/gcb.12647.

Johnson, D.M. 2016. A comprehensive assessment of the correlations between field crop yields and commonly used MODIS products. International Journal of Applied Earth Observation and Geoinformation 52(1): 65-81. doi: 10.1016/j.jag.2016.05.010.

Kang, Y., Ozdogan, M., Zipper, S.C., Roman, M.O., and Walker, J. 2016. How universal Is the relationship between remotely sensed vegetation Indices and crop leaf area Index? A global assessment. Remote Sensing 2016 8(7): 597 (591-529). doi: 10.3390/rs8070597.

Cotton yield vs NDVI Index

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

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