Category Archives: Evaluating Research Quality

On Declining Bird Populations

The conservation literature and the media are alive with cries of declining bird populations around the world (Rosenberg et al. 2019). Birds are well liked by people, and an important part of our environment so they garner a lot of attention when the cry goes out that all is not well. The problems from a scientific perspective is what evidence is required to “cry wolf’. There are many different opinions on what data provide reliable evidence. There is a splendid critique of the Rosenberg et al paper by Brian McGill that you should read::
https://dynamicecology.wordpress.com/2019/09/20/did-north-america-really-lose-3-billion-birds-what-does-it-mean/

My object here is to add a comment from the viewpoint of population ecology. It might be useful for bird ecologists to have a brief overview of what ecological evidence is required to decide that a bird population or a bird species or a whole group of birds is threatened or endangered. One simple way to make this decision is with a verbal flow chart and I offer here one example of how to proceed.

  1. Get accurate and precise data on the populations of interest. If you claim a population is declining or endangered, you need to define the population and know its abundance over a reasonable time period.

Note that this is already a nearly impossible demand. For birds that are continuously resident it is possible to census them well. Let me guess that continuous residency occurs in at most 5% or fewer of the birds of the world. The other birds we would like to protect are global or local migrants or move unpredictably in search of food resources, so it is difficult to define a population and determine if the population as a whole is rising or falling. Compounding all this are the truly rare bird species that are difficult to census like all rare species. Dorey and Walker (2018) examine these concerns for Canada.

The next problem is what is a reasonable time period for the census data. The Committee on the Status of Endangered Wildlife in Canada (COSEWIC) gives 10 years or 3 generations, whichever is longer (see web link below). So now we need to know the generation time of the species of concern. We can make a guess at generation time but let us stick with 10 years for the moment. For how many bird species in Canada do we have 10 years of accurate population estimates?

  • Next, we need to determine the causes of the decline if we wish to instigate management actions. Populations decline because of a falling reproductive rate, increasing death rate, or higher emigration rates. There are very few birds for which we have 10 years of diagnosis for the causes of changes in these vital rates. Strong conclusions should not rest on weak data.

The absence of much of these required data force conservation biologists to guess about what is driving numbers down, knowing only that population numbers are falling. Typically, many things are happening over the 10 years of assessment – climate is changing, habitats are being lost or gained, invasive species are spreading, new toxic chemical are being used for pest control, diseases are appearing, the list is long. We have little time or money to determine the critical limiting factors. We can only make a guess.

  • At this stage we must specify an action plan to recommend management actions for the recovery of the declining bird population. Management actions are limited. We cannot in the short term alter climate. Regulating toxic chemical use in agriculture takes years. In a few cases we can set aside more habitat as a generalized solution for all declining birds. We have difficulty controlling invasive species, and some invasive species might be native species expanding their geographic range (e.g. Bodine and Capaldi 2017, Thibault et al. 2018).

Conservation ecologists are now up against the wall because all management actions that are recommended will cost money and will face potential opposition from some people. Success is not guaranteed because most of the data available are inadequate. Medical doctors face the same problem with rare diseases and uncertain treatments when deciding how to treat patients with no certainty of success.

In my opinion the data on which the present concern over bird losses is too poor to justify the hyper-publicity about declining birds. I realize most conservation biologists will disagree but that is why I think we need to lift our game by having a more rigorous set of data rules for categories of concern in conservation. A more balanced tone of concern may be more useful in gathering public support for management efforts. Stanton et al. (2018) provide a good example for farmland birds. Overuse of the word ‘extinction’ is counterproductive in my opinion. Trying to provide better data is highly desirable so that conservation papers do not always end with the statement ‘but detailed mechanistic studies are lacking’. Pleas for declining populations ought to be balanced by recommendations for solutions to the problem. Local solutions are most useful, global solutions are critical in the long run but given current global governance are too much fairy tales.

Bodine, E.N. and Capaldi, A. (2017). Can culling Barred Owls save a declining Northern Spotted Owl population? Natural Resource Modeling 30, e12131. doi: 10.1111/nrm.12131.

Dorey, K. and Walker, T.R. (2018). Limitations of threatened species lists in Canada: A federal and provincial perspective. Biological Conservation 217, 259-268. doi: 10.1016/j.biocon.2017.11.018.

Rosenberg, K.V., et al. (2019). Decline of the North American avifauna. Science 366, 120-124. doi: 10.1126/science.aaw1313.

Stanton, R.L., Morrissey, C.A., and Clark, R.G. (2018). Analysis of trends and agricultural drivers of farmland bird declines in North America: A review. Agriculture, Ecosystems & Environment 254, 244-254. doi: 10.1016/j.agee.2017.11.028.

Thibault, M., et al. (2018). The invasive Red-vented bulbul (Pycnonotus cafer) outcompetes native birds in a tropical biodiversity hotspot. PLoS ONE 13, e0192249. doi: 10.1371/journal.pone.0192249.

http://cosewic.ca/index.php/en-ca/assessment-process/wildlife-species-assessment-process-categories-guidelines/quantitative-criteria

On Progress in Ecology

We are in ecology continually discussing what progress we are making in answering the central questions of our science. For this reason, it is sometimes interesting to compare our situation with that of economics, the queen of the social sciences, where the same argument also continues. A review by David Graeber (2019) in the New York Review of Books contains some comments about the ‘theoretical war’ in economics that might apply to some ecology subdisciplines. In it he discusses the arguments in social science between two divergent views of economics, that of the school of Keynesians and that of the now dominant Neoclassical School led by Frederich Hayek and later by Milton Friedman and many others of the Chicago School. John Maynard Keynes threw down a challenge illustrated in this quote from Graeber (2019):

“In other words, ‘(Keynes)’ assumed that the ground was always shifting under the analysts’ feet; the object of any social science was inherently unstable. Max Weber, for similar reasons, argued that it would never be possible for social scientists to come up with anything remotely like the laws of physics, because by the time they had come anywhere near to gathering enough information, society itself, and what analysts felt was important to know about it, would have changed so much that the information would be irrelevant. (p. 57)”

Precise quantitative predictions could be provided by simplified economic models, the Chicago School argued in rebutting Keynes. Graeber (2019) comments:

“Surely there’s nothing wrong with creating simplified models. Arguably, this is how any science of human affairs has to proceed. But an empirical science then goes on to test those models against what people actually do, and adjust them accordingly. This is precisely what economists did not do. Instead, they discovered that, if one encased those models in mathematical formulae completely impenetrable to the noninitiate, it would be possible to create a universe in which those premises could never be refuted. (“All actors are engaged in the maximization of utility. What is utility? Whatever it is that an actor appears to be maximizing.”) The mathematical equations allowed economists to plausibly claim theirs was the only branch of social theory that had advanced to anything like a predictive science.  (p. 57)”

In ecology the major divergence between schools of thought promoting progress have never been quite this distinct. Shades of complaint are evident in the writings of Peters (1991) and a burst of comment after that ranged from optimism (e.g. Bibby 2003) to more support for Peter’s critique (Underwood et al. 2000, Graham and Dayton 2002). Interest at this time seems to have waned in favour of very specific topics for review. If you check the Web of Science for the last 5 years for “progress” and “ecology” you will find reviews of root microbes, remote sensing of the carbon cycle, reintroduction of fishes in Canada and a host of very important reviews of small parts of the broad nature of ecology. As Kingsland (2004, 2005) recognized, ecology is an integrating science that brings together data from diverse fields of study. If this is correct, it is not surprising that ecologists differ in answering questions about progress in ecology. We should stick to small specific problems on which we can make detailed studies, measurements, and experiments to increase understanding of the causes of the original problem.

One of the most thoughtful papers on progress in ecology was that of Graham and Dayton (2002) who made an important point about progress in ecology:

“We believe that many consequences of ecological advancement will be obstacles to future progress. Here we briefly discuss just a few: (1) ecological specialization; (2) erasure of history; and (3) expansion of the literature. These problems are interconnected and have the potential to divert researchers and hinder ecological breakthroughs.” (p. 1486)

My question to all ecologists is whether or not we agree with this ‘prediction’ from 2002. There is no question in my judgement that ecology is much more specialized now, that history is erased in spite of search engines like the Web of Science and that the ecology literature is booming so rapidly that it feeds back to ecological specialization. There is no clear solution to these problems. The fact that ecology is integrative has developed into a belief that anyone with a little training in ecological science can call themselves an ecologist and pontificate about the problems of our day. This element of ‘fake news’ is not confined to ecology and we can counter it only by calling out errors propagated by politicians and others who continue to confuse truth in science with their uneducated beliefs.

Bibby, C.J. (2003). Fifty years of Bird Study. Bird Study 50, 194-210. Doi: 10.1080/00063650309461314.

Graham, M.H. and Dayton, P.K. (2002). On the evolution of ecological ideas: paradigms and scientific progress. Ecology 83, 1481-1489. Doi: 10.1890/0012-9658(2002)083[1481:OTEOEI]2.0.CO;2.

Graeber, D. (2019). Against Economics. New York Review of Books 66, 52-58. December 5, 2019.

Kingsland, S. (2004). Conveying the intellectual challenge of ecology: an historical perspective. Frontiers in Ecology and the Environment 2, 367-374. Doi: 10.1890/1540-9295(2004)002[0367:CTICOE]2.0.CO;2.

Kingsland, S.E. (2005) The Evolution of American Ecology, 1890-2000. Johns Hopkins University Press: Baltimore. 313 pp. ISBN 0801881714

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

Underwood, A.J., Chapman, M.G., and Connell, S.D. (2000). Observations in ecology: you can’t make progress on processes without understanding the patterns. Journal of Experimental Marine Biology and Ecology 250, 97-115. Doi: 10.1016/S0022-0981(00)00181-7.

On Christmas Holiday Wishes

We are all supposed to make some wishes over the Holiday Season, no matter what our age or occupation. So, this blog is in that holiday spirit with the constraint that I will write about ecology, rather than the whole world, to keep it short and specific. So, here are my 12 wishes for improving the science of ecology in 2020:

  1. When you start your thesis or study, write down in 50 words or less what is the problem, what are the possible solutions to this problem, and what can we do about it.
  2. Take this statement and convert it to a 7 second sound bite that points out clearly for the person on the street or the head of the Research Council why this is an important use of the foundation’s or taxpayers’ money.
  3. Read the literature that is available on your topic of study even if it was published in the last century.
  4. When writing your report, thesis, or paper on your research, prepare an abstract or summary that follows the old rules of stating clearly WHO, WHAT, WHEN, WHERE, WHY, and HOW. Spend much time on this step, since many of your readers will only be able to read this far. 
  5. Make tables and graphs that are clear and to the point. Define the points or histograms on a graph.
  6. Define all three- and four-letter acronyms. Not everyone will know what RSE or SECR means.
  7. Remember the cardinal rule of data presentation that if your data are an estimate of some value, you should provide the confidence limits or credible intervals of your data.
  8. Above all be truthful and modest in your conclusions. If your evidence points in one direction but is weak, say so. If the support of your evidence is strong, say so. But do not say that this is the first time anyone has ever suggested your conclusions.
  9. In the discussion of your results, give some space to suggesting what limits apply to your conclusions. Do your statements apply only to brown trout, or to all trout, or to all freshwater fish? Are your conclusions limited to one biogeographic zone, or one plant community, or to one small national park?  
  10. The key point at the end of your report should be what next? You or others will take up your challenges, and since you have worked hard and thought much about the ecological problems you have faced, you should be the best person to suggest some future directions for research.
  11. Once your have completed your report or paper, go back and read again all the literature that is available on your topic of study and review it critically.
  12. Finish your report or paper, keeping in mind the old adage, the perfect is the enemy of the good. It is quite impossible in science to be perfect. Better good than perfect.

And as you dive into any kind of biological research, it is useful to read about some of the controversies that you may run into as you write your papers or reports, particularly in the statistical treatment of biological data (Hardwicke and Ioannidis 2019, Ioannidis 2019). The statistical controversy over p-values has been a hot issue for several years and you will likely run into it sooner or later (Ioannidis 2019a, Siontis and Ioannidis 2018). The important point you should remember is that ecologists are scientists and our view of the value of our research work is the antithesis of Shakespeare’s Macbeth:

Life’s but a walking shadow, a poor player that struts and frets his hour upon the stage, and then is heard no more. It is a tale told by an idiot, full of sound and fury,
signifying nothing.”
(Act 5, Scene 5)

This is because our scientific work is valuable for conserving life on Earth, and so it must be carried out to a high and improving standard. It will be there as a contribution to knowledge and available for a long time. It may be useful now, or in one year, or perhaps in 10 or 100 years as an important contribution to solving ecological problems. So, we should strive for the best.

Hardwicke, T.E. and Ioannidis, J.P.A. (2019). Petitions in scientific argumentation: Dissecting the request to retire statistical significance. European Journal of Clinical Investigation 49, e13162.  doi: 10.1111/eci.13162.

Ioannidis, J.P.A. (2019). Options for publishing research without any P-values. European Heart Journal 40, 2555-2556. doi: 10.1093/eurheartj/ehz556.

Ioannidis, J.P.A. (2019a Ioannidis). What have we (not) learnt from millions of scientific papers with P values? American Statistician 73, 20-25. doi: 10.1080/00031305.2018.1447512.

Siontis, K.C. and Ioannidis, J.P.A. (2018). Replication, duplication, and waste in a quarter million systematic reviews and meta-analyses. Circulation: Cardiovascular Quality and Outcomes 11, e005212. doi: 10.1161/CIRCOUTCOMES.118.005212.

Is Conservation Ecology Destroying Ecology?

Ecology became a serious science some 100 years ago when the problems that it sought to understand were clear and simple: the reasons for the distribution and abundance of organisms on Earth. It subdivided fairly early into three parts, population, community, and ecosystem ecology. It was widely understood that to understand population ecology you needed to know a great deal about physiology and behaviour in relation to the environment, and to understand community ecology you had to know a great deal about population dynamics. Ecosystem ecology then moved into community ecology plus all the physical and chemical interactions with the whole environment. But the sciences are not static, and ecology in the past 60 years has come to include nearly everything from chemistry and geography to meteorological sciences, so if you tell someone you are an ‘ecologist’ now, they have only a vague idea of what you do.

The latest invader into the ecology sphere has been conservation biology so that in the last 20 years it has become a dominant driver of ecological concerns. This has brought ecology into the forefront of publicity and the resulting political areas of controversy, not necessarily bad but with some scientific consequences. ‘Bandwagons’ are for the most part good in science because it attracts good students and professors and brings public support on side. Bandwagons are detrimental when they draw too much of the available scientific funding away from critical basic research and champion scientific fads.

The question I wish to raise is whether conservation ecology has become the latest fad in the broad science of ecology and whether this has derailed important background research. Conservation science begins with the broad and desirable goal of preserving all life on Earth and thus thwarting extinctions. This is an impossible goal and the question then becomes how can we trim it down to an achievable scientific aim? We could argue that the most important goal is to describe all the species on Earth, so that we would then know what “money” we have in the “bank”. But if we look at the insects alone, we see that this is not an achievable goal in the short term. And the key to many of these issues is what we mean by “the short term”. If we are talking10 years, we may have very specific goals, if 100 years we may redesign the goal posts, and if 1000 years again our views might change.

This is a key point. As humans we design our goals in the time frames of months and a few years, not in general in geological time. Because of climate change we are now being forced to view many things in a shorter and shorter time frame. If you live in Miami, you should do something about sea level rise now. If you grow wheat in Australia, you should worry about decreasing annual rainfall. But science in general does not have a time frame. Technology does, and we need a new phone every year, but the understanding of cancer or the ecology of tropical rain forests does not have a deadline.

But conservation biology has a ticking clock called extinction. Now we can compound our concerns about climate change and conservation to capture more of the funding for biological research in order to prevent extinctions of rare and endangered species. 

Ecological science over the past 40 years has been progressing slowly through population ecology into community and ecosystem ecology while learning that the details of populations are critical to the understanding of community function and learning how communities operate is necessary for understanding ecosystem change. None of this has been linear progress but rather a halting progression with many deviations and false leads. In order to push this agenda forward more funding has clearly been needed because teams of researchers are needed to understand a community and even more people to study an ecosystem. At the same time the value of long-term studies has become evident and equipment has become more expensive.

We have now moved into the Anthropocene in which in my opinion the focus has shifted completely from trying to answer the primary problems of ecological science to the conservation of organisms. In practice this has too often resulted in research that could only be called poor population ecology. Poor in the sense of the need for immediate short-term answers for declining species populations with no proper understanding of the underlying problem. We are faced with calls for funding that are ‘crying wolf’ with inadequate data but heartfelt opinions. Recovery plans for single species or closely related groups focus on a set of unstudied opinions that may well be correct, but to test these ideas in a reliable scientific manner would take years. Triage on a large scale is practiced without discussing the issue, and money is thrown at problems based on the publicity generated. Populations of threatened species continue to decline in what can only be described as failed management. Blame is spread in all directions to developers or farmers or foresters or chemical companies. I do not think these are the signs of a good science which above all ought to work from the strength of evidence and prepare recovery plans based on empirical science.

Part of the problem I think lies in the modern need to ‘do something’, ‘do anything’ to show that you care about a particular problem. ‘We have now no time for slow-moving conventional science, we need immediate results now’. Fortunately, many ecologists are critical of these undesirable trends in our science and carry on (e.g. Amos et al. 2013). You will not likely read tweets about these people or read about them in your daily newspapers. Evidence-based science is rarely quick, and complaints like those that I give here are not new (Sutherland et al. 2004, Likens 2010, Nichols 2012).  

Amos, J.N., Balasubramaniam, S., Grootendorst, L. et al. (2013). Little evidence that condition, stress indicators, sex ratio, or homozygosity are related to landscape or habitat attributes in declining woodland birds. Journal of Avian Biology 44, 45-54. doi: 10.1111/j.1600-048X.2012.05746.x

Likens, G.E. (2010). The role of science in decision making: does evidence-based science drive environmental policy? Frontiers in Ecology and the Environment 8, e1-e9. doi: 10.1890/090132

Nichols, J.D. (2012). Evidence, models, conservation programs and limits to management. Animal Conservation 15, 331-333. doi: 10.1111/j.1469-1795.2012.00574.x

Sutherland, W.J., Pullin, A.S., Dolman, P.M., Knight, T.M. (2004). The need for evidence-based conservation. Trends in Ecology and Evolution 19, 305-308. doi: 10.1016/j.tree.2004.03.018

On Questionable Research Practices

Ecologists and evolutionary biologists are tarred and feathered along with many scientists who are guilty of questionable research practices. So says this article in “The Conservation” on the web:
https://theconversation.com/our-survey-found-questionable-research-practices-by-ecologists-and-biologists-heres-what-that-means-94421?utm_source=twitter&utm_medium=twitterbutton

Read this article if you have time but here is the essence of what they state:

“Cherry picking or hiding results, excluding data to meet statistical thresholds and presenting unexpected findings as though they were predicted all along – these are just some of the “questionable research practices” implicated in the replication crisis psychology and medicine have faced over the last half a decade or so.

“We recently surveyed more than 800 ecologists and evolutionary biologists and found high rates of many of these practices. We believe this to be first documentation of these behaviours in these fields of science.

“Our pre-print results have certain shock value, and their release attracted a lot of attention on social media.

  • 64% of surveyed researchers reported they had at least once failed to report results because they were not statistically significant (cherry picking)
  • 42% had collected more data after inspecting whether results were statistically significant (a form of “p hacking”)
  • 51% reported an unexpected finding as though it had been hypothesised from the start (known as “HARKing”, or Hypothesising After Results are Known).”

It is worth looking at these claims a bit more analytically. First, the fact that more than 800 ecologists and evolutionary biologists were surveyed tells you nothing about the precision of these results unless you can be convinced this is a random sample. Most surveys are non-random and yet are reported as though they are a random, reliable sample.

Failing to report results is common in science for a variety of reasons that have nothing to do with questionable research practices. Many graduate theses contain results that are never published. Does this mean their data are being hidden? Many results are not reported because they did not find an expected result. This sounds awful until you realize that journals often turn down papers because they are not exciting enough, even though the results are completely reliable. Other results are not reported because the investigator realized once the study is complete that it was not carried on long enough, and the money has run out to do more research. One would have to have considerable detail about each study to know whether or not these 64% of researchers were “cherry picking”.

Alas the next problem is more serious. The 42% who are accused of “p-hacking” were possibly just using sequential sampling or using a pilot study to get the statistical parameters to conduct a power analysis. Any study which uses replication in time, a highly desirable attribute of an ecological study, would be vilified by this rule. This complaint echos the statistical advice not to use p-values at all (Ioannidis 2005, Bruns and Ioannidis 2016) and refers back to complaints about inappropriate uses of statistical inference (Armhein et al. 2017, Forstmeier et al. 2017). The appropriate solution to this problem is to have a defined experimental design with specified hypotheses and predictions rather than an open ended observational study.

The third problem about unexpected findings hits at an important aspect of science, the uncovering of interesting and important new results. It is an important point and was warned about long ago by Medewar (1963) and emphasized recently by Forstmeier et al. (2017). The general solution should be that novel results in science must be considered tentative until they can be replicated, so that science becomes a self-correcting process. But the temptation to emphasize a new result is hard to restrain in the era of difficult job searches and media attention to novelty. Perhaps the message is that you should read any “unexpected findings” in Science and Nature with a degree of skepticism.

The cited article published in “The Conversation” goes on to discuss some possible interpretations of what these survey results mean. And the authors lean over backwards to indicate that these survey results do not mean that we should not trust the conclusions of science, which unfortunately is exactly what some aspects of the public media have emphasized. Distrust of science can be a justification for rejecting climate change data and rejecting the value of immunizations against diseases. In an era of declining trust in science, these kinds of trivial surveys have shock value but are of little use to scientists trying to sort out the details about how ecological and evolutionary systems operate.

A significant source of these concerns flows from the literature that focuses on medical fads and ‘breakthroughs’ that are announced every day by the media searching for ‘news’ (e.g. “eat butter”, “do not eat butter”). The result is almost a comical model of how good scientists really operate. An essential assumption of science is that scientific results are not written in stone but are always subject to additional testing and modification or rejection. But one result is that we get a parody of science that says “you can’t trust anything you read” (e.g. Ashcroft 2017). Perhaps we just need to repeat to ourselves to be critical, that good science is evidence-based, and then remember George Bernard Shaw’s comment:

Success does not consist in never making mistakes but in never making the same one a second time.

Amrhein, V., Korner-Nievergelt, F., and Roth, T. 2017. The earth is flat (p > 0.05): significance thresholds and the crisis of unreplicable research. PeerJ  5: e3544. doi: 10.7717/peerj.3544.

Ashcroft, A. 2017. The politics of research-Or why you can’t trust anything you read, including this article! Psychotherapy and Politics International 15(3): e1425. doi: 10.1002/ppi.1425.

Bruns, S.B., and Ioannidis, J.P.A. 2016. p-Curve and p-Hacking in observational research. PLoS ONE 11(2): e0149144. doi: 10.1371/journal.pone.0149144.

Forstmeier, W., Wagenmakers, E.-J., and Parker, T.H. 2017. Detecting and avoiding likely false-positive findings – a practical guide. Biological Reviews 92(4): 1941-1968. doi: 10.1111/brv.12315.

Ioannidis, J.P.A. 2005. Why most published research findings are false. PLOS Medicine 2(8): e124. doi: 10.1371/journal.pmed.0020124.

Medawar, P.B. 1963. Is the scientific paper a fraud? Pp. 228-233 in The Threat and the Glory. Edited by P.B. Medawar. Harper Collins, New York. pp. 228-233. ISBN 978-0-06-039112-6

On Mauna Loa and Long-Term Studies

If there is one important element missing in many of our current ecological paradigms it is long-term studies. This observation boils down to the lack of proper controls for our observations. If we do not know the background of our data sets, we lack critical perspective on how to interpret short-term studies. We should have learned this from paleoecologists whose many studies of plant pollen profiles and other time series from the geological record show that models of stability which occupy most of the superstructure of ecological theory are not very useful for understanding what is happening in the real world today.

All of this got me wondering what it might have been like for Charles Keeling when he began to measure CO2 levels on Mauna Loa in Hawaii in 1958. Let us do a thought experiment and suggest that he was at that time a typical postgraduate students told by his professors to get his research done in 4 or at most 5 years and write his thesis. These would be the basic data he got if he was restricted to this framework:

Keeling would have had an interesting seasonal pattern of change that could be discussed and lead to the recommendation of having more CO2 monitoring stations around the world. And he might have thought that CO2 levels were increasing slightly but this trend would not be statistically significant, especially if he has been cut off after 4 years of work. In fact the US government closed the Mauna Loa observatory in 1964 to save money, but fortunately Keeling’s program was rescued after a few months of closure (Harris 2010).

Charles Keeling could in fact be a “patron saint” for aspiring ecology graduate students. In 1957 as a postdoc he worked on developing the best way to measure CO2 in the air by the use of an infrared gas analyzer, and in 1958 he had one of these instruments installed at the top of Mauna Loa in Hawaii (3394 m, 11,135 ft) to measure pristine air. By that time he had 3 published papers (Marx et al. 2017). By 1970 at age 42 his publication list had increased to a total of 22 papers and an accumulated total of about 50 citations to his research papers. It was not until 1995 that his citation rate began to exceed 100 citations per year, and after 1995 at age 67 his citation rate increased very much. So, if we can do a thought experiment, in the modern era he could never even apply for a postdoctoral fellowship, much less a permanent job. Marx et al. (2017) have an interesting discussion of why Keeling was undercited and unappreciated for so long on what is now considered one of the world’s most critical environmental issues.

What is the message for mere mortals? For postgraduate students, do not judge the importance of your research by its citation rate. Worry about your measurement methods. Do not conclude too much from short-term studies. For professors, let your bright students loose with guidance but without being a dictator. For granting committees and appointment committees, do not be fooled into thinking that citation rates are a sure metric of excellence. For theoretical ecologists, be concerned about the precision and accuracy of the data you build models about. And for everyone, be aware that good science was carried out before the year 2000.

And CO2 levels yesterday were 407 ppm while Nero is still fiddling.

Harris, D.C. (2010) Charles David Keeling and the story of atmospheric CO2 measurements. Analytical Chemistry, 82, 7865-7870. doi: 10.1021/ac1001492

Marx, W., Haunschild, R., French, B. & Bornmann, L. (2017) Slow reception and under-citedness in climate change research: A case study of Charles David Keeling, discoverer of the risk of global warming. Scientometrics, 112, 1079-1092. doi: 10.1007/s11192-017-2405-z

A Modest Proposal for a New Ecology Journal

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

 

On Statistical Progress in Ecology

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

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

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

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

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

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

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

Chamberlin, T.C. 1897. The method of multiple working hypotheses. Journal of Geology 5: 837-848 (reprinted in Science 148: 754-759 in 1965). doi:10.1126/science.148.3671.754.

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

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

 

On Improving Canada’s Scientific Footprint – Breakthroughs versus insights

In Maclean’s Magazine on November 25, 2015 Professor Lee Smolin of the Perimeter Institute for Theoretical Physics, an adjunct professor of physics at the University of Waterloo, and a member of the Royal Society of Canada, wrote an article “Ten Steps to Make Canada a Leader in Science” (http://www.macleans.ca/politics/ottawa/ten-steps-to-make-canada-a-leader-in-science/ ). Some of the general points in this article are very good but some seem to support the view of science as big business and that leaves ecology and environmental science in the dust. We comment here on a few points of disagreement with Professor Smolin. The quotations are from the Maclean’s article.

  1. Choose carefully.

“Mainly invest in areas of pure science where there is a path to world leadership. This year’s Nobel prize shows that when we do this, we succeed big.” We suggest that the Nobel Prizes are possibly the worst example of scientific achievement that is currently available because of their disregard for the environment. This recommendation is at complete variance to how environmental sciences advance.

  1. Aim for breakthroughs.

“No “me-too” or catch-up science. Don’t hire the student of famous Prof. X at an elite American university just because of the proximity to greatness. Find our own path to great science by recruiting scientists who are forging their own paths to breakthroughs.” But the essence of science has always been replication. Long-term monitoring is a critical part of good ecology, as Henson (2014) points out for oceanographic research. But indeed we agree to the need to recruit excellent young scientists in all areas.

  1. Embrace risk.

“Learn from business that it takes high risk to get high payoff. Don’t waste money doing low-risk, low-payoff science. Treat science like venture capital.” That advice would remove most of the ecologists who obtain NSERC funding. It is one more economic view of science. Besides, most successful businesses are based on hard work, sound financial practices, and insights into the needs of their customers.

  1. Recruit and invest in young leaders-to-be.

“Be savvy and proactive about choosing them…. Resist supporting legacies and entitlements. Don’t waste money on people whose best work is behind them.” We agree. Spending money to fund a limited number of middle aged, white males in the Canadian Excellence in Research Chairs was the antithesis of this recommendation. See the “Folly of Big Science” by Vinay Prasad (2015). Predicting in advance who will be leaders will surely depend on diverse insights and is best evaluated by giving opportunities for success to many from which leaders will arise.

  1. Recruit internationally.

“Use graduate fellowships and postdoctoral positions as recruitment tools to bring the most ambitious and best-educated young scientists to Canada to begin their research here, and then target the most promising of these by creating mechanisms to ensure that their best opportunities to build their careers going forward are here.” This seems attractive but means Canadian scientists have little hope of obtaining jobs here, since we are < 0.1% of the world’s scientists. A better idea – how about Canada producing the “best-educated” young scientists?

  1. Resist incrementalism.

If you spread new money around widely, little new science gets done. Instead, double-down on strategic fields of research where the progress is clear and Canada can have an impact.“ Fortin and Currie (2013) show that spreading the money around is exactly the way to go since less gets wasted and no one can predict where the “breakthroughs” will happen.  This point also rests on one’s view of the world of the future and what “breakthroughs” will contribute to the sustainability of the earth.

  1. Empower ambitious, risk-taking young scientists.

Give them independence and the resources they need to develop their own ideas and directions. Postdocs are young leaders with their own ideas and research programs”. This is an excellent recommendation, but it does conflict with the recommendation of many universities around the world of bringing in old scientists to establish institutes and giving incentives for established senior scientists.

  1. Embrace diversity.

Target women and visible minorities. Let us build a Canadian scientific community that looks like Canada.” All agreed on this one.

  1. Speak the truth.

“Allow no proxies for success, no partial credit for “progress” that leaves unsolved problems unsolved. Don’t count publications or citations, count discoveries that have increased our knowledge about nature. We do research because we don’t know the answer; don’t force us to write grant proposals in which we have to pretend we do.” This confounds the scientists’ code of ethics with the requirements of bureaucracies like NSERC for accounting for the taxpayers’ dollars. Surely publications record the increased knowledge about nature recommended by Professor Smolin.

  1. Consider the way funding agencies do business.

“We scientists know that panels can discourage risk-taking, encourage me-too and catch-up science, and reinforce longstanding entitlements and legacies. Such a system may incentivize low-risk, incremental work and limit the kind of out-of-the-box ideas that….leads to real breakthroughs. So create ambitious programs, empower the program officers to pick out and incubate the brightest and most ambitious risk-takers, and reward them when the scientists they invest in make real discoveries.” What is the evidence that program officers in NSERC or NSF have the vision to pick winners? This is difficult advice for ecologists who are asked for opinions on support for research projects in fields that require long-term studies to produce increases in ecological understanding or better management of biodiversity. It does seem like a recipe for scientific charlatans.

The bottom line: We think that the good ideas in this article are overwhelmed by poor suggestions with regards to ecological research. We come from an ecological world faced with three critical problems that will determine the fate of the Earth – food security, biodiversity loss, and overpopulation. While we all like ‘breakthroughs’ that give us an IPhone 6S or an electric car, few of the discoveries that have increased our knowledge about nature would be considered a breakthrough. So do we say goodbye to taxonomic research, biodiversity monitoring, investigating climate change impacts on Canadian ecosystems, or investing in biological control of pests? Perhaps we can add the provocative word “breakthrough” to our ecological papers and media reports more frequently but our real goal is to acquire greater insights into achieving a sustainable world.

As a footnote to this discussion, Dev (2015) raises the issue of the unsolved major problems in biology. None of them involve environmental or ecological issues.

Dev, S.B. (2015) Unsolved problems in biology—The state of current thinking. Progress in Biophysics and Molecular Biology, 117, 232-239.

Fortin, J.-M. & Currie, D.J. (2013) Big science vs. little science: How scientific impact scales with funding. PLoS ONE, 8, e65263.

Prasad, V. (2015) The folly of big science. New York Times. October 2, 2015 (http://www.nytimes.com/2015/10/03/opinion/the-folly-of-big-science-awards.html?_r=0 )

Henson, S.A. (2014) Slow science: the value of long ocean biogeochemistry records. Philosophical Transactions of the Royal Society of London A: Mathematical, Physical and Engineering Sciences, 372 (2025). doi: 10.1098/rsta.2013.0334.

 

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

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

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

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

Explicit hypothesis and alternative hypotheses

“Hypothesis”

“Test”

“Prediction”

“Model”

Yes

22%

Mean

3.1

7.9

6.5

32.5

No

78%

Median

1

6

4

20

No. articles

51

Range

0-23

0-37

0-27

0-163

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

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

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

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

Chamberlin, T.C. 1897. The method of multiple working hypotheses. Journal of Geology 5: 837-848 (reprinted in Science 148: 754-759 in 1965). doi:10.1126/science.148.3671.754

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

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

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

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