Category Archives: Ecological Research Funding

A Dilemma of Ecological Science

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To save myself from the current problems of funding science in general in North America, I would like to ask an impossible but perhaps interesting question: What research would ecologists carry out if they had ten billion dollars of funding? This of course is a ridiculous question, but it is interesting because it would focus our minds on what the major issues of our time are in the ecological sciences and where to go next. The history of the hard sciences like physics, chemistry and medicine is punctuated with a specification of the most important issues that need solving. These specifications change as progress occurs in each science so that there are many books about successes in solving problems in these hard sciences. Could we do this in ecology and what might this list of problems and possible solutions look like?

The first response is that ecology is not a hard science like physics and chemistry with a plethora of well-defined laws. I think this is a cop-out. Ptolemy and Newton and Darwin did not avoid these questions and forged new ways of thinking in their respective sciences. A second response is that ecological science deals with contingent events much as geological science does. We can understand volcano eruptions and tsunamis, but we cannot predict if, when and where they will occur in the same way we can predict that a bridge will fall over if the construction materials are not correct.

We have in ecology today two major schools of thought about what are the most critical issues that ecologists need to investigate. The first school of thought is that we need to understand how populations and communities are structured, how their components interact, and how much these ecosystems vary in different parts of the Earth. We have adequate to good methods to investigate these questions but lack the funding at present. The major unanswered questions within this paradigm are how these ecosystems will respond to global change with respect to human population growth and climate change. But these questions can only be answered with long-term studies, both observational and experimental. The system is hampered by two constraints – the length of an individual scientist’s research, and the short-term view of funding which assumes all these questions can be answered with 3-5-years of research funding. We can achieve success only by establishing teams of ecologists that focus on major questions and cooperate with observations and experiments that exceed the ability of a single scientist with a limited research lifespan. Success on this front can be seen most readily in the aquatic sciences, avian and mammal ecology and least readily in the ecology of the small guys – insects, bacteria, viruses. So, our current understanding in population and community ecology is best with the species we can eat and with large species rather than small. There is no question but that these advances in ecological knowledge are more difficult in the tropical countries with more complex ecosystems and in general less money for research.

The second major school of thought in the ecological sciences is biodiversity science. This school of thought passes over all the problems of ecosystem ecology to describe the species that exist on Earth. This is a gigantic problem because of the large number of undescribed species. We make progress on this list slowly, and at present if you pick up a plant, small animal, and insect, or a bacterium among other species it is impossible to assign a taxonomic name and description. Progress in identification is progress is moving rapidly because of DNA technology but the desirable target of having an inventory of life on Earth is still a long way off.

Given that we have this partial inventory, the major issue of biodiversity science is the problem of extinction – we do not want to see any species go extinct. This is a tall order but an important one. And it is here that the two major schools of ecology must join forces because you cannot understand extinction unless you have adequate knowledge of the role of each species in the ecosystem. If you read the news today, you will become rather depressed because of reported rates of extinction at the present time. The sentiment is good; the data are poor. An unresolved problem is that most species are rare. We humans notice the big species and the colourful birds and insects, but rare species are difficult to study. News media report every species that was thought to be extinct because none were seen for perhaps 20 or 30 years but now a few were found again. With enough funding and person-power ecologists could analyse the details of extinction in a few species but there is no hope that this could be done for the small fauna that are rare and expensive to find.

So, the take home message is that the two major schools of ecology must interact more to achieve success on both fronts but the shortage of funding and the shortage of ecologists in each of the two major areas are limiting. At some point this will change. There are many very wealthy people in western countries who could fund a very large sum of money for ecological science. To date such a financial event is rare, and a possible reason for this is that the ecological sciences do not support economic growth and human health in the same way that physics, chemistry and medicine do. The ecological costs of economic growth are largely ignored, and the two largest of our global problems are climate change and human population growth which exceeds the carrying-capacity of the Earth.  Both issues operate on a time scale greater than the average human lifespan, so we pass the problem on to our children. Ecological science is caught in the trap of not increasing the god of GDP and reporting more problems every day than it is solving. We have a long way to go, and it is important that ecologists look at the long-term and adjust their scientific goals accordingly. Much talk is good if it leads to much action. But action cannot be done without funding.

Duda, M.D., Beppler, T., Austen, D.J., and Organ, J.F. 2022. The precarious position of wildlife conservation funding in the United States. Human Dimensions of Wildlife 27(2): 164–172. doi:10.1080/10871209.2021.1904307.

Gallo-Cajiao, E., Archibald, C., Friedman, R., et al. 2018. Crowdfunding biodiversity conservation. Conservation Biology 32(6): 1426–1435. doi:10.1111/cobi.13144.

Guénard, B., Hughes, A.C., and Williams, G.A. 2025. Limited and biased global conservation funding means most threatened species remain unsupported. Proceedings of the National Academy of Sciences 122(9): 2412479122. doi:10.1073/pnas.2412479122.

Lant, M., Bendel, C.R., Parent, C.J., and Kaemingk, M.A. 2025. A need for assessing the resiliency of conservation funding. Ecology and Society 30(3): 9. doi:10.5751/es-16322-300309.

Papp, C.R., Scheele, B., Rákosy, L., and Hartel, T. 2022. Transdisciplinary deficit in large carnivore conservation funding in Europe. Nature Conservation 49: 31–52. doi:10.3897/natureconservation.49.81469.

How Can We Best Advance Ecological Research

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Everyone who supports scientific research wishes to see progress in understanding of the problems being studied. Ecologists face four critical difficulties in achieving these goals of progress.

  •  There are far too many ecological problems to be sorted out given the number of ecologists in the scientific world. There is a partial solution to this issue by dividing the ecological research into two broad categories: large scale critical problems and small-scale local problems. Large-scale problems are those that apply to many communities and ecosystems, from the local to the global. Large scale problems require first an agreement of what these problems are and second how they should be approached – both difficult to achieve in the current research environment. So there is too little agreement even on this simple issue. Large-scale problems require a coordinated team effort and to date in ecology large-scale problems have been poorly addressed. Small scale problems can be studied with less person power and are much more common. In an ideal world, governments would fund large-scale research programs that require effort that stretches over many years and require considerable reliable funding, and smaller grants could support the many specific postgraduate studies with a time limit of 3-4 years. It would be optimal for these two groups to meld together but this is difficult to achieve. The whole system we have currently fights against this cooperation, partly because in the world of science most of the recognition and rewards go to individual scientists and not to a research team.
  •  A second problem is that there are two paradigms of ecological science that are only partly overlapping. The first paradigm in its strong form states that ecological science will advance most rapidly by means of descriptive studies of changes in communities and ecosystems. Gaiser et al. (2020) provide good examples of this approach. Long-Term-Ecological-Research (LTER) approaches are typically large-scale and rely too much on the assumptions of correlation = causation science, but this paradigm suggests that long-term data will lead us to the long-term understanding of communities and ecosystems. The second approach can be described as the mechanistic paradigm because it attempts to explain long- and short-term population and community changes from whatever cause using experimental methods (Krebs 2002). Hone and Krebs (2023) detail the evidence levels needed for strong inference in both short-term and long-term issues. Lindenmayer (2018) provides an excellent synopsis of the difficulties of long-term research and a synopsis of how we might act to answer ecological questions about future issues (Lindenmayer et al. 2015, Lindenmayer 2018).
  • The third difficulty is that the individual scientist as the unit of research makes it unlikely in the present organization of science funding that these two paradigms can be easily brought together. Scientists by and large wish to be independent, a desirable trait, but we can and should work in a team effort, an interlocking independent research program that has specified objectives that all are organized into a partnership. If you want examples of this approach, you have only to look at the successes and failures of many long-term ecological research (LTER) programs around the world. One example of a successful LTER research program in Austria is reviewed in Gingrich et al. (2016). Additional evaluations of current LTER projects can be found in Vanderbilt and Gaiser (2017) and Rastetter et al. (2021). There has been a movement to integrate social and ecological frameworks to LTER research. A good example of this social-ecological approach is disturbance ecology described for the USA in Gaiser et al. (2020). But ecological approaches of the type described in Vanderbilt and Gaiser (2017) and Gaiser et al. (2020) appear to reduce ecological research to an endless study of descriptive changes in ecosystems with little theory. The hope is to advance ecological science by observations of changes in ecosystems as affected by human activity and climate change. The objective of these research programs is to provide solutions for future environmental problems from long term data sets. However, describing the past does not inherently predict the future, as evidenced by the issues surrounding climate change.
  • A fourth problem is that the long-term funding necessary to understand new and continuing ecological problems too often falls to a new Director or Chief who wishes to change the direction of the research or stop it altogether, so long term objectives are not supported. Another aspect of the funding problem for LTER research is the lack of substantial funding on a spatial and monetary scale that would permit comprehensive research with suitable replication. Cusser at al. (2021) have analysed LTER studies in the USA with respect to how long studies must be to achieve good results. They concluded that half of the LTER studies required 10 years or more to produce consistent results, and some required more than 20 years. Many of these LTER studies are focused on the descriptive paradigm and would not qualify as experimental ecology with specific hypotheses about community and ecosystem dynamics. LTER descriptive studies are useful for advancing knowledge of trends, but they may not be sufficient to identify and test the underlying drivers of community and ecosystem change.

Cusser, S., Helms IV, J., Bahlai, C.A., and Haddad, N.M. 2021. How long do population level field experiments need to be? Utilising data from the 40-year-old LTER network. Ecology Letters 24(5): 1103-1111. doi:10.1111/ele.13710.

Gaiser, E.E., Bell, D.M., Castorani, M.C.N., Childers, D.L., and Groffman, P.M. 2020. Long-term ecological research and evolving frameworks of disturbance ecology. Bioscience 70(2): 141-156. doi:10.1093/biosci/biz162.

Gingrich, S., Schmid, M., Dirnbock, T., Dullinger, I. et al. 2016. Long-Term Socio-Ecological Research in Practice: Lessons from Inter- and Transdisciplinary Research in the Austrian Eisenwurzen. Sustainability 8(8): 743. doi:10.3390/su8080743.

Hone, J., and Krebs, C.J. 2023. Causality and wildlife management. Journal of Wildlife Management 2023: e22412. doi:10.1002/jwmg.22412.

Krebs, C.J. 2002. Two complementary paradigms for analyzing population dynamics. Philosophical Transactions of the Royal Society of London, Series B 357: 1211-1219. doi:10.1098/rstb.2002.1122.

Lindenmayer, D.B., Burns, E.L., Tennant, P., Dickman, C.R., Green, P.T., Keith, D.A., et al. 2015. Contemplating the future: Acting now on long-term monitoring to answer 2050’s questions. Austral Ecology 40(3): 213-224. doi:10.1111/aec.12207.

Lindenmayer, D. 2018. Why is long-term ecological research and monitoring so hard to do? (And what can be done about it). Australian Zoologist 39: 576-580. doi:10.7882/az.2017.018.

Rastetter, E.B., Ohman, M.D., Elliott, K.J., Rehage, J.S., and al., e. 2021. Time lags: insights from the U.S. Long Term Ecological Research Network. Ecosphere 12(5): e03431. doi:10.1002/ecs2.3431.

Vanderbilt, K., and Gaiser, E. 2017. The International Long Term Ecological Research Network: a platform for collaboration. Ecosphere 8(2): e01697. doi:10.1002/ecs2.1697.

Problems in Funding Biological Conservation Research

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Everyone is in favour of preventing extinctions and the job of the conservation ecologist is to specify how to achieve this scientific goal. That scientific job leads into a maelstrom of problems that have been discussed extensively in the literature. I want to concentrate today on the related question of how much funding is needed and available for conservation and how it can be used most efficiently. The literature on these aspects of conservation action is extensive and I discuss here only a small part of the problems and approaches.

Funding for scientific research has always been limited and in a democratic society would improve only if public interest in research becomes stronger. This is now happening, but the governments of western countries are pulled in many directions for funding and the ecological data needed for protecting threatened and endangered species and ecosystems cannot be obtained by voluntary citizen science, valuable though it is. One of the funding success stories from the United States has been the enactment of the Pittman-Robertson Act of 1937 (Duda et al. 2022). Wildlife conservation in the USA has been supported by a tax on the purchases of guns and ammunition by hunters and those funds were given to each state to support wildlife conservation. But the number of hunters has declined in the USA although the sales of lethal weapons continue to increase. Sport shooters who are not hunters now provide about half of these tax dollars for conservation, and there has been a move to broaden the tax base to more outdoor activities.

Philanthropic funding has contributed greatly to increased funding for conservation work, but these funds are often country-specific (Yang et al. 2024), and while they benefit wealthy countries, they are sparse in the poorer countries with high species richness and where conservation is even more essential. Yang et al. (2024) discuss the rising philanthropic funding for biodiversity conservation in China while recognizing that while conservation funding is rising it represents <1% of all the philanthropic funding in China. While there is a massive amount of philanthropy that contributes to medical science, there is a strong need for philanthropic funding to increase in all the wealthy countries. Kedward et al. (2023) discuss why private funding alone will not be able to deliver positive achievements for conservation goals. They point out that conservation funding is approximately 5-7 times lower than is needed to reverse biodiversity losses, which argues for direct public funding of conservation by governments. Private investors wish to have some financial return for their investments which can lead to perverse incentives and “greenwashing” with no positive results for biodiversity conservation.

A further concern is that conservation research requires a long-term investment combined with a high tolerance for uncertainty. Given that we can achieve both private and governmental funding for conservation, we find two critical decisions – what species do we focus on since we cannot do all species, and what scale must be achieved to stop biodiversity loss. It is no surprise to conservation ecologists that both taxonomic and aesthetic biases extend throughout biodiversity research. Adamo et al. (2020) compiled for the European Union the funding for plants and animals with the EU over the last 3 decades. They found that animal species obtained three times more funding than plant species. This large-scale approach turned up an array of surprises. In plants for example, species found at northern latitudes with broad distributions and with blue flowers obtained more funding regardless of whether or not they were in danger of extinction.

The species ecologists are attracted to are obvious to any naturalist. We are concerned more about elephants than small rodents. We worry more about sequoias than we do about algae. 

The scale question in biodiversity research is the second major issue. Protected areas like National Parks are a key component of safeguarding biodiversity, and setting aside these protected areas is a major effort in conservation. But when one looks at the global scale and compile only those protected areas that are properly resourced with adequate staff and a sufficient budget, Coad et al. (2019) found that only 4-9% of terrestrial amphibians, birds, and mammals are adequately represented in protected areas. Hebblewhite et al. (2022) evaluated the Yellowstone to Yukon (Y2Y) large-landscape conservation achievements since its establishment in 1993. The focal species of this large region was the grizzly bear, an umbrella species for this large area of 1.3 million sq. km in western North America. During the last 25 years the amount of protected area in this particular landscape grew by 8%, achieving a total of 18% of the landscape in national parks and reserves, a major conservation success. This program is a clear success but not yet achieving the 30% proposed by the Global Biodiversity Framework of 2022 (Saunders et al. 2023).

The scale issue is critical at small scales as well, and the critical point is that detailed small scale research efforts are essential for conserving the biodiversity in all protected areas. Most conservation research is at small scale with a limited budget and working on a limited area with a time frame of 3 years. Yet the purpose of many research grants is to achieve results that will flow through into policy at the government level. LeFlore et al. (2022) evaluated how many small-scale studies in the flora and fauna of coastal marine environments were utilized in policy actions. They found that only 40% of these marine studies were reported to result in a positive outcome for conservation. Specific reliable scientific data are a prerequisite to defining action plans for conservation but there needs to be more interaction between government policy makers and scientists collecting relevant data. Reliable data are necessary for proper conservation policy actions but not sufficient.

Adamo, M., Sousa, R., Wipf, S., Correia, R.A., Lumia, A., Mucciarelli, M. & Mammola, S. (2022) Dimension and impact of biases in funding for species and habitat conservation. Biological Conservation, 272, e109636.doi: 10.1016/j.biocon.2022.109636.

Coad, L., Watson, J.E.M., Geldman, J., Burgess, N.D., Leverington, F., Hockings, M., Knights, K. & Di Marco, M. (2019) Widespread shortfalls in protected area resourcing undermine efforts to conserve biodiversity. Frontiers in Ecology and the Environment, 17, 259-264.doi: 10.1002/fee.2042.

Duda, M.D., Beppler, T., Austen, D.J. & Organ, J.F. (2022) The precarious position of wildlife conservation funding in the United States. Human Dimensions of Wildlife, 27, 164-172.doi: 10.1080/10871209.2021.1904307.

Hebblewhite, M., Hilty, J.A., Williams, S., Locke, H., Chester, C., Johns, D., Kehm, G. & Francis, W.L. (2022) Can a large-landscape conservation vision contribute to achieving biodiversity targets? Conservation Science and Practice, 4, e588.doi: 10.1111/csp2.588.

Kedward, K., Ermgassen, S.z., Ryan-Collins, J. & Wunder, S. (2023) Heavy reliance on private finance alone will not deliver conservation goals. Nature Ecology & Evolution, 7, 1339-1342.doi: 10.1038/s41559-023-02098-6.

LeFlore, M., Bunn, D., Sebastian, P. & Gaydos, J.K. (2022) Improving the probability that small‐scale science will benefit conservation. Conservation Science and Practice, 4, e571.doi: 10.1111/csp2.571.

Saunders, S.P., Saunders, S.P., Grand, J., & Price, J. (2023). Integrating climate‐change refugia into 30 by 30 conservation planning in North America. Frontiers in Ecology and the Environment 21(2): 77-84. doi:10.1002/fee.2592.

Yang, F., Tao, Z. & Zhang, L. (2024) Trends and dynamics of philanthropic funding for biodiversity conservation in China. Conservation Science and Practice, 6, e13059.doi: 10.1111/csp2.13059.