The majority of empirical ecology research published in our journals is short-term with the time span dictated by the need for 1–2-year Master’s degree studies and 3-4-year PhD research. This has been an excellent model when there was little of a framework for researching the critical questions ecologists ought to answer. Much of ecology in the good old days was based on equilibrium models of populations, communities, and ecosystems, an assumption we know to be irrelevant to a world with a changing climate. Perhaps we should have listened to the paleoecologists who kept reminding us that there was monumental change going on in the eras of glaciation and much earlier in the time of continental drift (Birks 2019). All of this argues that we need to change direction from short-term studies to long-term studies and long-term thinking.
There are many short-term ecological studies that are useful and should be done. It is necessary for management agencies to know if the spraying of forest insect pests this year reduces damage next year, and many similar problems exist that can be used for student projects. But the big issues of our day are long term problems, defined in the first place by longer than the research lifespan of the average ecologist, about 40 years. These big issues are insufficiently studied for two reasons. First, there is little funding for long term research. We can find a few exemptions to this statement, but they are few and many of them are flawed. Second, we as research scientists want to do something new that no one has done before. This approach leads to individual fame and sometimes fortune and is the social model behind many of the research prizes that we hear about in the media, the Nobel Prize, the MacArthur Awards, the National Medal of Science, the Kyoto Prize and many more. The point here is not that we should stop giving these awards (because they are socially useful), but that we should take a broader perspective on how research really works. Many have recognized that scientific advances are made by groups of scientists standing on the shoulders of an earlier generation. Perhaps some of the awards in medicine recognize this more frequently than other areas of science. My point is that large problems in ecology require a group effort by scientists that is too often unrecognized in favour of the individual fame model of science prizes.
A few examples may exemplify the need in ecology to support group studies of long-term problems. The simplest cases are in the media every day. The overharvesting of trees continues with little research into the long-term recovery of the harvested area and exactly how the forest community changes as it recovers. We mine areas for minerals and drill and mine tar sands for oil and gas with little long-term view of the recovery path which may stretch to hundreds or thousands of years while our current research program is long-term if it goes for 10 years. Canada has enough of these disturbance problems to fill the leger. The Giant Gold Mine in the Northwest Territories of Canada mined 220,000 kg of gold from 1948 to 2004 when it closed. It left 237 tonnes of arsenic trioxide dust, a by-product for extracting gold. The long-term ecosystem problems from this toxic compound will last for centuries but you might expect it will be much sooner forgotten than subjected to long-term study.
So where are we ecologists with respect to these large problems? We bewail biodiversity loss and when you look at the available data and the long-term studies you would expect to measure biodiversity and, if possible, manage this biodiversity loss. But you will find only piecemeal short-term studies of populations, communities, and ecosystems that are affected. We tolerate this unsatisfactory scientific situation even for ecosystems as iconic as the Great Barrier Reef of eastern Australia where we have a small number of scientists monitoring the collapse of the reef from climate change. The only justification we can give is that “Mother Nature will heal itself” or in the scientific lingo, “the organisms involved will adapt to environmental change”. All the earth’s ecosystems have been filtered through a million years of geological change, so we should not worry, and all will be well for the future, or so the story goes.
I think few ecologists would agree with such nonsense as the statements above, but what can we do about it? My main emphasis here is long-term monitoring. No matter what you do, this should be part of your research program. If possible, do not count birds on a plot for 3 years and then stop. Do not live trap mice for one season and think you are done. If you have any control over funding recommendations, think continuity of monitoring. Long-term monitoring is a necessary but not a sufficient condition for managing biodiversity change.
There are many obstacles interfering with achieving this goal. Money is clearly one. If your research council requests innovation in all research proposals, they are probably driven by Apple iPhone producers who want a new model every year. For the past 50 years we have been able to fund monitoring in our Yukon studies without ever using the forbidden word monitor because it was not considered science by the government granting agencies. In one sense it is not whether you consider science = innovation or not, but part of the discussion about long term studies might be shifted to consider the model of weather stations, and to discuss why we continue to report temperatures and CO2 levels daily when we have so much past data. No one would dream of shutting down weather monitoring now after the near fiasco around whether or not to measure CO2 in the atmosphere (Harris, 2010, Marx et al. 2017).
Another obstacle has been the destruction of research sites by human developments. Anyone with a long history of doing field research can tell you of past study areas that have been destroyed by fire or are now parking lots, or roads, or suburbia. This problem could be partly alleviated by the current proposals to maintain 30% of the landscape in protected areas. We should however avoid designating areas like the toxic waste site of the Giant Gold Mine as a “protected area” for ecological research.
Where does this all lead? Consider long-term monitoring if you can do the research as part of your overall program. Read the recent contributions of Hjeljord, and Loe (2022) and Wegge et al. (2022) as indicators of the direction in which we need to move, and if you need more inspiration about monitoring read Lindenmayer (2018).
Birks, H.J.B. (2019) Contributions of Quaternary botany to modern ecology and biogeography. Plant Ecology & Diversity, 12, 189-385.doi: 10.1080/17550874.2019.1646831.
Harris, D.C. (2010) Charles David Keeling and the story of atmospheric CO2 measurements. Analytical Chemistry, 82, 7865-7870.doi: 10.1021/ac1001492.
Hjeljord, O. & Loe, L.E. (2022) The roles of climate and alternative prey in explaining 142 years of declining willow ptarmigan hunting yield. Wildlife Biology, 2022, e01058.doi: 10.1002/wlb3.01058.
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.
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.
Wegge, P., Moss, R. & Rolstad, J. (2022) Annual variation in breeding success in boreal forest grouse: Four decades of monitoring reveals bottom-up drivers to be more important than predation. Ecology and Evolution.12, e9327. doi: 10.1002/ece3.9327.