Jeremy made a compelling case that the typical scientist produces modest contributions to the field but that is enough (it is still leaving the world better than we found it). But several commentors, while acknowledging that in a field with thousands of scientists most of us aren’t going to do more than Bill Murray in Groundhog Day, still felt that a vision of science that doesn’t also include some big advances was unsatisfying (me among them). So the question emerges, are there big advances happening in ecology right now? or will there be in the immediate future?
Obviously this is a somewhat subjective question, but I think it is not entirely subjective. While you wouldn’t get 100% consensus, I bet there are ideas in the recent past that could get at least 70% consensus as big ideas that changed the field that emerged in recent decades. Metapopulations/metacommunities (technically emerged in 1969 but major ripple effects for decades after including the follow-on concept of metacommunities that emerged in the 2000s). Macroecology in the 1990s. Species distribution modelling. Functional traits. Global change ecology or biodiversity in the Anthropocene. Biodiversity and ecosystem function (so big it has an acronym, BEF). Now some people are fans of those ideas, and some aren’t. But I think most of us could agree they had a big impact on the literature and directions of research. And they all started in the late 1990s and bloomed in the decade of the 2000s (and are all still going today). So what are the new big ideas of the 2010s and 2020s? or have we stopped generating new ideas?
First, I think it is important to distinguish big questions from big ideas. Big questions may be hot and drive the field. But they start with a specific question: how does x work? or what is the nature of y? I think the global change ecology or biodiversity in the Anthropocene question is an example of a fairly emergent new big question, “how are humans changing biodiversity” (definitely going back to the ’00s but still going strong). Mike mentioned this as a candidate in the Groundhog Post. And we are and will advance on this question. But it is a question. Not a new idea or framework or combination of processes. So it is not changing how people think about the ecological world and processes outside of that question (at least yet). There are also classic big questions (e.g. why are there more species in the tropics). These big questions certainly drive research and are important. And it is good to work on classic big questions. On some level you have to work on a big question. It’s hard to get your PhD or get hired as a faculty member if you cannot tie your work to a big question. And don’t get me wrong. Big questions are exciting and motivating. But if they’ve been around for 100 years (latitudinal gradient, community phylogenetics, traits, etc all arguably go back to Darwin), then that says something (not necessarily good nor bad) about our field, and it would be good to own that ecology is a field that just keeps grinding away at a handful of major questions. So in this post, I’m really only interested in NEW big questions (without in anyway devaluing longstanding big questions).
But a big idea is different. It is a new conceptual framework that lets us reorient our view of the world. The theory of island biogeography (again its own acronym: TIBG) is one. The question was fairly mundane – why do some islands have more species than others. But the idea of TIBG (a dynamic community of species immigrating and going extinct with various factors controlling those rates) was colossal. It spawned fields ranging from reserve design to renewed interest in species area relationships, to neutral theory. It changed the whole set of cupboards and hooks on which we slot and organize our understanding of nature. Metapopulations was a big idea too. It didn’t initially answer any question, but it has also reorganized our thinking of the world (and interestingly has some real connections with TIBG). Big ideas have reach far outside of where they start.
Sometimes its hard to distinguish a big idea from a big question initially. Was community phylogenetics a big idea (species interacting in communities have a phylogenetic/macroevolutionary history that is measurable) or a big question (what is the phylogenetic structure of communities). But as time went on, I think it emerged that it was a question, and not one with super clear answers in many cases.
I can identify plenty of candidates for big questions. Just a few examples (admittedly very tilted to my own research interests).
- What determines the number of species that can coexist? This includes the why are there more species in the tropics. But also local versions. What is the role of productivity? Of dispersal? Of macroevolution? This has been around in some form since the 1800s and if I had to put a number on it we’re about 50% of the way to answering it.
- What are humans doing to biodiversity? Which human impacts matter the most? What aspects of diversity are influenced the most (it’s mostly not species richness)? Can we predict future outcomes of biodiversity change? Yes you can argue this is just a more specific, applied version of #1. But there are reasons it stands alone too.
- What determines the species geographic range. A fundamental unit we have talked about for more than century but we have next to know theory linked to test on this topic. Also around since the 1800s but I would say we’re only 10-20% of the way to answering it.
But only one of those big questions (#2) is NEW instead of classic. And I already identified some big ideas that emerged in the 00s (functional traits, neutral theory, BEF, community phylogenetics). But I can’t identify any big ideas (again process-based frameworks that change how perceive the world). And other than the biodiversity in the Anthropoecene, maybe some questions related to mutualism and disease which were woefully understudied until recently, I’m not sure I can identify emergent new big questions either.
There are a number of theories about why this might be:
- Ecology has picked the low hanging fruit and new big questions and big ideas are going to be increasingly rarer and rare as time goes forward. Just look at how the scope of questions in physics have gotten more narrow over time. This is good – science should have an endpoint.
- There are big ideas and new big questions that I’m missing. Maybe I’m missing them because I’m a single individual with a narrow perspective and they’re right in front of me. Or maybe it takes the whole field some time and the benefit of seeing things in the rear view mirror to identify big ideas and new big questions. I doubt anybody who read Levin’s 1969 paper on metapopulations the year it came out thought it was going to change the world. I think of this as an optimistic point of view – there are still big questions and ideas – you just can’t see them when you’re in the middle.
- Ecology still has big ideas and new big questions to emerge, but we are in a local suboptimum where systemic incentive structures, obsession with statistics or big data, 3 year cycles of grants and 5 year cycles of PhDs, the exponential growth of scientists and papers, or other systemic factors are making us less efficient at identifying new big ideas and big questions but if we fix that we can return to the earlier days. (Obviously if this is the case it is really important to identify and fix the systematic constraints).
- Ecology is producing new big ideas and big questions at the same rate as the 1950s-1970s so there is no need for angst. Just chill. Because big ideas last for decades, they look bigger in the rear view mirror than when they’re still emerging. But arguing against this, there is some quantitative evidence that research as measured at the unit of a journal paper is less disruptive.
- Nothing is new under the sun. Ecology just circles over the same territory again and again (hopefully in a spiral, not a circular rut!). Metacommunities were on the cover of Andrewartha and Birch’s textbook in the 1950s. BEF was a concern of Elton. TIBG was mostly just species area relationships (Arrhenius 1920s) and dynamic community structure driven by immigration and local extinction (paleontology since the 1800s, island biogeography since early 20th century, naturalists forever). SDMs are just a fancier stats version of Grinnell’s 1917 paper on the Niche of the California Thrasher. The frontier of the study of plant competition in 2000 was 13/14ths or 93% already tackled with similar general conclusions by Clements 1929 book Plant Competition (see middle of this post). Newness exists only in the minds of new up and coming researchers who didn’t live through it last time. To be really blunt, newness is just ignorance of the past. So get used to classic questions and classic big ideas periodically reemerging. This is a version of Jeremy’s Groundhog vision on steroids!
So. Does ecology have NEW big ideas or big questions (where define NEW as having fully gained steam in the 2010s or 2020s with initial papers perhaps a decade older)? What are your candidates? I’m really curious to see your suggestions in the comments. Or if we don’t have new big ideas and big questions, why? Which of theories A-E do you favor?
Dynamic Ecology 
I would suggest the METABOLIC THEORY OF ECOLOGY as a new big IDEA. [See JBrown overview: ecol_85_721.1790_1791.tp (hawaii.edu).] It fits your time frame, and has massively increased in influence over the last decade; The Jim Brown 2004 overview [ attached] is the second most cited paper ever published in the Journal ECOLOGY [ in a virtual tie with one other paper].
Its an idea because it suggests that a lot can be understood by using in simple formula that combines body size and temperature to predict biological rates and times. It has been used in zillions of ways in the literature, and its citation rate is increasing even after 20+years.
ric
Agreed – a very good candidate. Like nearly every other big idea, you can find roots back to the 1920s, but there is no doubt from the 1990s into the 2000s this experienced an enormous amount of new attention and development.
MTE—specifically the “fundamental equation”—is perhaps the best example I’ve seen here yet, and at the same time highlights why I think “B” is the best answer. Ecology, to paraphrase Douglas Adams, is Really Really Big, and draws on so many other sciences. Just look at the phone book that is Begon Harper and Townsend. It’s hard to keep up with everything, and fun enough to mine our own veins of truth.
Francis Crick once said something to the effect “A mark of a big idea in science is that it predicts visible phenomena from what was heretofore invisible causes.” In that spirit I’m pretty convinced that much ecological phenomena of interest is driven by the health of individual organisms, which in turn reflects their nutrition. Optimal Foraging Theory started the ball rolling asking how community phenomena could be extrapolated from the distribution of energy and simple rules used by critters to get it. Along the way Ecological Stoichiometry (and the Geometric theory of ecology) started working in the role of N and P, carbs, fats and proteins, their physiology and geography. Now we are seeing how all 25 or so elements essential for life can have their own physiological function, interaction, and geography.
Indeed, much of what we see today in this field is a fusion of ecosystem, physiological, and population ecology. Like MTE (and OFT before it) it rests on the idea if we know the rules by which individual organisms work, we can make nontrivial predictions about the abundance of populations in space and time. And it has sparked growing concern about one byproduct of CO2 enrichment—that plants the world over based on straightforward mass-balance thinking—are fixing more carbon and diluting the nutrient content of plant tissue. Those who see only the “greening of the earth” are blind to the nutritional collapse of Earth’s food webs and all the *abundance* declines that result.
mike
PS Eric, while rifling through my library today I came across my copy of your self-published monograph on OFT with GordonO. One of my fav mementos of the Sci biz.
Hi mike; thanks for the kind words. The 1973 book with Gordon Orians is available for free on the Web. One source is here: Optimal Foraging: Some Theoretical Explorations (unm.edu)
Fascinating post Brian. Certainly there are aspects of mutualism that remain under-explored, though whether these count as new big ideas or questions is debatable. For example, in a book chapter some years ago I showed that, as mutualisms become more physiologically and morphologically integrated between partners, they become more phylogenetically exclusive. But there’s no real theory to explain why this might be the case, or what is cause and what is effect.
Personally I’d like to see ecologists collaborating more with paleontologists in order to determine whether, 100s of millions of years ago, the planet’s communities and ecosystems really functioned the way they do now. Or were aspects completely different? This might then give us some insights into how different or similar the ecologies of other planets might be. Now xenoecology WOULD be a big question!
Love your suggestions both in mutualisms and paleo & xeno biology! I agree about the paleo especially. I am lucky to hang out with several paleoecologists who see themselves as ecologists first and paleontologists (or botanists or mammalogists) second. So much material there. Including answers to anthropocene impacts – everything humans are doing has been done in slightly different form by nature in the past. And Xenobiology will be big whenever it happens.
Some more thoughts on this. The ubiquitous and often profound impacts of microbial symbionts on the reproduction and interspecific interactions of their hosts has become clear in recent decades. Impacts range from the evolution of mating “strains” of insect species via Wolbachia infection, to psychological changes associated with differences in the gut flora, to the manipulation of pollinator behaviour via yeast fermentation of nectar. It needs a profound shift in our understanding of the natural world to really appreciate the fundamental importance of this ‘invisible’ element of the biosphere.
Yes, I’ve been working with some paleontologists recently on questions of how we recognise pollinators in the fossil record and why a deep-time perspective on biotic pollination is important. Really fascinating and stimulating, especially as fossil hunting was one of my first loves. I could easily have become a professional paleontologist!
I definitely agree on the impact of microbes as a candidate for this! Brian linked to this elsewhere in the comment threads, but that was my proposal in a post on DE 1.0: https://dynamicecology.wordpress.com/2014/04/07/what-do-you-think-is-the-biggest-recent-conceptual-advance-in-ecology/
One thing that I think about sometimes is the way museums are structured and how they would be set up today, given what we’ve learned about the way the world works. I think that traditionally institutions have tended to have Museum of Zoology and an Herbarium (but definitely am not an expert in how these tended to be set up!) It seems like, if these institutions were being established today, we’d probably want to have microbes as a key focus, right?
Hi Meghan – yes, I think that the silos zoology v. botany v. geology (where paleontology is often based!) imposed in museums has historically been a problem. Ditto putting fungi into herbaria, when phylogenetically they are much closer to animals.
“Just look at how the scope of questions in physics has gotten more narrow over time. This is good – science should have an endpoint”
I partly agree with this because most fields are now mature, although I don’t necessarily believe that science should have an endpoint. I also see a growing interest in applied ecology/biology being powered by technology. If “big idea” is about new understanding, we are certainly deriving new knowledge through CRISPR technology, etc. So, the current notion of “big idea” may be intertwined with technology such that they are not recognizable to traditionalists, who are more comfortable with hypothesis-theory progression.
I agree that “end point” for science might be a bit too much. Maybe an asymptotic approach? at least a decelerating approach for sure.
I agree that methods (satellites & aerial imagery, camera traps, eDNA would be some of my list) are impactful. I’m not sure I would say they’ve totally changed the way we think though. Not in the way that say discovery of DNA (or CRISPR) changed molecular & cellular biology.
Does Hatton et al. 2024 count as a new question or new idea? https://www.science.org/doi/10.1126/science.adg8488
technical quibble, that might be more than a quibble: I don’t quite see why one would assume sublinear intraspecific density dependence but linear interspecific density dependence. And I say that as someone who’s done it himself! (in my case, because it seemed to fit the data; Fox 2023 Ecology). Wouldn’t it make more sense to assume sublinear density dependence in both intra and interspecific interactions? At least to the extent that you’re imagining intra- and interspecific competition, as opposed to interspecific interactions like predator-prey or mutualism? The authors only have one arm-wavy paragraph in the supplementary material about this issue.
Ooh – missed that paper. The whole diversity/stability debate had a bit of a start in the 1990s along with BEF, but to my read faded. I guess time will tell whether either diversity/stability or alternative forms of population dynamics become a big idea (it certainly seems like population dynamics is ripe for innovation, but also hard to imagine what hasn’t been suggested previously).
Thinking about that paper today, and about first author Ian Hatton’s previous work, it seems like a new big question might be: why is density dependence sublinear? That is, why is it subject to diminishing marginal returns–the first additional individual reduces the population’s per-capita growth rate a lot, the zillionth additional individual hardly reduces the population’s per-capita growth rate at all.
That Hatton et al. 2024 Science paper doesn’t offer any hypotheses; just says that sublinear density dependence is a phenomenological model that fits the data. (unless I missed it? It’s one of those Science papers where the paper itself is almost an extended abstract for a ginormous online supplement. Personally, I wish it had been an Ecological Monographs paper because that would’ve been easier for me to read, but YMMV.)
IIRC, Peter Abrams did a bit of work deriving the shape of consumer density dependence from various consumer-resource models. He concluded that it was very idiosyncratic. That you could get sublinear, superlinear, or combinations of both. But if sublinear really is the general rule, then it’s either some kind of statistical attractor sensu Steven Frank*, or there’s some generic robust explanation that’s independent of the details of any consumer-resource model.
Ok, I’m off to google a review of explanations for diminishing returns in economics. In the hopes that maybe there’s some generally-applicable analogy between diminishing returns in economics, and sublinear density dependence.
*for readers who have no idea what I’m talking about: https://dynamicecology.wordpress.com/2014/06/30/steven-frank-on-how-to-explain-biological-patterns/
Doesn’t Sibly et al 2005 (Science) effectively empirically show that (very) sublinear density dependence is by far the most common form in nature (using the GPDD population dynamics database)? Also a chapter in a great book on population dynamics by Sibly & Clutton-Brock (https://www.amazon.com/Wildlife-Population-Growth-Rates-Sibly/dp/0521533473).
It doesn’t seem that hard to visualize to me. It is just a continuous extension of the binary world of “don’t have to compete for resources”/”do have to compete for resources”, and many features like territoriality and aggression that go with this state have a binariness (although there are obviously still degrees to both).
OK authoritative big-data paper followed by handwavy theory, but that is exactly what you should expect from somebody who calls themself an empirical ecologist!
Yes, Hatton et al. actually rely heavily on Sibly et al. 2005, while also presenting their own analysis that recovers similar results to Sibly et al. 2005.
As an aside, relying on Sibly et al. 2005 might be a bit risky. Sibly et al. 2005 came in for various lines of criticism at the time, IIRC. I’d have to go back and look to recall exactly what the criticisms were, whether they were correct, and whether Hatton et al.’s own analysis addresses them.
Saether et al. 2007 show that density dependence varies from sublinear to superlinear among bird species, along a fast-slow life history continuum. But Hatton et al. think that sublinear density dependence is more or less universal, not just a characteristic of species at one end of the fast-slow life history continuum.
There is an older paper by Charles W Fowler; 1981 Ecology62:602-610, titled Density dependence as related to life history strategy.
It and a few other papers by Fowler, showed that the shape of density dependence with pop size was strongly related to Ro-max, the hypothetical maximum Ro as N goes to zero (and density dependence is relaxed.).
I develop “Fowler’s rules’ for pop dynamics on pgs 124-127 of my 1993 LIFE HISTORY INVARIANTS book.
Fowler and I were office mates in grad school, and he worked for many years for NOAA fisheries, National Marine Mammal Survey [?]. He has some gray literature pubs on density dependence in mammals, and several papers in journals and books.
I am of course biased but I totally agree with your statement that population dynamics is ripe for innovation.
I fail to understand how we can continue to represent the state of a population by a single number as in the Hatton et al. paper. Especially when at the same time we call attention to intra- and interspecific variation. By far the brunt of intraspecific variation is due to differences in developmental state. So which metric do we pick to represent a population of butterflies? The biomass of the butterflies or the caterpillars? Or both? There are many, many species, not only holometabolous insects, where juvenile and adult individuals have very different ecologies in addition to the fundamental difference that juveniles develop and mature whereas adults reproduce. When are we going to take the richness, uniqueness and complexity of ecological systems serious and admit that we cannot capture a population by a single number? I often wonder why this tradition is still going strong in ecology. Is it due to some physics envy? If so, biological individuals do something that is very different from any physical or chemical analogue: they develop (in many multicellular species even a lot).
@Andre
I’m sorry your comment got blocked by our hyperactive spam filter again. It’s a great comment. There is a real disconnect between comment threads say intraspecific variation is a key innovation (and arguably that traits are as well), but continuing to model populations as N=.
I’m glad people are working on the more complex approaches. As always, I guess the challenge is to find the golden middle right level of complexity.
Ok, I went back and reminded myself about the technical criticisms of Sibly (2005).
One key issue is that, if the abundance doesn’t vary over a huge range including values far below K, then it’s impossible to get independent estimates of r and theta. There’s a ridge in the likelihood surface because the two parameters can compensate for one another; any combination of r and theta with the same product r*theta will produce an equally good fit to abundance data that never get too far from K. So what ends up happening in real (or realistic simulated) data is that you end up either vastly underestimating or vastly overestimating theta, with the former being more common. That is, estimates of theta tend to be biased towards finding concave-up density dependence, which is what Sibly (2005) finds. See Clark et al. 2010 Methods Ecol Evol, and Polanksky et al. 2009 Ecology. Here’s Clark et al:
https://besjournals.onlinelibrary.wiley.com/doi/full/10.1111/j.2041-210x.2010.00029.x
I’m now somewhat less excited about Hatton et al. 2024. I need to go back and look closely at their supplementary material to see if/how they address the technical issues here. Because these aren’t minor issues, they’re crucial to the paper’s central argument.
Love the topic and perspective Brian, thanks. I really should take a class taught by a person with your breadth.
When I switched from physics to ecology, my geophysicist type dad and his colleagues were bewildered. What a waste of time Scott (they were concerned for me as these colleagues knew me since I was born): ecology has nothing to show for itself like physics does. I tried to argue, and failed! I hoped that I would someday be able to better defend our field.
It is in this vain I especially keyed into Brian’s qualification “Now some people are fans of those ideas, and some aren’t. But I think most of us could agree they had a big impact on the literature and directions of research.” This seems to imply that a big idea could be something all together siloed in our own community. I would suggest (and maybe this is actually Brian’s intention and I’m reading wrong) that “big idea” should be one that extends outside of our field. One that influences the world not because we say it should, but because it has. I.e. not because we have convinced institutions to apply the big idea and how to do so, but because institutions have applied them and they have had a measurable influence. You know, like vaccines, or semiconductors, nuclear fission, advertising strategy and democracy.
Woops.. .and that sounds too much like I think a big idea needs to be applied. What I mean is that a big idea should not be defined by the group (or discipline) that creates it.
I understood your point about final judgment coming from spread to external fields. It is an interesting debate though whether ecology (or public health) will ever get to spread and impact society the same way. People have argued that society (specifically corporations) embraced science when it was mostly about physics and biomedical, because those could be sold. While ecology seems more about criticizing and limiting economic growth. Some have even pinpointed it to Rachel Carson’s Silent Spring. Is it even possible for ecology to have an idea that is influential beyond those who care about the environment? Biodiversity and ecosystem services are ecologists attempts, and certainly they have had some impact, but I don’t know that it is the same vaccines or semiconductors. I guess my first instinct is that kind of spread isn’t possible for ecology?
That is interesting about the way different big ideas could take root. I think that could be part of it.
I believe very smart people dedicate their lives to stopping kids from taking vaccines to protect them (and my wife interacts with these dedicated people). That is one of many examples social psychologists examine to show how groups can legitimize their goals and beliefs. Based on this line of work, I think internal evaluation could be flawed. There is only one paper out there that applies social psychology to biases in ecology and evolution ( Vellend 2019 Phil Topics. A great paper I think. Please let me know if you know of others!). So not only do we self-evaluate, we don’t use the relevant science being done across campus to guide our self-evaluation. Perhaps, as you say Brian, we can’t use the same approach as say materials science to evaluate if we’ve developed “big ideas”, but I think we need something other than asking ourselves whether e.g. ecosystem-function biodiversity work is a big idea. And I don’t think the quantity of work done within the field, number of faculty lines created, and many papers in science and nature on a topic which had us as reviewers, is evidence. Perhaps there are ways we have not though of.
A simple thought experiment: what would we be saying about how many “big ideas’ our field has in a world in which there aren’t any. I think the answer is: we’de say we have a bunch of them. Of course we have — we need to have had! Otherwise what are we doing!? (all that , in our subconscious perhaps). Of course this doesn’t answer if we’ve had big ideas or not, but perhaps it gives some perspective on how to evaluate.
I consider quantum mechanics a big idea.
I take your point about the need for external validation of what is truly world changing vs insider baseball navel gazing (to mash two metaphors). I guess ive argued it won’t come from the world of commerce. What do you make of old home ec departments that call themselves human ecology departments or education researchers who talk about an ecological view of classrooms. I guess they’re validating the whole field and it’s embrace of complexity and systems thinking. But it’s something. I think linguists have adopted the phylogenetic views of branching and extinction. I think many fields including linguistics have adopted diversity as a central object of study. Maybe resilience too? When i think about the economic work on the stress consequences of poverty it has a lot of parallels with the ecology of fear even if they haven’t directly borrowed from each other.
Scott, I had your work on TMIIs in a related post on DE 1.0! https://dynamicecology.wordpress.com/2014/04/07/what-do-you-think-is-the-biggest-recent-conceptual-advance-in-ecology/
I think it’s a little bit of A (less low-hanging fruit), B (hard to recognize new ideas right away), and E (old wine in new bottles).
As for new ideas that took off in the 2010s, how about intraspecific trait variation? There were a couple of influential papers in TREE in 2011 and 2012 — surely you remember one of those, Brian!
I’ve still got some good money on C (incentive structures antithetical to big thinking), but that is very pessimistic, so I’m glad to hear others think differently.
I think intraspecific variation is an excellent candidate for something that was long ignored in ecology and finally getting it’s due. You could go from Bolnick et al’s 2003 Mercer award winning paper right up to (at least in some senses) today’s talk in the Theoretical Ecology Webinar (https://iite.info/seminar/) by Robin Snyder.
And yes, Viva la variance! I’m always amazed how there were so many hypotheses put out in the paper about how to measure and interpret intra-population and intra-species and inter-species variation that have mostly been ignored and that paper just gets cited (very frequently) as a generic reference for intraspecific variation. Which I guess sort of proves your claim of intraspecific variation as a big idea.
Let’s go further back, to the great work by D.S. Wilson in this area — typically I think overlooked. E.g. Wilson, D. S. 1998. Adaptive individual differences within single populations. –Philosophical Transactions of the Royal Society of London Series B-Biological Sciences 353:199-205.
The tremendously interesting concept of epigenetics and how this is seen in wild populations may have an important impact on how we interpret and assess several ecological phenomena. For example:
https://academic.oup.com/icb/article/60/2/267/5825282
Good suggestion. Although I know it is really different, your suggestion of epigenetics also made me think of microbiomes, which was Meghan’s answer to a ten year old iteration of this post by Jeremy which I can’t believe I forgot to link to.
Here’s one I’ll put some money on: size-structured population dynamics. It hasn’t caught fire yet (though André de Roos has been working hard), maybe because the math is more daunting than a couple of ODEs. But it reflects the uniquely biological process of individual development from newborns to adults. How can we even think of modeling populations without acknowledging this almost-universal fact? (speaking rhetorically of course 😉
Size- structured pop dynamics is big in Fisheries biology; see work of Ken Andersen, and his princeton monograph in pop biology: 11-BR Michel [Cybium 2019, 434]_0.pdf (sfi-cybium.fr)
Thanks, I’m quite familiar with Ken’s work but it should be much more widely known! I think that size-structured population dynamics shouldn’t be seen as some esoteric theoretical development, but could move central stage in our thinking.
Your comment got caught up in the new overzealous spam filter unfortunately. I guess the challenge is to incorporate the right level of complexity. But size structure seems central. Some phenotypic variation might also be important.
I think C, but would add “short term thinking” as a key problem. Here in Australia everything needs to have a clear public benefit within ~5 years to get funded, which means that blue sky thinking is pretty rare. Even our undergrad teaching has become short-term with a focus on “job ready graduates”. Add “overload” to that (resulting from substantial staff decreases through covid and a massive increase in admin), and we’re all running around so much with our hair on fire trying to get it all done that it’s hard to take a breath and actually get any thinking time. HOWEVER, I think it is easy to look back with rose coloured glasses and focus on the outstanding successes – I think that average research and teaching quality have actually gone up dramatically over the last 25 years.
“I think it is easy to look back with rose coloured glasses and focus on the outstanding successes – I think that average research and teaching quality have actually gone up dramatically over the last 25 years.”
This is a very interesting remark, Angela. I wonder about this a lot, and not just in the context of ecology. It connects up with the question of whether a scholarly field should be judged by the very best work in the field (e.g., “classic” papers), or by typical work in the field. I have an old post on this, drawing on an old New Yorker article that asks the same question in the context of literature: https://dynamicecology.wordpress.com/2019/10/23/should-we-judge-a-scientific-field-by-its-classic-papers-its-typical-current-papers-or-its-best-current-papers/
Yes, I agree. Without the genius major leaps, a field makes progress like lichen over a rock. Would recreating the types of environments that spawned major insights in the past work today? Perhaps a program that recruited talented young musicians/scientists/writers and sent them on a multi-year ocean voyage in a small ship?
I realize the time scale is too far back to meet your date demands, but the rise of ESS thinking must rank high as a great new idea and/or question. Its origins go back to early sex ratio theory[ 1930s-1970s], and the habitat selection theory[ ideal free distribution] of the late 1960s, but the real revolution was in the early/late 1970s. Anyone who doubts that theory in ecology can work out should pay particular attention to ESS ideas, and for data to back up the insights, sex ratio studies.
I mention it since there is a bang-up history of those early days, written by an historian of science, and GA Parker [ one of the early pioneers], and based on interviews with several theoretical/data-based pioneers. The history paper is here: The early rise and spread of evolutionary game theory: perspectives based on recollections of early workers (royalsocietypublishing.org)
Them were exciting days.
Without quibbling on time frames, I would have to agree the ESS was a big contribution. In addition to all the examples in sex ratio theory (which is the real world example I use when I teach ESS) and behavior, it has crept into community ecology pretty heavily under the notion of invasability (where an ESS is an uninvadable strategy that – in most definitions – is an attractor). Chessons’ coexistence theory is arguably an ESS strategy over the time-scale/process of community assembly (rather than species evolution).
And “Them were exciting days.” is exactly what I personally feel is missing these days and why I wrote this post.
I think early on there was also some “demographic stochasticity” in research due to fields being smaller. But overall I’d vote for “A” as what’s mostly going on throughout science. And I’d add the the early “low-hanging” fruits were very broad & big but many of them were not all that tasty. Meaning, many of them were strongly predictive in some systems (and based on that became famous) but weakly predictive in most systems. Which is totally fine, I just like working in the era where (1) we’re explaining more and more dynamics in specific systems but also (2) recognize the primacy of context-dependency. Eg, we know that a handful processes often dominate the dynamics of a given population, but which handful it is depends on the system.
Very interesting question to ponder. I think of these as theoretical frameworks, and what’s interesting about them is that they are often themselves not really tested (the way we traditionally think of testing theory) but more taken to be good enough to be useful. For me a fairly recent example is Modern Coexistence Theory – has quite a big following and is a way of thinking about the world. Also the Metabolic Theory of Ecology fits the bill, as someone else mentioned.
Very interesting point. I think big ideas earn their keep more by how many new ideas they generate. Not as a hypothesis that is successfully directly tested.
Agreed. Although it’s often worth seeing if some of the major assumptions underlying the big idea can be tested. Which has been done for many of the big ideas above and can lead to the refinement or development of the theory. For Modern Coexistence Theory an example is: can this framework actually predict patterns (e.g. co-occurance) that we see in nature? Very rarely tested.
A quick note on the Park et al. (2023) paper cited as evidence that each unit of evidence is becoming less disruptive: a recent preprint argues that the main finding of that paper is an artifact of mistakes in data analysis. I have not evaluated really the evidence myself, so I don’t want to claim that the preprint is right, only that the jury may still be out.
https://arxiv.org/abs/2402.14583
Thanks for the caveat.
I would argue that one big idea is that we’re finally reaching the point where we can start to explain how some plant communities work in physiological terms. (I’m not sure about animals or microbes—I’d love to hear from animal/microbial ecophysiologists!) The way the story takes form in my mind, correctly or not, is that ecophysiology was mostly focused on autecological themes for a long time due to technical limitations on measuring both physiology itself and environmental variables at fine scales. However, there’s been really steady progress on those fronts for the last few decades, which I think bring us closer and closer to the point where can predict not just how species respond to their abiotic environment, but how whole communities respond to their abiotic environment and to each other.
There are a spectrum of approaches here. On the one end, you can treat certain physiological measurements as just “hard” functional traits, which can be useful but isn’t necessarily a big new idea. There are a number of studies which use broad survey measurements of turgor loss point or other such traits to get at questions about community assembly through space and time. On the other end, you can try to fit an integrative physiological model of an entire (usually still rather simple) community. Off the top of my head, one example of a study on this end might be Mas et al.’s new-ish paper in New Phytologist (https://doi.org/10.1111/nph.19358) where they use the model SurEau to predict how oaks and beeches would alter each others’ mortality risk under drought. Unfortunately they don’t actually end up testing the predictions, but I think it’s a nice demonstration of what might be possible in the future. Among other things, thinking physiologically could allow us to (for example) explicitly account for environmental dependence in the strength and direction of species interactions.
There are definitely limitations (some very strong) to how much we can currently use physiology to understand complex communities in complex environments, which I could expand on. But I’m optimistic, perhaps too optimistic, that putting ecology on a more physiological basis can help to tame the lawlessness of community ecology. I think a lot of the power of this approach comes from the fact that it rests on a set of general physical and chemical principles that govern how plants work; maybe the solution to physics envy is to become a physicist!
The vision of building community ecology from physiology (and behavior for animals) is very compelling. And it’s been around a long time. I’m thinkingnof a paper by Schoener (1972?) that articulated it. But it’s very cool to hear it’s starting to come to fruition! Some of the trait community assembly work fits this too.
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With the soon-to-be-obvious caveat that I, like all scientists, am biased, I’m going to go with option B: there are new big ideas and questions that most ecologists are missing. Part of the reason is that our search image for big ideas and questions are more social than scientific. As mentioned, ecologists often search for how ideas and questions change the way we see the world or how much agreement there is that they are indeed “big.” Such changes and agreement can often be independent of or even inhibit scientific progress. A more scientific perspective would focus on the generality and predictive precision of theory…contributions made by ideas like F=MA, the periodic table of elements, the transcription-translation dogma, etc. This is where the metabolic theory of ecology (MTE) is most impressive as vividly illustrated by the 12 orders of magnitude of body size that it’s largely consistent with the data. However, it suffers on at least two major counts. One is imprecision e.g., the several orders of magnitude of variability around the central three-quarters power law scaling. The other is that it’s not particularly ecological. Its scope is more physiological emphasizing metabolism and productivity rather than focusing on the more ecological structure and function of ecological systems. Yet more issues are its MTE’s questionable mechanistic basis (just a regression?) and its failures at smaller scales and for many phylogenetic subsets of species. Still, I agree that emphasizing the successes of big ideas wherever we can find them more accurately identifies their scientific contributions and often provides more promising avenues for further inquiries.
In that spirit, I’m suggesting that the scaling up of detailed interspecific interactions to whole systems that “gained steam in the 2010s or 2020s with initial papers perhaps a decade older” is the idea that is being missed yet fulfills many of the goals mentioned on this thread and, more importantly, quite generally and precisely predicts the structure and function of ecological systems including populations, communities and ecosystems. Building on food-web theory of the 90’s, theory formalized by the niche model, beginning in 2000, has quite precisely predicted key attributes of complex food webs in freshwater, marine, and terrestrial habitats containing a huge diversity of species. Perhaps the most significant of its successes is its ability to predict the variation (s.d.) among coexisting specialists and generalists to one and often two significant digits. The niche model performs similarly for variability of vulnerability and among key measures of trophic overlap such as the average similarity between each coexisting species and its most trophically similar partner. Furthermore, it was able to do this for extremely well-studied paleofoodwebs a half billion years old. The mechanistic basis for the theory are two-fold. One is that species occupy a hierarchy that is thermodynamically constrained according to all heterotrophs dependence on autotrophs. (duh…) The other somewhat less obvious basis is that heterotrophs that eat more than one species are physiologically/evolutionarily constrained to consume within a more or less contiguous area of this hierarchy. Less well developed is theory of mutualistic networks (e.g., nestedness) that has been actively building steam in recent decades and is also an important part of my suggestion that the scaling up of detailed interspecific interactions to whole systems is an important candidate for a new big idea in ecology.
Perhaps more in line with establishment ecology is the extension of network ecology to the dynamics of ecological systems. Building on Yodis’ and Innes’ 90’s bioenergetic reformulation of Rosensweig’s and MacArthur’s theory of predator-prey interactions, MTE has been incorporated into food web theory to understand and predict the dynamics of populations, communities and ecosystems. It introduced itself by ritualistically beating the very over-dead horse known the diversity-stability “debate” (or does Hattin et al. 2024 elevate that horse to zombie status?). In any case, like very many other ideas, what has become known as allometric trophic network (ATN) theory showed that adding almost any realistic aspect of ecological networks yields vastly more stable systems than the randomly and linearly interacting species in the networks that ushered in the debate. In ATN’s case, those aspects were the more realistic network structures supplied by the niche model parameterized by consumer-resource body-size ratios observed in nature and metabolic, consumption, and production rates supplied by MTE. ATN seems to work well with empirical network structures and parameters derived independently from the niche model and MTE but doing so obscures many of the most important contributions of ATN theory including its generality and tractability.
Some good examples of the steam ATN theory has gained include successful quantitative predictions of the effects of species removal in the field on the abundance of the remaining species. Such quantitative prediction of interaction is a major advance beyond the keystone species concept where multiple experiments in particular contexts were needed to qualitatively identify whether or not a species is a keystone. Similarly, ATN theory pushed forward three decades of qualitative plankton ecology group theory towards quantitatively predicting the seasonal dynamics among many species in a freshwater lake. More recently ATN theory is incorporating non-trophic mechanisms such as environmental variability (e.g., stochasticity), maturation (e.g., life stages), reproductive services (e.g., pollination, see dispersal), evolution (e.g., sympatric and allopatric speciation and extinction), and the ecology and economics of humans interacting within ecosystems. This points to perhaps the ‘biggest’ aspect of big scientific ideas: unification. ATN theory almost seamlessly integrates ecological subdisciplines from physiology to ecosystems.
Those are all a bunch of big claims if not big ideas described in my 2020 review of ATN theory: https://www.frontiersin.org/articles/10.3389/fevo.2020.00092/full Before taking issue with them (please do!), folks might want to see if the issue has already been sufficiently addressed.
Still, there are other criteria for big ideas in this thread that are relevant. Perhaps my favorite is how much ideas have influenced other fields. Indeed, the influence of May’s stability-complexity theory on general systems theory in many fields may be the most outstanding ecological idea in this regard. ATN theory has had significant influence on the huge and rapidly growing field of network science including many of the fields that science now forms an important part. For example, ATN theory has advanced and refined central network science theories about small worlds and scale-fee networks, the subjects highlighted on multiple covers of Science and Nature in the last few decades. ATN theory has also helped show how understanding the mechanisms responsible for network structure and function, as opposed to less deeply understanding their statistics, can significantly improve network science.
So, the scaling up of detailed interspecific interactions to whole systems, most specifically ATN theory, is my big idea candidate for choosing option B. Another candidate should be Maximum Entropy Theory (John Harte et al.) but I think its contribution lies more in the “null model” mold of big ecological ideas (another essay). So yah, option B and Allometric Trophic Network theory as a candidate for an ignored idea. Any votes for or against?