Are there big ideas or new big questions in ecology any more?

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).

1. 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.
2. 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.
3. 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:

1. 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.
2. 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.
3. 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).
4. 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.
5. 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?