Population and community ecology: past progress and future directions

Abstract

Population and community ecology as a science are about 100 years old, and we discuss here our opinion of what approaches have progressed well and which point to possible future directions. The three major threads within population and community ecology are theoretical ecology, statistical tests and models, and experimental ecology. We suggest that our major objective is to understand what factors determine the distribution and abundance of organisms within populations and communities, and we evaluate these threads against this major objective. Theoretical ecology is elegant and compelling and has laid the groundwork for achieving our overall objectives with useful simple models. Statistics and statistical models have contributed informative methods to analyze quantitatively our understanding of distribution and abundance for future research. Population ecology is difficult to carry out in the field, even though we may have all the statistical methods and models needed to achieve results. Community ecology is growing rapidly with much description but less understanding of why changes occur. Biodiversity science cuts across all these subdivisions but rarely digs into the necessary population and community science that might solve conservation problems. Climate change affects all aspects of ecology but to assume that everything in population and community ecology is driven by climate change is oversimplified. We make recommendations on how to advance the field with advice for present and future generations of population and community ecologists.

Population and community ecology are the foundation elements of the ecological sciences. After a centenary of progress in these developing sciences, we review the strong and weak points and how to progress with nine key recommendations for future research.

INTRODUCTION

When Charles Elton wrote his Animal Ecology text (Elton 1927), ecology was just emerging as a science. Practical insect ecology and fisheries management were already in their youth, and Elton had already been to Svalbard (Summerhayes & Elton 1923) and was writing a review of periodic fluctuations in animal populations (Elton 1924). Much has been achieved since Elton's time, and many critiques of ecological progress have been presented from many perspectives (e.g. Peters 1991; Hone et al. 2023), but the focus has been specific rather than general about the state of the population and community ecology as a science. We ask a simple question: What has the population and community ecology achieved in the last century, what are its foundations today, and where should it be headed? We learned long ago that sciences do not march forward with unrelenting linear progress over time, but that we all face some successes and failures and always the need to return to a critical assessment of where we have been, where we are today, and where we might be headed. It is in this spirit that we offer this critical review of the current state of this part of ecology, and we hope that it will stimulate discussion since we have no pretense of complete knowledge.

The science of ecology comprises three critical threads: theoretical ecology, statistics and statistical models, and experimental ecology. Each of these threads can be divided into the three major foci of ecology: population ecology, community ecology, and ecosystem ecology. We concentrate here on population and community ecology and focus on understanding the reasons behind the distribution and abundance of organisms, why these can change over time, and how they interface with the human impacts on the globe.

We discuss here ecological progress from the viewpoint of multicellular organisms because that is our experience. We do not discuss the important areas of microorganism ecology because the ecology of viruses, bacteria, and fungi is a very different and critical area of ecological science that operates on a different time scale and thus needs a separate review.

NATURAL HISTORY

We sometimes forget how much we ecologists owe to natural historians who map the details of the ecological background of individual species. Where do they live, when do they breed, what does this organism do in the community, what it eats, and who eats it? Many authors have echoed this point (Schradin 2017; Travis 2020), which is important as a background to good analyses in ecology. So, the first question to ask when you begin a research program is this: what do we know about the natural history of the organisms we study?

Much of the natural history literature on plants, insects, and vertebrates qualifies as simple observations, level 0 in Table 1, and does not qualify as science as defined by Platt (1964). Natural history studies provide no framework for hypothesis testing a priori as has been declared essential to ecological science (Peters 1991; Hodges 2008; Sugihara et al. 2012; Nichols et al. 2019). Natural history never asks the question “why,” and hence it cannot produce predictions or test hypotheses. Nevertheless, the data gathered in natural history studies must be subject to the rules of reliable observations to be repeatable. While useful, natural history is not an ecological science and should not be considered as a substitute for proper ecological research.

Table 1.

Ranking the four levels of the strength of causal inference in science

Strength of evidence	Method 1 Simple observations	Method 2 Experiments with hypotheses	Method 3 Hypotheses with parallel data	Method 4 Observations with predictions	Method 5 Manipulated experiments with validation
Zero	Association	Association		Association	Association
First order strength	Timing	Experiment	Direct evidence	Unique mechanism and timing	Experiment with change and timing
Second order strength	Direction of change	Mechanism	Mechanism	Validated predictions	Unique mechanism
Third order strength			Parallel evidence replicability		Validated predictions

Research in ecological science should be ranked by these four levels of increasing evidence to determine cause and effect. All five methods assume a clearly specified hypothesis and alternative hypotheses. Methods 1–4 represent proposals from philosophers of science. Association = observation, timing = cause must precede effect. Methods 4 and 5 are modified from Hone and Krebs (2023). We should aspire to Method 5 but cannot always achieve that strength of evidence.

Natural history investigations can also suffer from the problem of variation within the same species in different habitats as well as variation over time as the biomes of the world shift because of human disturbance and climate change. Natural history faces becoming outdated in an era of climate change and possibly of limited value. Ecological science is very much like physics and chemistry, in that we have general laws that govern the way ecology works (natural selection, basic population dynamics, and energy pyramids to name a few). These general laws are going to apply every bit now as well as in a world changed by climate. In summary, natural history data can be useful but may or may not be necessary as a starting point for ecological research which asks “why” and tests hypotheses as outlined in Platt (1964), Peters (1991), and Kimmel et al. (2021).

PHILOSOPHICAL BACKGROUND

Population and community research must be driven by the common scientific assessment of cause and effect. There is a very large literature on cause and effect that is important for all the sciences to link to the philosophical literature about causality and the very general issue of what we mean by evidence in science (Platt 1964; Pearl 2009; Sugihara et al. 2012; Kimmel et al. 2021; Hone & Krebs 2023). Table 1 provides a summary of this discussion that classifies scientific inferences into five levels that indicate increasing evidence of cause and effect. We can use this table as a guide to the strength of evidence that all our population and community research literature brings to bear in defining progress in understanding how and why populations and communities change.

THEORETICAL ECOLOGY

The usual application of theory in science is to explain empirical observations, and the history of ecology followed this route for many years, peaking in the interval of 1965 to 1990 with a large set of excellent mathematicians attempting to place a theory over the messy world of empirical ecological data. In our experience, this has been a mixed success partly because theoretical progress has exceeded empirical research progress. So, by the 1990s, we had a full basket of verbal and theoretical models that had an uncertain relation to the real world. This discrepancy could be blamed partly on the empirical ecologists who live in a world of imprecise data and long time frames to conduct real‐world studies and test the validity of the theory. Assumptions implicit in ecological theories should be grounded very clearly in the real world (Ginzburg & Jensen 2004). Theoretical models must be subject to empirical testing. One good example of how this should work regarding competition theory is presented in Abrams (2022), who delivers a trenchant review of the failure of competition theory to fulfill its initial promise as a key process in ecology. Theoretical models as a key point of ecological science were inspirational when ecology was a young science and has since moved to an elegant scientific platform that has helped ecologists to solve the major ecological questions of our time.

One of the difficulties facing all ecologists is that theoretical ecology must develop specific connections between theoretical ecology and empirical ecology, which too often may live in separate worlds of research. Theoretical ecology has established a firm foundation for the science of ecology and serves as a platform for understanding real‐world evidence.

STATISTICS AND STATISTICAL MODELING

The statistics and statistical modeling threads of ecology have provided a sound basis for designing and analyzing empirical ecological research and have worked well to improve the rigor of empirical ecology. Statistical methods, in particular, have aided in developing better experimental designs and more precise methods of estimation of ecological parameters. The literature on the use of statistics in ecology is far too extensive to review here, so we can suggest only a few recent reviews to cover this point (Low‐Décarie et al. 2014; Yen et al. 2015; Pearce & Lawlor 2017; Castilho & Prado 2021). One clear example has been the changing landscape from the early methods of population estimation from the 1930s (e.g. Lincoln Index, Jolly‐Seber model) to the present rigorous mark–recapture methods (Pradel 1996; Laake et al. 2011; Grimm et al. 2014; Nichols 2016; Efford & Boulanger 2019) and new approaches to use camera data to estimate abundance (Luo et al. 2020; Becker et al. 2022; Kenney et al. 2024). All the statistical advances of the last century have provided a strong foundation for the estimation of ecological parameters necessary for understanding ecological change and building realistic models.

Modeling of ecological systems is a bridging discipline that brings together theoretical ecology, mathematical rigor, and statistical sciences. Models in ecology have evolved from simple descriptive word models in two directions to rigorous mathematical models and statistical models. Mathematical models in ecology have a long history, and they have evolved from the simple models of Lotka and Volterra to the more complex models of Robert May (May 1976, 1999). The insights of mathematical models have produced for ecology a rich vision illustrating the complex outcomes that can arise from simple assumptions. Mathematical models up to the present time have been most successful for population ecology, which has a rich background of simpler questions involving single‐species dynamics. Community ecology struggles to use mathematical models to guide research because the complexity of multi‐species interactions tends to overwhelm the ability to achieve models that can guide field research on whole communities. Mathematical models have led applied ecologists into the world of statistical models that can be applied to empirical questions in conservation, wildlife and fisheries management, and pest control. Good statistical models are useful because they force us to be explicit about hypotheses and definitions and tell us what we need to measure to produce evidence to explain and test our understanding of ecological changes. Statistics follows through with the details of how to measure the modeled parameters accurately. The biggest difficulty is to confuse theoretical and statistical models with reality, so testing models is a critical aspect of improving ecological understanding (McCrea et al. 2023). A second major problem with statistical models is that it is too easy to include parameters in models and functional relationships that are impossible to measure in the real world (Ginzburg & Jensen 2004; Ginzburg & Damuth 2022). Our impression is that statistical models in ecology are becoming more sophisticated by the inclusion of parameters more rapidly than the actual data can be collected to validate them (Nichols et al. 2019). We have many models that lack the data that must be collected to test and apply them.

EXPERIMENTAL ECOLOGY

Experimental ecology is where mechanistic hypotheses, models, and management approaches of ecological science are put to the test. It is where “beautiful hypotheses meet ugly facts” (Chitty 1996) and in it, the value of ecological science in solving problems in the biosphere is most exposed. In reviewing the problems of experimental ecology, we must include all the Earth's problems in which ecological scientists agree on a solution, such as exponential population growth, water pollution, and overfishing. As an example of this situation, you can look at the growing human population of the Earth and the conclusion of most ecologists that we have already exceeded the carrying capacity of the Earth (Wackernagel et al. 2021). We emphasize that ecologists can play a key role in suggesting solutions to solve many of these political/ecological problems, but our solutions too often come up against political and social walls that emphasize humans rather than the biosphere. It is not for lack of scientific information that prevents a remedy for these important global problems.

We will provide here a broad overview of two subdisciplines of experimental ecology—population and community ecology—separately because they differ greatly in their achievements in understanding and protecting biodiversity.

Population ecology

Population ecology is a strong part of ecological science because it asks what is happening to individual populations of a single species in terms of changes in distribution and abundance. Population ecology has a strong background in mathematical models to focus thinking and an equally strong background in the design of experiments. By concentrating on a single species, it concentrates all the methods now developed to measure accurately demographic parameters and makes it possible to increase understanding in time for management actions. It merges with community ecology in the linkages of the chosen species or population to the food web and the interaction web of indirect effects.

Many excellent population studies serve as models of what can be done in single‐species studies. They range from studies of African wildebeest by Sinclair et al. (1985), moose by Gasaway et al. (1992), lemmings by Fauteux et al. (2016), and boreal forest grouse (Wegge et al. 2022), among many other papers. The three qualities that have served all these as models of population studies are the ability to census the population precisely; the ability to study marked individuals to obtain birth, death, and movement rates; and often the ability to carry out field experiments on potential limiting factors (Kelt et al. 2019).

Population ecology is now seen most strongly in conservation biology and the management of wildlife and fisheries. Unfortunately, conservation biology is time and funding limited so that the required field and laboratory research is hard to carry out, especially over the long term and experimentally. Hence, it is difficult to answer the simple question of how to diagnose the conservation problem of a declining population. It was most eloquently formulated by Graeme Caughley (1994). His fundamental insights were elaborated with examples in Caughley and Gunn (1996). Many of the problems of conservation deal with animals and plants that were abundant at some point and are now declining. For most of these conservation issues, ecologists have solutions but they are compromised by human population growth, politics, and habitat destruction and are thus difficult to implement successfully. For the other set of animals and plants, given that there is superabundant evidence that most species are rare, it is most difficult to specify conservation action because it is very difficult to study rare species in most ecosystems. Consequently, the general solution for the conservation of populations is to establish national parks and reserves in the hope that there will be something left within the next century if we can set aside large enough areas. The prognosis for this approach is not good as shown elegantly by Newmark (1985, 1995) for Yellowstone and other National Parks in the United States and more recently by too many protected areas around the world (Maxwell et al. 2020). The dilemma of protected areas is that they protect the present rather than the future considering climate change. The final solution for biodiversity science is to put endangered species in zoos and save some DNA so that in the future we can reconstruct the biological world. There is much interesting research being done on conservation issues for single species, and this will solve some problems in the short term and generate interesting science, but we have currently lost the big picture of how to use ecological science to prevent biodiversity loss, given that the solutions needed are often social and political (e.g. the destruction of the Brazilian rainforest). Climate change is at present the most pressing issue, which has raised the conservation issue into public awareness, but present progress in addressing conservation issues is slow.

Management actions for fisheries and wildlife are also difficult but not as impossible as conservation issues. Fisheries and wildlife managers are typically concerned with abundant species of economic interest, so all the tools and methods of population ecology developed over the past 80 years are a certain guide in how to do research properly (e.g. Walters & Martell 2004). However, if conservation programs are driven more by conservation interest groups rather than by academics (see Tinsley‐Marshall et al. 2022), wildlife and fisheries management is largely driven by government agencies and the hunters and fishers who rely on proper management for their livelihood. If this is the case, why are there so few cases of good management? Part of the answer would appear to be in funding and politics. If Western governments spent as much money on conservation, wildlife, and fisheries problems as they currently do on subsidies to energy companies and human health and social issues, we might be able to remove at least one impediment to applied ecology—“we do not have enough money to do this.”

Ironically, if there was any part of population ecology that was most amenable to experimentation, it would be many of these conservation and management issues. Economics certainly constrains many possible solutions, and the tendency is for governments to allow destructive practices and then, after the problem is highly visible, ask ecologists to solve the problem with inadequate funding and limited options. If you need an example, consider the overharvesting of timber by forestry companies (Price et al. 2021), which has led to declining caribou populations in Canada (Nagy‐Reis et al. 2021), or fisheries management problems (e.g., Hilborn et al. 2015; Costello et al. 2016; Rose & Walters 2019). There is a solution for these problems within the science of ecology if we adopt proactive adaptive management (Walters 2007; Westgate et al. 2013; Serrouya et al. 2019), which carries the strengths of population ecology into community dynamics by means of experimental approaches. As concerned citizens, ecologists need to do their part to encourage the public and politicians to make ecologically informed decisions, which is essential to putting conservation and resource management on a proper sustainable course.

Community ecology

Community ecology began as a descriptive science nearly devoid of what would now be called level 0 or level 1 science (Table 1). Partly this was due to the critical need for much essential descriptive natural history to be done on the species composition of communities and how that varies in space and time. However, there has been a shortage of a set of basic questions that community ecology has focused around. To be sure there are a whole set of questions that both plant and animal ecologists focus on, but they continue to be descriptive, vague, and/or untestable: What is a community? How can we best measure biodiversity? Does biodiversity lead to stability? How can we define the niche of a species? Should we analyze the community as units or as a continuum? Many of these types of questions in community ecology led Peters (1991, table 1.3) to despair of any progress in the science of ecology. He was criticized by many of the leading ecologists of the day, but we would encourage aspiring ecologists to read his book without bias to see what valid points Peters made and the need for testable hypotheses in both population and community ecology.

Plant ecologists have often developed a highly descriptive approach to community ecology that has led to much descriptive plant ecology but always with the assumption that if we define the physical and biotic parameters of a plant species’ niche, we will be able to predict future community changes (Austin 1999a, 1999b). Much progress has been made along these lines, particularly for trees, but all these descriptions suffer from the question of whether the regressions of the present will allow us to predict the communities of the future (Van Niel & Austin 2007; Hong et al. 2022). There is only one way to determine this for any specific problem and that is to monitor populations and communities into the future so that we can determine if these vegetation models predict correctly under climate change. All empirical models are subject to these constraints of being correct for the past but possibly not for the future, and continued monitoring is an essential part of population and community ecology. Community ecology is hampered in time by the long time scale of data required to test hypotheses. These worries are illustrated by decisions about which tree species to replant in areas recently harvested or lost to fires as climate changes (Noseworthy & Beckley 2020; Frelich et al. 2021) and could be considered a long‐term test of conventional plant ecological niche theory. Turkington et al. (2014) illustrate a 20‐year experimental approach to plant community dynamics and show that important questions can be answered with long‐term studies in the field. However, understanding what drives communities and populations today may not be sufficient to predict the future structure of communities. Community ecology has led ecologists into the important area of restoration ecology that illustrates in a practical way how difficult it is to put simple concepts of community ecology into practice (Turkington 2009; Stanturf et al. 2014; Anderegg et al. 2020). Restoration ecology proceeds on a scale of tens to hundreds of years, so short‐term goals are difficult to set and continue to monitor, and thus may be difficult to defend (Hoffmann 2022).

A community can be defined by a food web or an interaction web. The major question that arises once this descriptive work has been done is how the species interact via competition or predation and what consequences these interactions have for community structure and composition. Paine (1992) was a leader in pressing experimentation on the complex community of the rocky intertidal food web by selective removal experiments. Paine et al. (1998) carried the ideas of disturbance further by imposing compound perturbations on his rocky intertidal food web, and they generalized these ideas to community recovery from compounded disturbances and the ecological surprises they entailed. The generality of Paine's conclusions was challenged by Foster (1990), which led to an open dispute of Paine's conclusions (Paine 1991). This dispute was interesting because it focused attention on the limits of generality from answers about community organizations obtained from local areas (Underwood 2000). What works in one part of the geographical range of a community may not work in another part with a different climate and different interacting species. Kearney and Hilborn (2022) provide a good example of this local versus global problem with respect to global fisheries. All ecologists must appreciate this fundamental limitation of local studies and global conclusions.

There has been a great deal of effort devoted to the describing of communities, particularly plant communities (e.g. Pielou 1984), but these efforts are always spatially limited, and a more descriptive recognition of community types has led to the discrete community/continuum controversy (Austin & Smith 1989). Broad patterns of plant and animal communities are easy to define on a map but nearly impossible to study. The boreal forest biome is a good example. Environmental gradients have resulted in mixtures of species in a local community, and all the attempts to recognize local communities as units of study have failed because of a cacophony of climatic changes, introduced species, and human disturbances. Experimental community ecology has fractionated with many plant ecologists going in the direction of continued description with only a small amount of experimental analysis while some plant and animal ecologists attempt to analyze animal communities experimentally (Turkington et al. 2014). Competition has been a focus of many of these community studies, and while field experiments of competition in communities have shed light on local problems (e.g. Tilman et al. 2006), the complete theory of competition between species remains unresolved (Abrams 2022).

The most recent development in community ecology has revolved around conservation, biodiversity, resilience, and stability. The last three of these critical concepts remain ill‐defined. Biodiversity is impossible to describe except for a specific taxonomic group in a circumscribed area or ecosystem, and therefore, any scientific statements about biodiversity should be specific. There is much research to be done here in taxonomy and natural history. So, we as scientists can only speak operationally of defined parts of biodiversity—mammals, birds, fish, insects, plants, fungi, etc.—which is good as far as it goes but leaves one of the biggest issues of our time—global biodiversity loss—difficult to discuss except in the most general terms with much handwaving. Williams et al. (2020) state this dilemma of ecological science for conservation elegantly by pointing out the lack of progress in conservation except in very specific cases, which are driven largely by population ecology rather than vague concepts of community ecology. Grimm and Wissel (1997) pointed out that there were 163 definitions of 70 different stability concepts, which tend to render the concept so vague as to be useless for scientific discussions about conservation. Hodges (2008) disagreed and pointed out that language evolves and that ecology can be stifled by strict definition. We think that part of the reason that community ecology flounders is that it floats too much on vague concepts rather than operational ones and relies on description rather than experimentation.

The Kluane project

To provide a concrete example, we would like to illustrate the difficulties of carrying out community ecology from our own work in the boreal forest of the southern Yukon in Canada (Boonstra et al. 2016, 2018). We began our studies in 1973 with a simple survey of how many species of small rodents were in a large area to be designated as a national park (Krebs & Wingate 1976), a very restricted biodiversity approach for only a small part of this ecosystem. This evolved in 1976 into trying to understand the causes of the snowshoe hare 9–10‐year cycle, a spectacular feature that occurs across the 5 million km² of Canada's boreal forest zone and was studied very early by Charles Elton (Elton 1933; Elton & Nicholson 1942). In 1977, we expanded our research into an experimental community ecology analysis of how this boreal forest food web is structured (Fig. 1; Krebs et al. 1986; Sinclair 1986; Smith et al. 1988). The food web shown in Fig. 1 was then subject in 1987 to several large‐scale experimental manipulations described in detail in the book by Krebs et al. (2001). In 1997, we expanded into further monitoring of a larger part of this community, along with smaller experimental manipulations of specific interactions in the food web (Krebs et al. 2023). Virtually, all our results of these studies are published, but what we want to highlight here is that after much research over 50 years, we are missing many elements in this analysis of Kluane food web species interactions. We progressed over these years from a simple observational approach to applying theoretical models of population dynamics to address the variables we needed to measure to add details to these models. This led us to the practical problems of applying statistical ecological methods to our data to answer particular questions of snowshoe hare dynamics and predator–prey models and trying to put all our data together to address food web dynamics. We are still addressing unknowns in how this ecosystem operates; so much is known but much is still missing from our understanding.

Figure 1.

Food web for the boreal forest in the southern and central Yukon. The species that have been monitored most closely are shaded. Only the major feeding linkages are shown (Reproduced/Adapted from Boonstra et al. 2018, with permission).

At the largest level, we could not study the large mammals like moose and bears in this boreal forest ecosystem because we had insufficient funding. At the smaller level, we did not have the expertise to do complete studies of some of the predators (e.g. weasels), the passerine birds, or the insects all because of a personnel shortage. Thus, we have been monitoring the abundance of many species for all or part of these last 50 years, but we have not been able to do community‐level manipulations on all of them to see how the food web would react to changes in abundance. In summary, we have devoted with the assistance of many students and other scientists about 500 person‐years of work to try to unravel the structure and function of this relatively simple food web. If you think that community and ecosystem ecology can be done quickly or simply, you will be very surprised at the necessary effort. Consider one simple interaction in the food web shown in Fig. 1—predation. One focus of our work has been on Canada lynx preying on snowshoe hares (O'Donoghue et al. 2010). However, for the present, we have data on kill rates only in winter, and we have very limited data on the lynx diet in summer. Complicating this are predators like coyotes (which appeared in this part of the boreal forest in the 1920s) who also prey on hares, great horned owls that we have data on for only one 10‐year period, and numerous predators like red squirrels that kill baby hares before they are 1 week old (O'Donoghue 1994; Stefan & Krebs 2001; Hodges et al. 2001), and numerous other predator–prey interactions like intraguild predation that ought to be part of the understanding of the role of predation in this community.

Snowshoe hares reduce their reproductive output during the decline phase of the 10‐year cycle (Keith et al. (1984). Two hypotheses could explain these reductions—food supplies or stress. We need in future to test both these mechanisms. We suspect that physiological stress produces these reductions in reproduction but do not know why without more studies of how stress from unsuccessful predator chases affects brain function (Sinclair et al. 2003; Lavergne et al. 2021). Many gaps thus occur in our research on this food web even after 50 years of study. We have reached level 2 of evidence (Table 1) and for some elements, level 3. Whether snowshoe hare 10‐year cycles will disappear with climate change cannot be predicted but can be detected with continued monitoring

The simple consequences of this brief example of one study system are that community dynamics and the understanding of the roles of species in communities are a lifetime + of work. In our Yukon work, we have little information on passerine birds or indeed any of the birds or insects, so we cannot address the widespread belief that bird biodiversity is in drastic decline (Rosenberg et al. 2019), or that insect diversity and numbers are also declining rapidly (Wagner et al. 2021). We, ecologists, continue to raise the alarm about biodiversity losses and potential losses from a worldwide database at which any reader interested in empirical precision will shudder.

One solution to these problems is additional funding so that environmental and ecological issues are funded at higher levels, but that is not all because the methods we currently use to measure simple items at a local level like species diversity, population density, and spatial dynamics are difficult, crude, and often of limited value for making management decisions.

One objective offered by ecologists for support is that we can make reasonable predictions about the future state of the planet. Our take on this goal is that it is identical to that of medicine attempting to predict human health issues in the coming century. The goal of our Yukon studies has been modest—to make some predictions about the state of this community over the next decade. One thing is certain, the future of ecological systems will not be like that of the immediate past, and on the human time scale of about a century, we have limited vision amid all the talking.

CONCLUSIONS

Much of current community and ecosystem ecology focuses on climate change (Jones & Driscoll 2022) and the main approach seems to be to look backward with the information of physiological ecologists and forward with the climate models from the IPCC. One result is that climate change research is correlational rather than experimental and is confounded by rapid environmental changes. In most cases, we have achieved only level 1 evidence (Table 1). Two major exceptions to this statement are the aquatic experiments pioneered by David Schindler (Schindler et al. 2008) and Steve Carpenter (Carpenter et al. 2009), who have evidence that reaches levels 4 and 5 of Table 1. That climate change affects the dynamics of populations and communities goes without question (Wan et al. 2022) but also without clear solutions. Not all ecological problems can be investigated with manipulative experiments, but evidence from observational experiments can reach levels 1 and 2 of Table 1 and greatly increase our ecological knowledge.

Experimental ecology is not currently limited by theoretical ecology or statistical ecology but rather by limitations in two dimensions—funding, and experimental facilities. Experimental facilities for laboratory research are expensive, and sites for field investigations are rarely left undisturbed by human landscape alterations. Funding shortcomings are set by time limits on funding long‐term problems and the required funding to address needed conservation and management actions. Funding in ecological research is limited by a piecemeal approach with little vision to address large problems. Universities are trained to produce ecologists that study small problems that can be addressed in 2–3 years with graduate and postgraduate students. A larger issue is the shifting baseline of ecological science where because of climate change and human exploitation of ecosystems, critical questions change more quickly than they can be solved. Ecologists propose solutions to environmental problems, but corporations and governments may have a different agenda for change. This conflict is partly because the research agenda of ecology is long term and global problems demanding solutions arise short term but can be solved only by long‐term research.

Many people appear to wish to keep their local world the same as it always has been in the face of shifting climate niche envelopes, immense human alteration of the land and water base, and emphasis on continued growth as the human model. There are limited ecological solutions at the local level as long as societal priorities continue as they are. Ecological research can never provide “solutions” under the current eternal growth paradigm, but it may help to allow for “ecologically informed decisions” as public awareness grows and sustainability prevails. There is a clear path to alleviation of climate change, but it requires drastic actions for governments and citizens that we ecologists can strongly recommend but do not control.

Anthropogenic threats to biodiversity are too great to survey and are another subfield of population and community disturbance ecology. The question is: What is the best method for getting evidence that could guide conservation action (Christie et al. 2022)? The principles for getting evidence for conservation are well described by Christie et al. (2019), and there is an increase in the understanding that conservation action must rely more on ecological knowledge than on casual observations. Most of the papers that deal with the long‐term restoration of ecosystems from anthropogenic disturbances have little more than a guesstimate of the time frame. Restorations on site will fail when climate shifts, and we may need to move entire communities to a new site in the new climatic optima, a nightmare scenario that we are only now beginning to face (Ferreira et al. 2019).

Moreno‐Mateos et al. (2020) discuss a restoration science operating for centuries to millennia to restore a degraded ecological landscape to somewhere near normal function. Discussing ecological recovery on such a long timescale makes it impermeable to the current time scales of data collection. Despite all these problems, trying to reverse the consequences of human‐caused disturbances is vitally important for conservation. Important success stories like that of removing rats on islands (Jones et al. 2016; Duron et al. 2017) and creating fenced havens from introduced cat and fox predators (Legge et al. 2018) need to be multiplied and enlarged to spatial scales that are rarely considered possible with our current budgets. Ecological restoration has population and community effects but the methods of achieving restoration rely heavily on physiological ecology and population ecology, including censusing methods combined with designating protected areas where disturbances can be regulated (Fitzgerald et al. 2021).

SOME RECOMMENDATIONS FOR EXPERIMENTAL ECOLOGY

We offer some recommendations with this caveat in mind.

• ‐Decide for your area of interest what the big questions are. Not all will agree on what these are but concentrate on a few that are critical.
• ‐Place any future natural history work within the broader context of cause‐and‐effect research.
• ‐Focus on the hypotheses of interest and their alternatives and on the evidence needed to test them.
• ‐Validate your measurement methods rigorously relative to past studies to ensure that present findings are ground‐truthed.
• ‐Determine what the critical experiments are. These may be large or small‐scale, multidisciplinary if possible, and involve a cohort of collaborative ecologists.
• ‐Find the funding from a source that thinks big and long‐term. This rarely involves the normal scientific granting agencies, which too often operate on a short time frame.
• ‐Now look for the best ecological methods available to answer your question. Methods are critical, and statistical models and designs are essential.
• ‐Now go back with your team and go over all this again. Build a model if you can to go over your conclusions. Find a good statistician as a critic.
• ‐Work hard. If you wish to do ecological science for the sake of conservation, be fully aware that some but not all of your research may be the deciding factor in what happens going forward. Conservation is an extremely difficult goal to achieve but a necessary one.

CONFLICT OF INTEREST STATEMENT

We have received no funding to complete this paper. We have no conflicts of interest. We have no competing interests in the material in this paper. We have no financial or proprietary interest in this article.

Krebs CJ, Boutin S, Boonstra R (2025). Population and community ecology: past progress and future directions. Integrative Zoology 20, 2–14. 10.1111/1749-4877.12863