1 Why a hard science needs strong critique
Roger Cousens 
How to cite this chapter
Cousens R. D. (2023) Why a hard science needs strong critique. In: Cousens R. D. (ed.) Effective ecology: seeking success in a hard science. CRC Press, Taylor & Francis, Milton Park, United Kingdom, pp. 1-12. Doi:10.1201/9781003314332-1
Abstract This chapter sets up the book. It gives various reasons why ecology is, and always will be, a difficult science. The case is made for ecology to be judged by its ability to provide answers to specific questions. The researcher’s task is to design and implement a pathway that will effectively lead towards a reliable conclusion. However, our research often lacks clear goals, making it difficult to evaluate progress. An ongoing process – critique – is needed to evaluate our science, to identify weaknesses that we can work upon, so that we can improve the outcomes of future research. Finally, the chapter sets out the structure and objectives of the chapters that follow.
1.1 Why ecology is difficult
Ecology is one of the most difficult of sciences (though beware that there is a second definition of the term: Box 1.1). Many of the natural phenomena that ecologists study are of great diversity and complexity, and are inherently variable. There are so many different organisms, each with their idiosyncrasies in the ways that they live, occupying so many different environments. Every location on earth provides a unique set of living conditions, determined by their position on the globe and modified by regional and local geology and geomorphological processes. Every location differs in the groups of organisms that have found themselves there at any given point in time and that have then undergone further evolution.
How do we begin to understand it all?
Science and philosophy have provided us with an array of logical, procedural and analytical tools that we can use. There are so many questions that we might ask, any number of ways to proceed, so many things to observe or measure. But, alas, no perfect recipe as to how to proceed.
We can do a great variety of things that we recognise as components of science, each contributing fragments of evidence, like the pieces in a jigsaw puzzle. But unlike a jigsaw, the picture will never be complete and even the pieces themselves may be blurred and indistinct. The same evidence may be explained by multiple alternatives, some of which may not even have occurred to us yet. We may well have cause to wonder whether we will recognise the true explanation when we have it! Can we ever be certain of anything?
This book is about the science that we call ecology, first coined by Haeckel (1866) and derived from the Greek ‘oikos’ meaning dwelling place and ‘logia’ meaning study. Although there have been many modifications of the definition over the years (Andrewartha 1961; Odum 1959, 1975; Margalef 1968), the consensus is that ecology is ‘the study of the interactions between organisms and their environments’. As we will show, there are many ways in which ecology can be done and various forms of output. Ecology is not an easy thing to tie down.
Over time, the many people engaged in this activity of ecology have diversified (and sub-divided) their objectives and their approaches, established standards, conventions, reputations and traditions, created a machinery for the vetting and publication of its research, concepts and ideas, fashioned an underlying social structure (societies with their conferences, outreach and other services) and developed educational programs. The resulting scientific ‘discipline’ of Ecology is, in its entirety, so much more than the mere collection and assembly of pieces of knowledge that it deserves its own special recognition. In this book, when we want to draw attention to this overall scientific edifice that ecologists have created, we capitalise the word: Ecology.
It is important, however, to recognise that there is another definition of ecology that has nothing directly to do with science or study. The ‘logia’ part of the word has become redundant: ecology has entered the vernacular as simply ‘the relationship between living things and their environment’.
The ‘ecology’ of a penguin, for example, relates to its breeding cycle, the food it eats, its predators, how it is affected by weather, climate and so on. The ‘ecology’ of a lake relates to the community of organisms that it supports, and to its chemistry, hydrology and seasonal weather cycles, since these all interact with the organisms. We refer to the latter as an ‘ecological system’ or ‘ecosystem’.
To put it another way, an entity has an ecology. Ecology is used in this sense by scientists and the public alike and it is the definition we most often see used in the media. Scientists are as comfortable using the same word for their own research activities as for the object of their actions. Does this ever result in confusion? This second definition of ecology does not specify that our knowledge – the narrative that we would tell - has been achieved through the methods of science. A penguin has an ecology whether we have studied it or not (just like a tree falling in a forest will create pressure waves in the air, even if there is no one there to perceive them!). It is worth noting that the same dichotomy of meaning applies to ‘natural history’: natural history is both the activity of observers and the attributes that they are observing. Such is the nature of language! It is not always logical, but common usage ultimately dictates the evolution of language and we learn to live with it (Newberry et al. 2017).
Another linguistic consequence of this other ecology is that people may validly label themselves as ecologists simply by having cultivated an interest and a knowledge of the topic, or being employed within the environmental management industry, or active in a policy setting. Membership of ecology’s professional societies and institutes may also not require the individual ever to have been involved in quality-controlled research. All may be regarded by the media as experts. This is perhaps why some researchers now refer to themselves as ‘ecological scientists’ to make the distinction clear.
An additional layer to this complexity is that ecologists are human observers, with all the constraints that it carries. We see nature through the eyes of humans, who have been taught to view things in particular ways. We are all individuals, who vary in our interests and opinions, and in our technical and cognitive abilities. We will see the same issue in somewhat different ways, do things differently from one another, interpret the results differently and potentially gain different insights. We differ in the levels of evidence that we regard as sufficient to support our views. Different ecologists have different levels of expectation: they will vary in the vehemence of their claims and in the headlines that accompany their publications. It is quite possible that they may well reach different conclusions from the same evidence. Like professionals in any discipline, we also make mistakes, which may be inconsequential but may be more serious, undermining our efforts to make progress. Scientific convention attempts to define standards of rigour, so that this variation can be minimised, but it can never be eliminated.
Ecologists have risen to such challenges over many decades. Judging by the titles and summaries of our scientific papers, we seem to be remarkably optimistic and positive, uplifted by doing science and thrilled by our discoveries. There is good reason to congratulate ourselves and our predecessors on the ecological knowledge that we have assembled thus far. We make extensive use of surveys, experiments and models. It has been fortunate that technological advances have allowed us to extend and fine-tune a wide range of techniques, in data collection and data analysis. A vast amount of evidence from a wide variety of contexts has been accumulated, so that we can determine whether our ideas have generality. But because we cannot measure many things directly, we have come to rely on surrogate measurements – things that we think, and trust, will reflect the true underlying processes. We are also forced to make a great many assumptions in order to simplify problems and to bring solutions within our reach; and we create a great many concepts - human constructs that help us as observers to better comprehend the systems with which we work.
The paradox is that such tools, which we use to make science easier for us, actually add further levels of uncertainty. It is surely not surprising, then, that progress towards greater understanding in ecology can be frustratingly slow, inconsistent and uncertain. Success can be temporary or, in hindsight, illusory. There is always the possibility of false leads and mistakes along the way. Moreover, progress will seldom come from a single piece of research, but from the accumulation of many decades of effort.
Ecologists are playing ever-greater roles in society. We are now routinely involved in preparing advisory reports and are consulted in the development of government policy, in addition to our more traditional roles in communication, education and conservation. With the increasing impacts of global environmental change to the planet, ecologists are going to be critical contributors to the very survival of humanity over the coming decades. Our opinions and our insights are, and will continue to be, valued. However, our reputations ultimately depend on the rigour of our contributions to science, not just the politics of our opinions.
In order to maintain high levels of quality control, we need to apply the highest standards that we can. Here we propose that a strong element of critique applied to our work can help to guide us in this quest.
1.2 Questions and answers in science
A great deal has been said in the past about the way that we should do science, often by those who do not do science themselves: some of these philosophical issues will be discussed in Chapter 3. These discussions can easily become bogged down in semantics and ideas that can be easy to state but difficult to apply in practice. At a pragmatic level, however, science is about posing questions and using evidence from relevant sources, in ways that are logical and therefore defendable, in order to reach answers. These conclusions can be synthesised and built into frameworks of connected ideas which, in turn, lead to new questions – perhaps through hypotheses based on previous results and syntheses - and a search for new answers.
Through science, we can achieve and share fundamental understanding about how the natural world works and formulate ways in which we might take actions to achieve particular outcomes. Our success in the science of ecology should therefore be judged in terms of our ability to pose and to answer questions about the ways in which organisms and their environment interact.
It is not easy to come up with a set of questions upon which to base a scientific study. There is, undoubtedly, a great deal of art involved in being a scientist and a great deal of variation among scientists. Clearly experience plays a major role in the questions we pose, as does observation. There is also likely to be a role for imagination. Ideas seldom simply strike us like a magic bolt of lightning (the so-called ‘Eureka moment’): most thoughts are inspired by something.
The best scientists tend to be the ones with a knack for posing the most illuminating questions and identifying the most effective pathways, sets of procedures, towards the solution. They are also likely to be the ones that are most critical, of both themselves and of others.
The quest for answers can be illustrated with a simple cartoon. It is no easy matter to come up with the right question: a poorly-phrased question may make the path to an answer opaque (Figure 1.1a). We might, for example, ask something very mundane about spatial variation in an index of diversity when in fact we want to know something fundamental about interactions within communities, believing naively that the former will somehow lead to the latter. The first consideration of a researcher needs to be the determination of the ultimate objective of the research, rather than merely coming up with something that we can easily do or calculate, or something that someone has done before. It may not have given them the answer before and it will probably not give you the answer now. Does the question lead us towards the objective?
We often have a favoured answer when we first pose the question (Figure 1.1b); this is especially true as we become more experienced. We may well be right, but it is easy to let our confidence cloud what we do. Indeed, it is common in ecology to set out to ‘test’ a particular idea or hypothesis and in doing so accumulate evidence that supports what we think. This can lead to ‘confirmation bias’, since we may subconsciously ignore evidence that is contrary or that is inconclusive. There may be several possible answers to our question, some of which we have not even considered. Support for one answer does not exclude the possibility that another may be correct: we may need to demonstrate lack of support for alternatives rather than just support for our cherished idea (the principle of refutation is discussed in Chapter 3).
Figure 1.1 The quest for answers (A1, A2, A3 etc) to a question (Q). See text for details.
Part of the art of science is to design a pathway that will effectively lead towards the true answer (Figure 1.1c). A single step is unlikely to take us all the way there. It may or may not draw upon hypotheses and it may be informed by evidence from a wide variety of sources and methodologies. There may be many alternative steps, each of which contributes something to the answer: the best pathway may need to include steps that go in a variety of directions, and draw on a wide variety of skills other than our own, before coming together as we get closer to the answer. Synthesis plays an important part in science and it is not uncommon that information from scientists asking very different questions becomes relevant to us. Some steps may not take us any closer to the answer and may even be distracting: in itself scientific activity, ‘busy work’, does not necessarily lead towards an answer. We might spend many decades going nowhere because we are not using the appropriate procedures, or because we have failed to specify an appropriate – or even a tractable - question.
Even if we are going in the right direction, the size of our steps will vary and may diminish over time: the law of diminishing returns. We then have a difficult decision: how close (intellectually) do we need to get before we are willing to claim that we know the answer, ‘beyond reasonable doubt’? We all differ in our levels of confidence of when we are right, or when we are prepared to accept that we are wrong.
In science, we are part of a community and it is not a simple matter of convincing ourselves, but of convincing others. Like minds may be convinced by the same (incomplete) information. But, to ensure the highest of standards, we must be able to convince the most rigorous of our peers. Even then, there is no guarantee that we will be correct: there will always remain a degree of uncertainty. The need to convince others, as well as ourselves, leads naturally to the discussion of the role of critique (and its cousin, debate) in science.
1.3 The role of critique in science
Critique and criticism have the same root, the Greek kritikos meaning ‘able to make judgements’. In the Socratic tradition, criticism was a necessary, healthy aspect of enquiry: an evaluation of our logic and our progress to reassure ourselves that our quest for knowledge proceeds in the right direction. History shows that science is not an inexorable accumulation of correct knowledge; we make mistakes (Bronowski 1979). Science feeds upon such errors, testing and often rejecting them, in the realisation that we have made, and rectified, previous errors (though see Banobi et al. 2011). Scientists all have strengths that we can recognise and exploit. And they all have weaknesses. A good scientist – within a healthy scientific discipline - needs to know their limitations (to paraphrase Milius and Cimino 1973).
Regrettably, modern English uses ‘criticism’ asymmetrically, meaning an expression of disapproval. The result is that criticism, even ‘constructive criticism’, can offend and cause people to become defensive, so that the benefits of criticism are lost. Failure and weakness are frowned upon in society. If we are seen to have failed, or if we admit the weakness of our understanding, then our reputations will be impaired. We may be seen as having wasted time and money and may raise concerns about the soundness of our policy advice. Governments do not want highly resourced scientists to say ‘we don’t know’ or ‘we’ve made a mistake and need to go back to the drawing board’. Modern ecologists, perhaps more than any other scientists, pride themselves on their inclusive attitudes and their respect for the views of others. Thus, open criticism may be seen by some as undesirable and unwelcome to the general spirit of collegiality, or even as bullying (Vazire 2017, as is debate: Box 1.2). Language can, of course, be toned down to avoid overt confrontation. But there are perhaps times when unambiguous or emphatic statements are needed to halt the proliferation of poor science and, as a result, ensure the prevalence of strong science.
Sadly, most forms of interaction among ecologists are passive and unidirectional, informing colleagues through our publication media and short, polite questions at conferences, rather than an active multidirectional exchange of thoughts and ideas. Even when we identify serious problems within an area of research or across the entire discipline (Steel et al. 2013; Morales et al. 2017), our responses tend to be informative and advisory, rarely leading to a concerted effort to overcome the problem. To gain the full benefits of criticism we must welcome it into ecology by providing greater opportunities for open and non-threatening discourse.
We use the term ‘critique’ throughout this book as ‘detailed analysis and assessment’, a necessary and ongoing process of evaluation. Critique, if embedded in science, can help us to maintain quality-control in what we do because it does more than simply find fault: it identifies our weaknesses so that we can work to overcome them. Ideally, critique should be as dispassionate as possible and, wherever possible, appraise evidence against stated criteria. No critique, however, can ever be completely objective, since it inevitably involves some form of interpretation.
Given the high level of uncertainties involved in ecology, a realist might argue that we should review and question everything that we, and our colleagues, do and claim: to make up our minds on the basis of a rigorous examination of evidence. Such scepticism is a philosophically rational response to difficulty rather than lack of trust or a submission to negativity or doubt. Only intense scrutiny will identify deficiencies that, if it is possible, we can address. The criterion that we should use to evaluate the effectiveness of research should be its purpose or goal. What was a particular study meant to achieve? How was the investigation done? What are the potential problems with it? What was not achieved? How could it be done better?
Statements of what we think we know, as in traditional review papers, are little help in setting directions unless accompanied by an evaluation of precisely what it is that we are trying to achieve. The application of some new method, no matter how ‘advanced’ it is, does not in itself guarantee a major advance in understanding. We should also be careful not to equate effectiveness with the number of papers that result, even though that criterion may often be used in the judgement of our case for promotion or for our suitability to be allocated a research grant.
Critical assessment need not wait for decades until someone decides that it is about time to write a book or publish an article! It makes sense for critique to be ongoing and forward-looking, rather than merely retrospective; and to be pro-active, through the research designer, rather than reactive by reliance on the haphazard and protracted process of peer review. It makes sense, when designing every aspect of every project, to bear in mind specifically what we are trying to achieve, in both the short term and the long term. Is what we are about to do capable of success (or of substantially contributing towards success)? Just because other ecologists are doing the same thing, or because a particular method has not previously been applied to our study system, it does not mean that it is the best thing to do. Could we do something else, or do it in a different way, perhaps with skills that are not currently included?
In hindsight, what did we actually achieve? How could we have achieved more if we were to step back in time? Every ecological researcher goes through such self-examination to some extent: it would be insulting to suggest otherwise. But it is a skill that needs to be appreciated, acquired and honed; some of us are better at it than others. There are also times when our own skills are insufficient, such as when we are ‘too close’ to something: the best critique may then come from others.
If we are to evaluate ecological research in terms of its effectiveness in answering a given question, then we need to incorporate into this critique an assessment of the question. One is irrevocably dependent upon the other. A great many research questions are short-term in focus and context specific. This makes their evaluation relatively easy. For example: what do we need to do in order to increase the abundance of lynx in a particular national park? What is a specific technique capable of telling us about the effect of climate change on a particular coral reef community? The individual researchers, and their colleagues in those fields of research, are in the best position to evaluate their approaches. However, there are also ‘higher-order’ questions that relate to those working across many – if not all – contexts. These might be considered to represent the ultimate goals of ecology as a discipline, since these indicate where we have developed knowledge and understanding that transcend all the variability inherent in our systems. We will consider them in more detail in the next section.
A ‘debate’ is a discussion of opposing views, a process that helps us to assess the veracity of conflicting evidence and opinion and, hopefully, to reach a conclusion. The very words ‘debate’ and ‘argument’ are considered by some people to be too focused on winning and losing: they argue that science needs ‘discourse’, not debate. This may have semantic merit. In many walks of life ‘debate’ has become all about taking sides, winning and losing, right and wrong. There may be palpable (not just egotistical) rewards for winning and penalties for losing. Examples of intense debates in ecology include those concerning plant communities and life history traits (Grime vs. Tilman: Grace 1991), species co-occurrences (Diamond vs. Simberloff: Diamond and Gilpin 1982) or niche-based and neutral theories of community structure (Clark 2012; Wennekes et al. 2012). Clearly structured debates such as these are rare and often remain unresolved; perhaps the debates are intense and extended because they are unresolvable (Peters 1991).
In one extraordinary case, Snaydon (1994) was allowed by editors to liken Sackville-Hamilton (and by implication similar ecologists) to an outdated supporter of the phlogiston theory, for continuing to support the popular ‘replacement series’ experimental design. This escalated to the point of journal editors forbidding the use of the design for any purpose (‘The tendency to misuse the method is so pervasive that its continued use should be discouraged’: Gibson et al. 1999) and referring to it as ‘discredited’ (an editor’s comment, pers. comm.).
A few ecologists railed against these opinions on the basis that the imposition of such dogma could infringe intellectual freedom (Jolliffe 2001) and even threaten ecology’s status as a science (Cousens 1996). The Snaydon camp argued that because the use of the replacement series was highly questionable for some inferences, it should be banned for all uses. A similar personal debate was Lawton’s (1991) attack on Peters (1991) in a book review, but Peters’ right to have his views carefully evaluated was defended by Keddy (1992; see Keddy and Weiher 1999).
‘Debate’ of this sort, with people having to defend their reputations, is unhealthy, but so is a lack of insightful discourse. Discourse should involve the broad ecology community and not be hidden behind the secrecy of peer review or diminished by deference to the individuals with the strongest reputations.
1.4 Ecological goals
Progress is a nebulous thing: we all aspire to achieve it, in all walks of life. It is common to hear the claim that ‘we are making significant progress’, whether this refers to landing on Mars, defeating a disease, fighting drugs and cyber-crime, achieving targets on renewable energy or becoming good enough to win the football World Cup. But how do we measure progress? More specifically, how would we measure the progress in, and therefore the effectiveness of, ecological research? How would we respond to a question from a funding provider who asks us to demonstrate that what we have done with their money has been worthwhile?
The very term ‘progress’ begs the question ‘progress towards what’? Dictionary definitions of progress are typically ‘movement towards a destination’ (the achievement of a specified goal), or ‘towards an improved or more advanced condition’ (better than before). To be able to measure progress, we either need a clear goal – so that we can measure our distance from it – or we need to be able to define the current situation, so that we can, in turn, define ‘better’. With goals, we can objectively consider what we might do to improve progress. Without a goal, the doing of things likely to lead to progress all too readily becomes the goal. Attempts to justify claims that progress is being made, in any field of endeavour, thus often involve lists of the things we have done, rather than objective measurement of how much closer to the goal or how better we now are.
Peters (1991) was particularly critical of ecology’s lack of goals in ‘fundamental’ ecological research: ‘It is an elemental proposition that, if we want to get someplace, then we must know where we are and where we want to go.’ Keddy and Weiher (1999) provocatively used the analogy of landing on the moon: ‘There appears to be a naïve belief [in ecology] that the way to build a spaceship and land a human on the moon is to trust that, if everyone indulges themselves in an idiosyncratic and self-indulgent pastime at the taxpayer’s expense, the outcome will be positive. Like Voltaire’s Professor Pangloss, there is the insistence that this must be the best of all possible worlds, however inefficient or painful it may appear on the surface. If progress is forgotten about entirely… there is no particular need to be concerned about goals, progress and social contribution.’ But the counter-argument is that, in ecology’s case, we do not know where the moon is, how many moons there are or whether moons even exist! So, how can we set ourselves goals?
There are two common justifications given for ecological research. One, most often identified as pure or fundamental research, is the generation of knowledge for its own sake. Civilisation’s quest to understand the world around us (Garfield 1973) would be deficient – for many academically-minded people - without an appreciation of the roles played by organisms in that world. This is the type of ecology that fills our ecological text books: general principles, concepts and theories, along with case studies that we consider as support for them. With this information, that we might term ‘ecological theory’, we can help others in society to appreciate the insights from our science, especially how the living component of their world functions, their impacts on it and thus their ethical responsibilities (see Box 1.3).
The other justification, labelled as applied ecology, is to help solve or to mitigate environmental problems, such as conservation, reclamation and environmental risk minimisation. This is probably the most socially compelling reason in the modern era – at least when it comes to the case for financial support. Applied ecology can, but does not necessarily, make use of theory: the mere application of the procedures of science, such as surveys, experiments and data analysis, may be sufficient to draw conclusions.
Ecologists are highly motivated, often passionate, because they see great significance and value in what they can contribute to science, to society and to the planet. It is important at the outset to distinguish among these different contributions, because the subject of this book is research. That is not to discount the other contributions of ecologists: it is merely a statement of boundary. The social and political contributions of ecological researchers, in communication and education, in the development of policy and advice, even the administration of our societies and the management of our journals, are extensive and important but must be explored elsewhere.
Many professional ecologists see themselves as champions of the environment, not just as dispassionate scientists. Our roles in society can be complex and often it is our opinions that are sought rather than our provision of factual information: in such a setting, the dividing line between scientifically derived knowledge, expert judgement and guesswork is often unclear. As human beings, we are not immune to other influences such as politics and religion, and we can be biased.
What ecologists do in our research does not necessarily map directly on to this binary classification of fundamental and applied. There has long been an argument in all sciences that (applied) benefits to society from fundamental research will occur, but they are rare and inherently unpredictable: we must invest adequately in fundamental science so that we will not miss out on these opportunities.
This reasoning is similar to that used by people who buy tickets in lotteries: unless you play, you will never stand a chance of winning. But in the case of science, you do not even know if there is a prize! It is purely a matter of faith, rather than fact, that there will be (more) prizes. This serendipity argument is not just applied to the issue of high-level funding allocations to different types of science. It is often used to justify case studies of particular organisms, communities or ecosystems: a ‘silver bullet’ might be discovered, a way of saving a species from extinction, of managing a pest or a way of making a system more sustainable. Such claims are often made, but rarely justified, in many introductions to scientific papers and research grant applications: ’improved understanding of the ecology of X is necessary to improve our ability to manage it.’ A more persuasive argument for fundamental research might be that, when we are inevitably called upon to use our expertise (rather than facts) to make speculations for managers, a fundamental understanding of the ways that ecological systems behave will make it more likely that our informed guesses will be reasonable.
It is difficult to discern clear goals for much of ecology (Peters 1991), other than to achieve more or better on a case-by-case basis: more knowledge and understanding, more accurate predictions and better management advice. Take, for example, the websites of researchers or their labs. We are told very little about what they are trying to achieve through the research, whether it be fundamental or applied. What are the difficult questions that they are trying so hard to answer, the challenges, the things that would constitute breakthroughs? The information we read often refers to the interests of the researcher – a taxonomic group, an ecosystem or an academic theme – and the techniques they use. We may or may not be told why those topics are considered important. In almost every case we are told that it is anticipated that the research will lead, somehow, to better management. If management is truly a priority, then there are strategies for making research more effective (see From Forecasts to Policy, Chapter 6).
This extract from a website is perhaps typical: ‘I am interested in the processes that determine the success or failure of invasive plant species in coastal dune systems. Through experimentation, survey, sampling, laboratory analysis and modelling, I try to predict how abundance and distribution change under different conditions and hence what action we might take to manage populations.’ (The University of Melbourne, undated)
We assume that more research, guided by peer review of what we do, inevitably leads to better individual project outcomes and therefore progress for the discipline as a whole. But would fundamental ecology be better served if we set ourselves clear goals: specific things that we should strive to achieve? It is often argued that the sense of purpose provided by a goal can motivate and focus, while assisting in planning of a series of actions (Locke and Latham 2006). They can also be used to set milestones along the way and ‘key performance indicators’. When goals are shared by multiple researchers, they can – in theory - result in greater collegiality, greater combined capability, but also greater competition and challenge. The negative side of having goals is that they set us up to be criticised if they, or defined milestones towards them, are not achieved. Although ecologists are not in the habit of setting goals, the reformulation of fundamental research projects in terms of goals would appear to be relatively straightforward. If a funding agency demanded it, we would do it (Gannon 2003)!
At the level of individual projects, short-term goals are common in applied research. The funding often comes from a client who wants to achieve something in particular: for example, to develop a decision-making aid to guide efforts to save the Sumatran rhinoceros (Dicerorhinus sumatrensis) from extinction, to reduce the impact of facial tumour disease on the Tasmanian Devil (Sarcophilus harrisii) or to develop an effective biological control agent for kudzu (Pueraria lobata).
This does not mean that every research project is expected to achieve that aim by itself. Saving the Sumatran rhino requires tactical, political and social solutions rather than merely ecological knowledge. But it should be made clear how the scientific project will contribute to the goal. It is largely a matter of extending the short-term objective, to explain – as specifically as possible – the longer-term goal of the body of work into which the project fits.
Consider, for a moment, research on climate change. This has generated a large volume of information over the past two to three decades, the result of considerable government investment. In the great majority of instances, the specific research projects were the creations of individual researchers or small teams. The outcomes have been what we already suspected: that, in various case studies, climate change is already having impacts and – hardly a major surprise – we have predicted that these impacts will increase as climate changes further. Those impacts are also relatively predictable on the basis of our current understanding of ecology – although surprises may arise.
In an analysis of the summary sections of every project application funded by the Australian Research Council from 2003 to 2021 (using the search terms ‘climate’ and ‘ecology’), the dominant objective was to develop a better understanding of what has happened in nature so far. About one-third of projects claimed that the research would lead to a better ability to predict future changes. About one-fifth expected their research to result in unspecified benefits for the management of the impacts of climate change, but only 3% had management of the impacts of climate change specified as the target of the research.
Do we need more of the same types of climate change studies, examining further nuances to these established impacts, or serendipitously uncovering instances of interesting new impacts? Or are there bigger questions that require concerted efforts by researchers around the globe? Can we rely on the decisions of individual researchers to determine where, as a society, to go from here? The process of setting and agreeing on goals for fundamental research, however, is far from clear. Do we need some sort of high-level think-tanks? Who would be invited? Would they be effective: the process of reaching consensus often results in wording of outcomes that is general, encapsulating multiple views, rather than being specific and achievable? Would they gain popular support and be widely adopted?
There have been occasional attempts to find consensus on the most important ecological questions and future issues for research. In the case of a survey by the British Ecological Society (Sutherland et al. 2013), many of the questions would have been considered by Peters (1991) as unanswerable and therefore inappropriate as goals. How, for example, would we ever achieve a definitive answer to the question ‘What is the relative importance of trophic and non-trophic interactions in determining the composition of communities?’ Although many of us would agree that it is, indeed, an interesting ecological question, many decades of research are likely to still be inconclusive: it is unclear in most cases what specifiable observations – rather than just data that are somehow relevant - would constitute an answer. A decade and 400+ citations after the survey was published, it is difficult to see what effect its lists have had (or will have) on the direction of research activities in ecology. Instead of ecologists debating and refining the lists, formulating appropriate tests and initiating new collaborative or competitive research projects, the lists seem mostly to have been used to justify projects that were going to be done anyway.
How, then, should ecologists proceed? Does our discipline need to change? And how would change occur?
1.5 So what?
In his book ‘Critique for Ecology’, Peters (1991) commented upon the whole discipline, arguing that the way we do much of our work is fundamentally flawed and requires a new approach based on prediction. If Peters is correct, we will never achieve answers because they are the wrong questions. His views received little support, eliciting denial and defensiveness rather than useful, formative discussion of his criticisms.
It is pointless expecting that, somehow, ecology will undergo a major paradigm shift, with us all accepting that there is a better way of doing ecology, just because one person – or even several people – says so. Fundamental change does not happen that way. Our aim in this book is quite different from Peters’.
Instead of proposing how our colleagues should change what they do, we encourage them to embrace and to facilitate the process of critique themselves, so that it plays a more central role in their science. We will draw on examples from across the discipline in order to demonstrate what this might look like. In our book, we are not starting from a premise that ecology needs to be completely re-designed; it has achieved much in its current form. But it does require vigilance to maintain quality and, since it can never be perfect, it is capable of being improved.
Many of ecology’s core fundamental questions are long-standing and we are yet to achieve satisfactory answers. If we carry on as we are now, we will achieve more and our tools will become better. That is not in doubt. But progress is likely to continue to be slow, even though the researchers are being productive (in terms of outputs), because ecology is inherently a very difficult science.
There is little doubt in our minds – and supported by discussions with journal editors - that some things that we are currently doing are ineffective, sometimes erroneous, and should be changed or discontinued. Critique is a powerful tool for helping us all to identify those things that are most inhibiting progress and to stimulate us to identify what we might change in order to achieve better progress. Achieving satisfactory implementation of those changes is another matter – one that we cannot expect to resolve here.
We will begin the book with a short exploration of some of the ways in which the discipline of ecology has evolved thus far and the factors – the selection pressures – that influence what we do and how we do it (Chapter 2). We then discuss some of the reasons why it is hard to answer questions in ecology, the conceptual tools that we have at our disposal and some of the outdated thoughts about how scientific progress occurs (Chapter 3). This will be followed by a discussion of why it is difficult to draw conclusions from noisy data even with the best approaches that statistics has on offer (Chapter 4); there are no flawless recipes, and all conclusions need to be treated with care. We also explore the problem – indeed, the intriguing phenomenon – that research results are often qualitatively inconsistent, varying among studies (‘context specificity’), some of the reasons for this and how it might affect our approaches (Chapter 5).
We then use case studies to explore four issues that affect our ability to draw conclusions: how stronger inferences can be made from using multiple approaches to a given question (Chapter 6, using evolutionary ecology as an example); our reliance on assumptions (Chapter 7, using the example of studies of niche shifts in invasive species and species distribution models); how we test theories, make predictions and inform decisions (Chapter 8, using population forecasting as an example); and our struggles to achieve generality (Chapter 9, using community ecology as an example). These topics will be dealt with in greater depth than the previous chapters and will be more technical in some parts. Although case study areas may be daunting for the non-specialist, we hope that the generalist reader will take time to follow the critiques on each topic, to learn from the approaches that we take. Finally, Chapter 10 brings together a few loose ends and offers some ways forward in our approaches to what we are trying to achieve, the ways that we go about our quests and the need for better quality control systems.
Each chapter ends with a So what? section that raises both specific and general issues that, in our opinions, warrant greater thought and more extensive debate. The authors draw some conclusions of their own, highlight issues that ecologists everywhere need to consider and set challenges for their peers. What we do not do is to present an instruction manual for how to do better ecological research: that must always depend on the goals that are set and the objectives and questions that each researcher chooses to address. Indeed, that is perhaps the overall message of the book: that we need a critical approach purpose-built for every problem, instead of the replication of prescribed recipes that often seems to dominate ecology.
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