Chasing Biodiversity Off the Scientific and Conservation Tracks

1 Introduction

In the 1990s, two ideas—one normative, the other empirical—captured the public imagination. The normative idea is that, in light of evidently increasing rates of extinction, “saving biodiversity” should be conservation’s premier goal. The empirical idea is a causal thesis—namely, that biodiversity is causally responsible for the functional attributes of ecosystems. Ecologists yoked these two ideas together. Their thought (which §2.2 sets out in their own words) was that, by “demonstrating” biodiversity’s causal role in determining ecosystem functions and by tying these functions to services that benefit humankind, they could provide a scientifically unassailable basis for a mandate to conserve biodiversity.

That, in a nutshell, is what launched a program of ecological research dedicated to the mission of making biodiversity’s causal salience irrefragable. This program became the ecological subdiscipline of Biodiversity Ecosystem Function or ‘BEF’ research. From a handful of modest studies in the 1990s, it ballooned into what is now one of the biggest, most lavishly funded, and institutionally entrenched research programs of the late twentieth and early twenty-first centuries. Its size and impact on ecological science can be read off its enormous publication footprint. BEF research now consumes the scientific energy of many hundreds of scientists who, at a dizzying pace, add to many thousands of existing publications, which all revolve around the supposition that biodiversity is a significant or even dominant causal force in ecosystem functioning.¹

Enormous, too, is the commitment of resources to conservation organizations that, to a significant degree, operate under the influence of the idea of preserving biodiversity in order to preserve ecosystem services. The Nature Conservancy (2021 revenues of $1.8 billion), the World Wildlife Fund (2021 revenues of $451 million), and Conservation International (2021 revenues of $218 million) collectively spend the lion’s share of the world’s conservation dollars on programs at least partly underwritten by this idea.² The mission of preserving biodiversity specifically in order to preserve ecosystem services is also conspicuously sponsored by the United Nations: The United Nations Environmental Programme (UNEP) (2021 revenues of $1.02 billion) provides secretariat services to the Intergovernmental Science-Policy Platform on Biodiversity and Ecosystem Services (IPBES) (2018–2021 revenues, including from thirty-one of its 140 member nations, and in-kind contributions of $22 million). That latter organization’s very name all but announces its dedication to promoting ecosystem services by means of conserving biodiversity. By its own accounting (https://ipbes.net/about), the IPBES alone taps the energy of thousands of scientists across the globe who continually labor to expand an already monumental library of documents (numbering nearly 2,000 listed at https://ipbes.net/library as of this writing), including 247 “Assessments on Biodiversity and Ecosystem Services” (https://catalog.ipbes.net/assessments/), which promote, elaborate, and declaim policy based on this mission.

In short, overwhelming and overwhelmingly entrenched acceptance of the empirical thesis that biodiversity is a significant causal determinant of ecosystem functions aligns with similarly overwhelming and overwhelmingly entrenched acceptance of the normative conservation thesis that, via some supposed connection of ecosystem functions to ecosystem services, this causal relationship mandates biodiversity’s conservation. Yet no systematic review of either thesis has been undertaken by anyone who is not already directly or indirectly committed to them.³ This essay fills this enormously consequential lacuna.

Hundreds of thousands of pages have been written in support of the causal thesis and thousands more have rationalized biodiversity’s conservation by reference to it.⁴ Even back in 2011, Cardinale et al. observed, “there has been an exponential increase in the number of diversity experiments, and the number of publications has more than tripled since 2006 when earlier databases were put together” (2011, 573). The pace of publication has only increased since then. Nevertheless, concise examination of the causal thesis is possible because essentially all experimental data held to be evidence for it derives from experiments that (a) attempt to test the causal influence of species richness by manipulating levels of that variable while observing consequent levels of some ecosystem function, and (b) share interpretive and analytic assumptions (perhaps the only ones possible) to parse these data as evidence of species richness’ causal influence on the ecosystem function.⁵ We can therefore set aside other details to ask the heretofore-unasked question: Do the data produced by experiments characterized by these essential methodological and analytic elements constitute credible causal evidence for biodiversity’s causal influence?

Section 2 lays a conceptual and methodological foundation for answering this question by pinpointing minimal requirements for causal evidence, which are dictated by the distinguishing characteristics of causal relationships. Section 3 then asks whether data from experiments that manipulate species richness meet these evidential requirements. It finds that these data fall short of credibility as causal evidence because experiments count (and most likely cannot avoid counting) every data point at every level of richness as evidence of the impact of richness at that level, yet some enormous number have no causal relevance at all. Section 4 then examines the particular, standardly utilized analysis of experimental data, which “additively partitions” species richness’ supposed causal influence by resolving it into summed terms. It shows that the presumed causal significance of this sum-of-terms representation is wholly undermined by the fact that it merely restates a stipulative definition in algebraically equivalent terms.

Section 5 follows BEF science’s tack from species richness to functional diversity as the biodiversity factor that is supposed to impact ecosystem functions. It again asks whether data that are held to be evidence for this twin thesis meet basic requirements for causal significance. In this case, a negative answer follows from its particular use of HARKing (constructing Hypotheses After the Results Are Known) in which (a) data for some ecosystem function are culled from previously conducted species richness experiments and (b) correlation of functional diversity with that ecosystem function is achieved by choosing—from among an infinitude of differing and often contradicting, yet biologically qualified formulations of functional diversity—some formulation that makes it correlate.

Section 6 then answers another heretofore-unasked question: Setting aside whether or not biodiversity is, in fact, a cause of ecosystem functions, what argument, exactly, runs from that premise to the proposition that biodiversity is a cause of ecosystem services, and on to the conclusion that biodiversity ought to be conserved? By fully spelling out this previously unarticulated argument, each step can be seen to rely on a questionable assumption, invalid logic, or both.

Section 7 draws some conclusions about what these findings—about a conservation commitment and a scientific commitment to support it—entail for ecological science, for conservation, and for the conduct of science more generally.

2 Causal relationships and causal evidence in biology and BEF science

3 Experimental evidence for species richness as cause

Conditions (1)—(4) describe what should be expected of a species richness-manipulating experiment to produce credible evidence that species richness causally affects productivity. I shall focus on productivity in assessing how well these conditions are met both because productivity has been the most prominent effect variable in BEF experimentation and because the basic requirements for causal credibility appear to be indifferent to which ecosystem function—whether productivity, zoonotic disease suppression, or stability—species richness is supposed to influence.

I shall also focus on what is known as the random draw design for manipulating species richness as a candidate causal variable. There are again two reasons: This design is the benchmark and reference for producing essentially all the data that the BEF research community holds up as direct evidence for BEF science’s central claim—that species richness causally determines an ecosystem’s productivity independent of which species happen to reside in it.¹⁴ As well, if you wish to manipulate species richness in a way that isolates that variable from covarying variables that represent the presence of particular species or particular collections of species, then randomizing the selection of species is not merely the obvious design choice, it may be the only available one.¹⁵

As condition (1) suggests, BEF experiments utilizing random draw do not actually intervene on R. Instead, they simulate interventions on R. They accomplish this by comparing the productivity observed in R-differing treatments, the specific composition of which are determined by random draw (without replacement) of species from an antecedently determined pool of, typically, 8 to 32 species—a number represented below by the variable name ‘N’. With respect to any two treatments that differ in species richness R, the standard analysis interprets one treatment as the state of an ecosystem’s species richness before intervention and the other as the state of that ecosystem’s species richness afterwards. Analyses of BEF experiments treat these R-differing pairs of treatments as simulating interventions that are R-changing.

Simulating interventions on a candidate causal variable in this way is a perfectly legitimate means of probing hypothesized causal connections. Drug trials are a convenient reference. These experiments, too, often must contend with factors that may confound the action of the relevant Boolean causal variable D (0 = drug not taken; 1 = drug taken). Drug trials typically resort to simulating D-changing interventions because no single patient is both given the drug and also not given it.

However, in a BEF species-richness random-draw “trial,” a crucial question—nowhere considered in the BEF scientific literature—arises: In simulating R-changing interventions, what variable, exactly, is being manipulated? According to a number-changing interpretation, a pair of treatments qualifies as simulating an R-changing intervention strictly on the basis of a difference in the number of species assigned to them—that is, without qualification or restriction with regard to which particular species with which particular characteristics enter into either the before-intervention count or the after-intervention count. Although another interpretation is discussed later in this Section, this one may initially appear to be the only one possible. And it is the one and only one that BEF researchers, without applying that label, employ when they interpret differences in productivity between any two R-differing treatments as evidence that their difference in species richness is causally responsible—without qualification or restriction with respect to which particular species are in these treatments.

The number-changing interpretive stance has a striking implication. It entails that, in statistically analyzing the productivity data to assess the causal impact of a change in species richness, all treatments that have the same number of species are grouped together, regardless of which species they contain. Yet this assessment cannot avoid attributing causal significance to differences in productivity between R-differing pairs of treatments that cannot plausibly be viewed as simulating how a change in the species richness of some particular ecosystem affects the productivity of that ecosystem.

Consider a study utilizing the species pool, represented in set notation as {A,B,C,D}, where each letter stands for a particular species in the pool. Suppose that random draw produces the treatments {A} and {B,C,D}. The number-changing interpretive stance views this pair as causally relevant by virtue of simulating an R-changing intervention on the first, single-species treatment {A} by way of increasing its richness—by two—to arrive at the second, three-species entourage {B,C,D}. If the productivity of this latter, three-species treatment is observed to be greater than that of the first, one-species treatment, this is supposed to be evidence that increasing a particular ecosystem’s species richness (by two) causes that ecosystem’s productivity to increase.

In this example, the change in R consists in total replacement of species resident in the original ecosystem with an entirely different entourage. It is difficult to make sense of differences in these two ecosystems’ productivity as evidence that intervening to increase R in an ecosystem causes P to increase in that ecosystem. A more reasonable interpretation is that one ecosystem was obliterated, and the more speciose one that replaced it differed in productivity.

While any observed productivity difference in this case clearly has no credibility as evidence that changing the richness in some ecosystem causes that ecosystem’s productivity to change, one might initially dismiss it as a bit of data pollution so inconsequential that BEF analyses of can safely ignore it. But that is not so. A tedious but straightforward combinatoric analysis shows that for a species pool of size N there are¹⁶

(1)

entirely disjoint treatment pairs—that is, treatment pairs having no species in common. This number is 16 for N = 4; 2,472 for N = 8; 18,859,512 for N = 16; and 846,948,553,422,744 for N = 32, respectively. 847 trillion data points cannot legitimately be dismissed as “safely ignored noise.” Rather, these data points constitute a substantial portion¹⁷ of every dataset in hundreds of species richness manipulation experiments—data points that are treated as though they constitute evidence that changing an ecosystem’s species richness is causally responsible for changing that ecosystem’s productivity, even though they actually have no such causal significance.

A dataset so suffused with data points that lack evidential credibility is itself not credible. This places BEF science on the horns of a dilemma: On one side, it appears that there is no escaping the conclusion that the number-changing interpretation cannot make reasonable causal sense of data from all the many experiments that simulate manipulations of species richness. On the other side, there appears to be no alternative interpretation that can make sense of the sweeping causal claim that BEF scientists have striven to support—that species richness quite generally and without reference to the particular species or combination of species involved, is a significant cause of ecosystem functioning. Yet BEF science’s mission is to establish this claim as the “scientific” basis for the claim that diminishment of species richness will make ecosystem functioning disintegrate and therefore, somehow, diminish ecosystem services (§2.2).

This pervasive, because unavoidable, contamination of datasets with bad data points undercuts essentially all experimental evidence for species richness’ causal influence. Yet a second, independent problem is no less subversive of the evidence. This second problem consists of irresolvable entanglement of causal factors. It arises from the coupling of two complicating factors: (i) It is not possible to intervene on species richness R without also intervening on many other, independently operating causal factors that are highly correlated with R via their logical/conceptual rather than empirical coupling with it. And crucially, as we shall see: (ii) It is not possible to disentangle the contribution of these confounding causal variables by intervening on each of them individually without concomitantly intervening on R.

Empirically correlated causal factors not uncommonly arise in experimental setups. Drug trials illustrate why they need not pose insuperable obstacles to effectual experimental test of a factor’s causal influence: It may not be possible to intervene (or simulate interventions) on D (drug taken or not) without also intervening (or simulating interventions) on C (capsule taken or not). However, a drug trial may still distinguish the causal contribution of these two factors by intervening on C without also intervening on D. That’s what enables a drug trial’s placebo group to perform its cause-disentangling role, thereby surmounting complication (ii) of the preceding paragraph.

Similar recourse is not available to BEF experiments. They are subject to complication (i) because intervening on R also necessarily (logically and conceptually) involves intervening on multiple causally entangled variables. These variables include some number of the N causal variables S_i (the i^th species S_i present or absent) representing individual species from a species pool of size N that are added or removed as part of intervening on R. Many more variables arise from some number of the $\sum _{k=2}^N\left(\begin{array}{c}N\\ k\end{array}\right)$ combinations of species that are added or removed as a consequence of intervening on R. For example, the R-changing intervention that adds N–1 species to (let us say) one initially present species concomitantly adds, minimally, the N –1 causal factors S_i. It also adds many more independent causal factors, including all $\sum _{k=2}^N\left(\begin{array}{c}\begin{array}{c}N\\ k\end{array}\end{array}\right)$ combinations of two or more species in that pool.¹⁸ The number of added combinations is: (2^N − 1) − N, or 11 for N = 4; 247 for N = 8; 65,519 for N = 16; and 4,294,967,263 for N = 32, respectively.¹⁹ Each one of these causal factors plausibly operates independently of richness: Each species has a characteristic productivity that is independent of its combination with other species. Each combination of two or more species also makes some characteristic causal contribution. For example, a grass that employs the form of photosynthesis known as “C4 photosynthesis” (rather than C3 or CAM photosynthesis) in combination with a legume is characteristically more productive than the C4 grass alone.²⁰

The particular conundrum posed by complication (ii) might suggest that it could be remedied by viewing pairs of treatments that are identical in R but differing in composition as simulating a richness-preserving intervention. Nothing comparable is possible for drug trials. BEF experimenters certainly have not sought to do this. And it seems clear that a richness-preserving intervention could not be interpreted as an intervention on species richness. But more importantly, data points from these simulated interventions would still be irretrievably compromised as causal evidence by the first, dataset pollution problem: Two ecosystems with the same number of wholly different species cannot coherently be regarded as some one particular ecosystem that was intervened upon. Nor would these R-preserving interventions even remedy the second, irresolvable entanglement flaw: Their inclusion could not avert the introduction of a tangle of causal contributions from all the individual S_i as well as all the combinations of S_i that occur only in either the pre-intervention ecosystem or the species-equinumerous, post-intervention ecosystem.

Absent any other suggestion, a remedy for both the dataset contamination problem and the irresolvable entanglement problem might be sought by simply abandoning the number-changing interpretation. This, no doubt, is the nuclear option for BEF science, for it entails also abandoning the sweeping empirical claims, cited in §2.2, for the causal impact of the sheer number of species in an ecosystem on its functioning without reference to which species they are. And abandoning that thesis, in turn, requires abandoning the similarly sweeping plea (discussed in Section 6) to conserve biodiversity lest declines in the number of species cause declines in ecosystem services.

That said, and although not employed in actual BEF experimental practice, analyses, or statements of findings, one might nonetheless look to a collection-modifying interpretation of R-changing interventions in which the only changes to species richness that play an evidential role are ones in which species enter or exit an existing collection. Indeed, this picture might more closely align with actual concerns about biodiversity. However, under this interpretation, R no longer signifies what everyone means by “species richness”—the number of species in an ecosystem. Rather, R now means something relational, tied to some initially defined collection of particular species that persist through interventions that add others. Yet imposing the specific restrictions of a collection-modifying interpretation of R-changing interventions still falls short of erasing the causal entanglement problem: Even when interpreted in this way, the simulated addition or removal of species from an ecosystem still does not permit disentanglement of multiple, independently operating causal factors that are highly correlated with species richness via logical coupling.

To see why, consider two experimental treatments, the first containing one species (n = 1) drawn from a pool of N species. Suppose that this treatment is paired with a second, post-simulated-intervention treatment that adds to it all other N–1 species in the pool. This pair of treatments satisfies the relational constraint of the collection-modifying interpretive stance in simulating an intervention that is analyzed as a change in species richness Δr = N–1. However, it concomitantly simulates addition of the N–1 independent causal factors consisting of each of the added species. It also simulates the addition of the other independent causal factors consisting in all $\sum _{k=2}^N\left(\begin{array}{c}\begin{array}{c}N\\ k\end{array}\end{array}\right)$ combinations of two or more species in that pool. This number (of added combinations) is (2N–1)-N, or 11 for N = 4; 247 for N = 8; 65,519 for N = 16; and 4,294,967,263 for N = 32, respectively. 4.29 billion cannot reasonably be presumed to not represent some major causal contribution and importantly, one that is strongly correlated with R, therefore subverting any claim that R is causally responsible. As well, the billions of data points that arise from two treatments where n = 1 for the first are joined by billions more that arise from two treatments where n > 1 for the first. Finally, the collection-modifying interpretation fares no better than the number-changing interpretation in making available viable means of independently intervening on the independently operating causally confounding variables in order to disentangle their effects from any effects that might be due to species richness.

The details that this section elaborates in order to expose an apparently sweeping failure of BEF experiments to produce credible evidence should not obscure how simple and basic the essence of that failure is: By virtue of the very definition of “species richness,” experiments that attempt to manipulate that variable ineluctably produce huge numbers of causally irrelevant data points, which are analytically indistinguishable from all the others. In the history of science, instances of widespread blindness to evidential flaws this conspicuous have most frequently occurred in circumstances such as these, where it was rooted in widespread commitment to affirming one particular result.

4 Additive partitioning

Early critics of BEF research (for example, Aarssen 1997, Huston 1997, Huston et al. 2000, and Huston and McBride 2002) also questioned whether the experimental data truly isolated species richness as a causal factor that operates independently of species composition. In reacting to this challenge, BEF scientists did not see a need to change any essential design element of their experiments. Nor did they see a need to question, modify, or qualify their claim that data from these experiments evidence species richness’ causal influence on ecosystem functions. They instead changed only how they analyzed these data—following the suggestion of Loreau and Hector (2001) to represent the supposed causal influence of species richness as the simple sum of two (or more) factors, which they refer to as “mechanisms”²¹ or “components” of this influence. This representation, in terms of what is called the additive partitioning equation, quickly became so integral to every experimental data-based claim for species richness’ causal influence and to the defense of these claims that, were this essay not to consider them, its assessment of the evidence for these claims would be quickly (and justifiably) brushed aside.

In the context of the BEF mission to show that species richness causally impacts ecosystem functions, there may be a temptation to view the additive partitioning equation as a mathematical expression of the idea that changes in levels of ecosystem functions due to additions or removals of particular species or combinations of species are themselves caused by changes in species richness. But that would be a conceptual mistake. The stipulated meaning of species richness = $\sum _{i=1}^N{S}_i$logically entails that species richness increases with the addition of some new species. The addition does not cause species richness’ increase. In much the same way, it is a category mistake to suppose one can cause a circle’s area to increase by increasing its radius. That is because (as Archimedes showed) the Euclidean definitions for circles and triangles together logically entail that the area of a circle with radius r is 2πr.²²

However, the additive partitioning equation’s incapacity to contribute causal or even empirical information relevant to the question of species richness’ causal influence is made fully apparent by looking at what, exactly, that equation means. In its most basic form, the additive partitioning equation asserts that any observed difference in productivity (or other ecosystem function) associated with a difference in species richness—labeled NE for “the net biodiversity effect”—is a simple sum of two terms—namely, “the selection effect” SE and its conjoined twin, “the complementarity effect” CE:

Interpreting this equation as representing a causal relationship whereby changes imposed on species richness bring about a net change in productivity NE requires interpreting the “effects” represented by SE and CE as factors that mediate the causal operation of species richness in producing that productivity change. Thus interpreted, SE is supposed to represent the portion of species richness’ influence that is due to the particular “selection” of species—whether naturally or through experimental random draw—that count towards an ecosystem’s species richness.²³ In contrast, CE has no settled interpretation: It represents whatever portion of species richness’ influence that is supposed to be due to any joint action and interaction of organisms that might arise from their specific differences—that is, some open-ended notion of composition.

Because Loreau and Hector’s (2001) seminal exposition of the additive partitioning equation frames it as a version of the Price equation (1970), it might be thought that the causal relevance of the former equation can be inferred from the causal relevance of the latter. It is therefore important to dispel that misconception. George Price’s original proposal arose from thinking about trait selection in biological organisms and consequent evolution of species. However, Price viewed his equation as a sweepingly general representation of any difference between (a) observed values of some trait in one population of (not necessarily biological) objects and (b) observed values of that trait in a second population of objects, which can be viewed—in some expansive sense not requiring clear-cut causal linkages—as having descended from objects in the first, so-called parent population. Illustrative is Price’s (1995) own example of the population of Modest Mussorgsky’s musical Pictures at an Exhibition, which (in his interpretation) “descended” from a parent population of paintings that the composer viewed at a memorial exhibition of paintings by Viktor Hartmann.

For the purposes of this essay, it suffices to say that the Price equation is a formal representation of a difference in some trait that may be observed in objects in one population with respect to that trait as observed in objects in another population that is somehow and not necessarily causally linked to the first. It presents a difference, which, given the observed trait values, is indisputably true—but only by virtue of meanings of the terms that enter into its expression. It is true, that is, in the non-empirical way that the equation 2 + 2 = 4 is true.

The non-empirical nature of the Price equation is obvious from how it is derived.²⁴ It starts with an equation that stipulatively defines a symbol representing a difference between the respective means of some trait for objects in two linked populations. The stipulated meanings of the terms that appear in this definition ensure that the Price equation can be derived from it via a sequence of algebraically correct transformations, which cannot add empirical content. Because the Price equation only restates the original definition’s expression of an equivalence between two different symbolic representations of observed differences in populations of objects, it cannot add causal content.

However, the additive partitioning equation’s causal relevance is not thereby doomed because, although Loreau and Hector (2001) tried to model it on the Price equation, they did not succeed in making it a version of the Price equation: The additive partitioning equation violates Price equation semantics in multiple ways, including some that help to illuminate the semantics of the former equation later in this section.²⁵

Equation 2 is supposed to be a simplified but equivalent re-presentation of Equation 3:²⁶

in which NE stands in for Equation 3’s ΔY, while the notation Cov( ) in Equation 3 makes Equation 2’s SE look like a standard statistical covariance and the notation E( ) makes CE look like a statistical expectation. The key to understanding what Equation 3 means is that it, in turn, is a provably equivalent re-presentation of Equation 4:

Equation 4 stipulatively defines the quantity ΔY to mean: any difference between (i) the sum of actually observed yields Y_Oi for each species i of plant in multi-species assemblages that draw on a pool of N distinct species, and (ii) the sum of (as we shall see, labeled with crucial ambiguity) expected (not observed) yields Y_Ei for each species i of plant in multi-species assemblages. Y_Oi and Y_Ei, in turn, are quantities that (as shown on the second line) are derived by weighting species i’s yield in monoculture (M_i) by its proportional contribution to yield in multi-species assemblages. RY_Oi is the proportion of the total yield that species i is actually observed to contribute in those mixed assemblages. On the other hand, RY_Ei, like Y_Ei, is not an observed quantity. Rather, it is stipulatively defined—as the proportional contribution of species i to the yield, computed on the basis of the surely false assumption—the experimental null hypothesis—that no plant’s yields are ever affected by the presence of other plants.²⁷ In Equation 3, ΔRY merely denotes the difference between RY_E and RY_O in abstraction from the particular contribution of each species i.

A few observations regarding Equation 3’s derivation from Equation 4 make it apparent that neither is relevant to the question of whether or not species richness causally determines productivity. First, as already observed, Equation 4 merely stipulates a definition for a symbol (ΔY). When yields do, in fact, deviate from the null hypothesis—as they very commonly will—the symbol ΔYmerely gives us a notational convention for compactly expressing this fact. But its use cannot and does not add empirical information to the already given fact. Illustrative is the reported response of the great Dutch footballer Johan Cruijff to the question of how he won games. Paraphrasing Cruijff: “By scoring one more goal than your opponent” (van Veelen et al. 2012). This “explanation” merely invokes the football convention—whereby outscoring one’s opponent in a match constitutes winning. Consequently, Cruijff’s response supplies no empirical information. Equation 4 is also merely a descriptive convention, which also cannot add empirical content to the state of affairs that it describes.

Mere reference to a convention is particularly evident in the definition that is stipulated for RY_Ei—species i’s proportional contribution to yield. As noted above, the relative yields RY_Ei are not observed quantities and are not, the subscript E notwithstanding, even expected in the customary sense of “what one should expect on the basis of empirical evidence.” That is because they are computed on the basis of the null hypothesis that a plant’s yields are never affected by the presence of other plants. And a long-standing mountain of evidence suggests that this hypothesis is routinely violated: Nitrogen-fixing legumes can promote the growth of many neighboring plants, while plants that produce allelochemicals (mostly excluded from experimental species pools) can suppress the growth of many others. Consequently, the sensible way to interpret any difference between yields computed with RY_Ei and actually observed yields, RY_Oi, is that it reflects the well-established fact, owing nothing to BEF research, of widespread violation of the assumption underlying RY_Ei’s computation. It makes little sense to interpret any such difference as reflecting a change in some actual property of actual ecosystems, let alone the operation of some causal factor.

This basic interpretive error may be obscured by multiple additional errors that Loreau and Hector (2001) make with respect to RY_Ei in taking the Price equation as their model. As indicated above, the Price equation simply describes how observed values of a trait in the objects in a parent population relate to observed values of that trait in a descendent population linked to it in Price’s expansive sense. In a species richness experiment, the trait that differs between parent and descendent populations clearly must be the yield of the varying assemblages of organisms in experimental treatments. The objects bearing these traits can only be assemblages. Therefore, in Price equation terms, a BEF experiment’s parent and descendent populations are populations of experimentally created assemblages.

Given that, we should ask: What would the parent population (of assemblages) be? BEF thinking on this is reflected in Fox’s (2005) characterization of the additive partitioning equation. According to him, it depicts “monoculture biomass as a trait on which selection can act.” If follows that the parent population is the population of assemblages in which monoculture biomass is a trait. That population is simply the population of monoculture assemblages. And from this parent population of monocultures, multi-species assemblages are supposed to descend. In fact, BEF experiments generate just such a descendent population—via random draw of species from a pool. This makes it clear that the “selection,” which Fox supposes to explain any overall yield difference ΔY between these populations of assemblages, consists in nothing other than selection by random draw of species from a pool to create multi-species assemblages in a BEF experiment.

The fact that the additive equation treats particular assemblages as members of linked populations raises challenging questions: First, what, exactly, is the biological meaning of the “selection” that is supposed to operate on one population to produce the other? And how, exactly, are the monocultures in the parent population supposed to causally influence the multi-species assemblages in the descendent population? These two questions have no obvious satisfactory answer. But I will set them aside to focus on questions about the stipulation that RY_Ei in Equation 4 means the frequency with which various values of the yield trait occur in the parent population, which as we have seen, is a population of monoculture assemblages. By assigning RY_Ei this meaning, Loreau and Hector (2001) sought to give RY_Ei the role that, in the Price equation, is played by the proportion of the parent population for which the given trait is observed to have a particular value. However, this gives rise to multiple incongruities:

1. RY_Ei, according to the definition that Loreau and Hector’s (2001) stipulate for it, is not a frequency of occurrence. Loreau and Hector (2001) may obscure this fact about RY_Ei’s assigned meaning by at one point also assigning it a value—equal to the proportion of species i organisms in an assemblage’s total. But asserting that some thing assumes some value does not alter what it is. We cannot change that a Chiriqui harlequin frog is a variegated amphibian by assigning it one of its many possible color values.

2. RY_Ei does not refer to the parent populations—the monocultures—for which it is supposed to be a frequency of occurrence. Rather, it refers to descendant populations of multi-species assemblages by way of invoking the null hypothesis.

3. RY_Ei’s values are not actual frequencies of occurrence of trait values. Actual frequencies, but not RY_Ei’s values, are determined by observing actual values and how frequently they occur in some actual population of objects.

4. RY_Ei is not even an expected quantity in the sense of “what we can rationally expect” because it expresses the null hypothesis, which is known to be false. Nor is it an expectation in the standard statistical sense because that would require it to be the arithmetic mean of a set of independent observations of an independent variable that varies over an actual population of objects.²⁸

An expectation in statistics is a frequency-weighted average for all the observed values for a variable that characterizes objects in some one particular population. The expression E(ΔRY*M) in Equation 3 does not satisfy this semantic requirement. ΔRY refers to differences in a relative yield variable between two different populations, the second of which—a descendent population of multi-species assemblages—is a fictional construct, not something observable, let alone actually observed.

For its part, a covariance in statistics is a property of, or relationship between, the observed values of two variables, each of which varies randomly over one, single population of objects. It summarizes the direction and magnitude of one variable’s observed deviation from its mean in that one population with respect to the direction and magnitude of the second variable’s observed deviation from its mean in the same population. Cov(ΔRY, M) in Equation 3 does not satisfy this semantic requirement, and for reasons similar to why E(ΔRY * M) does not satisfy the semantic requirements for an expectation: Its variables span different, parent and descendent populations, while the values for one variable are not even observed but rather computed on the basis of the null hypothesis.²⁹

In short, neither the notation E( ) nor the notation Cov( ) on the right hand side of Equation 3 have the statistical meanings that these notations suggest. Rather, they are semantically misleading syntactic shorthand for expressions that derive from Equation 4 solely via algebraic manipulation.

Summing up: Equation 4, the starting point for the additive partitioning equation’s derivation, is a stipulative definition (for ΔY). The additive partitioning equation, Equation 3, is merely an algebraically equivalent re-presentation of Equation 4. The truth of both is independent of contingent facts about the actual world.³⁰ That means that they are true independent of whether or not species richness causally influences productivity; they contribute no information one way or the other. In fact, these equations cannot even express predictive relationships: Prediction depends on reliable correlations between two factors that are observed in the real world. This requirement is not satisfied by the “expected” yields Y_Ei, which are computations based on a proposition—the null hypothesis—that is routinely contravened by what is actually observed. This circumstance even strips the additive partitioning equation of descriptive value.

A remarkable feature of additive partitioning’s incapacity to serve as a means of causal analysis is the sheer number of missteps integral to lending it any appearance of causal credence. It is difficult to imagine how every one of those errors could have been overlooked in the face of scrutiny unrestrained by prior commitment to the causal hypothesis it was supposed to prop up.

5 Functional diversity as cause

BEF researchers universally regard the ‘B’ in BEF research as standing for biodiversity, not for any one particular representation of it, such as species richness. So starting in the early 2000s, swift embrace of functional traits as an organizing concept in ecology led to increasing reinterpretation of biodiversity in terms of functional diversity. This trend manifested in BEF research as some efforts to establish the causal influence of biodiversity pivoted from species richness to functional diversity.³¹ BEF scientists cited in this section make clear their supposition that functional diversity is a significant cause of ecosystem functions by variously stating that it is “an important driver of ecosystem functioning” (Villéger et al. 2008), that it “can influence ecosystem functioning” (Clark et al. 2012), that it “control[s] biodiversity effects on biomass production” (Flynn et al. 2011), that functional diversity can (causally) explain ecosystem functioning when richness does not (Cadotte et al. 2011), that functional diversity “enhances ecosystem functions such as primary productivity” (Schittko et al. 2014), and that “functional diversity [is] a key factor to maintain important functions and services of ecosystems” (Laureto et al. 2015, 112). Schittko et al.’s supposition that functional diversity’s supposed causal determination of ecosystem functions gives warrant for its conservation (via some unexplained connection to ecosystem services) is echoed by others, including Caddotte et al. (2011, 1079) who state, “The goal of conservation and restoration activities is to maintain biological diversity and the ecosystem services that this diversity provides.”

It is a comparatively simple task to analyze the credibility of evidence for this causal hypothesis: As BEF researchers such as Lefcheck and Duffy (2015) themselves note, support for this thesis derives almost entirely from post hoc analysis of data produced by prior attempts to manipulate species richness. Little effort has been made to produce direct experimental evidence via experimental manipulation of functional diversity as a candidate causal variable.³²

Crucial to evaluation of any causal thesis is a generally agreed-upon, precise characterization of the candidate causal variable. It is therefore remarkable that no such characterization of functional diversity exists. Instead, there is general agreement only on three characterizing elements, which are so undemanding that they can be embodied in (literally) infinitely many ways that give rise to infinitely many ways to measure functional diversity, which yield assessments that often radically disagree and even conflict.³³ The three agree-upon elements are present in Díaz and Cabido’s (2001, 654) commonly cited definition. According to them, functional diversity is:

the value and range of functional traits of the organisms present in a given ecosystem.

The first element is a tacit and questionable empirical assumption—the assumption that every individual organism is a repository of some fixed collection of traits, each with a fixed value that is wholly determined by that organism’s species. This assumption is routinely violated, for example because (as is well known) many organisms are phenotypically plastic or vary greatly with the biotic and abiotic conditions in which they live. The second element is another empirical assumption—the assumption that these species-determined traits, with their species-determined values, causally determine functional properties of ecosystems in a way that makes the organism supplying these traits/values wholly interchangeable with any other or combination of the many other organisms that could also supply them.

The third element is an accompanying definition of functional trait, the source of functional diversity, which Díaz and Cabido (2001, 654) define as:

the characteristics of an organism that are considered relevant to its response to the environment and/or its effects on ecosystem functioning.

This definition makes functional traits out of most traits of most organisms: The preponderance of traits that are of ecological, evolutionary interest, or even general biological interest in some way enter into how organisms respond to the particular conditions in which they find themselves. And it is difficult to think of biologically interesting traits that do not collectively affect at least one ecosystem-wide property or ecosystem function.

Permissiveness in assessing an ecosystem’s functional diversity is further compounded by the fact that its definition places no constraint whatever on which of dozens of functional traits (Roscher et al. 2004; Cornelissen et al. 2003) of organisms to include and which ones to exclude. This license is reflected in the wide range and disparity of traits that different studies actually use to compute an ecosystem’s functional diversity. Yet addition or removal of just one trait can dramatically alter what an ecosystem’s functional diversity is supposed to be. Consider a Euclidean distance-based metric (discussed below) with trait T₁ for species {A,B,C} with values {0.5,1.0,2.0}, respectively; and trait T₂ with values {10,0,10}. Based on T₁ alone, the Euclidean distance d(A, B)=0.5, d(B, C)=1.0, and d(A, B)<d(C, D). Yet when T₂ is included, d(A, B)=10.0125 and d(B, C)=1.5: Adding T₂ reverses the inequality.

Permissiveness in assessing an ecosystem’s functional diversity is yet further compounded by lack of any constraint which few species of any ecosystem’s multitude of species to include and which many others to exclude. As with traits, no study selects for inclusion anything but a tiny subset of species that might occur in an ecosystem; and that set varies widely from study to study. BEF scientists routinely employ the phrase “the functional diversity of an ecosystem” to refer to functional diversity as a generally operating cause. Yet contrary to what the definite article suggests, every computation of an ecosystem’s functional diversity is relative to a choice of tiny minorities of its species and tiny minorities of the functional traits that are supposed to inhere in those organisms. This indeterminacy is made radical by the fact that there appears to be no independent test of the biological soundness of any of the myriad, sanctioned choices: No one can say what an ecosystem’s functional diversity actually is apart from its measurement by some measure.

Additionally, species and traits are but two sorts of unconstrained choices among others³⁴ that contribute to a literal infinitude of choices that engender an embarras de richesses of measures, which BEF scientists have proposed or actually utilized (Petchey and Gaston 2006; Mouchet et al. 2010). I shall focus on two of the most discussed and utilized. These fall into the category of ‘M’-type measures, which represent any species-determined value of any real-valued, species-determined functional trait as the coordinate value for one dimension of a continuous, multi-dimensional, Metric space. The location of any species in the space is given by the coordinate values for (typically) multiple traits. The metric defined on the space then supplies the distance between any two species-defined points. That distance is interpreted as a measure of the species’ differentness—the quantity of diversity that they embody.

Numerous problems arise with this proposal. One concerns discrete-valued variables because (a) a continuous, real-valued metric space is incapable of representing them and (b) they often have no sensible numeric representation at all. Yet many of the most salient functional traits are discrete-valued: season of first leafing, nitrogen-fixing or not, type of photosynthetic pathway, etc. BEF scientists routinely represent these fixed values with arbitrarily assigned integers—for example, photosynthetic pathways as {C3 = 1, C4 = 2, CAM = 3}—and treat the numeric differences as biologically meaningful, real number-valued representations of degrees of differentness.

Another problem arises from the metric. BEF scientists rarely if ever even discuss their choice of metric; they simply presume that trait spaces are Euclidean. Yet there appears to be no biological basis for presuming that accurate representation of differentness among species compels choice of a Euclidean metric. Why (biologically speaking), must the metric even be isotropic, homogeneous, and flat?³⁵ Yet non-Euclidean metrics can always be found that, for a given set of coordinates, yield distances and so functional diversity numbers that differ from the Euclidean assessment by any pre-specified amount.

The gravity of these and other problems is compounded by the fact that, even within the domain of ‘M’-type measures and even with respect to the same set of species and the same set of functional traits, conflicting assessments of functional diversity abound. Two of the most popular ‘M’-type measures are illustrative.³⁶ Rao’s quadratic entropy Q (Rao 1982; Ricotta 2007) is a schema for computing functional diversity as the sum of pairwise trait-based Euclidean distances between pairs of species located in a Euclidean space. Q weights these distances by the species’ abundances even though there appears to be no biological basis for determining whether or not abundance weighting improves the accuracy of functional diversity assessments. Schumacher et al. (2009), Roscher et al. (2012), Clark et al. (2012), Song et al. (2016), Funk et al. (2017), Weiser et al. (2017) all make use of Q.

Functional Richness or FRich (Lefcheck and Duffy 2015; Schittko et al. 2014), on the other hand, like most ‘M’-type measures but unlike Q, ignores abundances. However, like Q, FRich starts by computing a set of points in an abstract metric space. Each point “locates” one of the tiny number of species chosen for FRich’s computation, utilizing that species’ pre-chosen collection of traits, each assigned the value that all organisms of that species are presumed to have. FRich then veers into topological territory, focusing on the convex hull that this collection of species-points defines. Intuitively: if you draw lines that connect every pair of points in a space, then their convex hull is the minimal subset of points that forms an “envelope” fully containing all the lines. According to FRich, the ecosystem’s functional diversity is the volume of this convex hull. Yet nothing in biology explains why computing the volume—with a biologically arbitrary metric—of the convex hull of points that represent an arbitrary sample of an ecosystem’s species with an arbitrary sample of their traits and species-determined values produces the biologically correct value of that ecosystem’s functional diversity.

Both Q and FRich (and dozens more computational schemas that this discussion omits) evidently lack the biological mooring that would make them something more than a highly unconstrained and biologically dubious computational exercise. For example, utilizing FRich to measure functional diversity commits one to the principle that an ecosystem containing species that differ vastly in some one functional trait—for example, plants that reach multiple meters in height versus others that never exceed a centimeter or two—has no functional diversity at all, should no other trait differ: A one-dimensional difference in volumes, no matter how stupendously great, is no difference at all.

Similarly vexing is that FRich and Q provide assessments of functional diversity that, it is easy to see, diverge systematically and without bound: Neither adding nor deleting a point located inside the envelope formed by FRich’s convex hull affects its assessment of functional diversity. Yet the total of the added or deleted point’s pairwise distances to all other points are added to or subtracted from Rao’s quadratic entropy Q.

When NASA’s Wilkinson Microwave Anisotropy Probe (WMAP) and The European Space Agency’s Planck spacecraft returned independent measurements of 13.722 and 13.82 billion years, respectively, for the age of the universe, astronomers regarded their relative closeness as encouraging in light of much greater disagreement among previous measurements. Yet they took the 0.5% discrepancy that still remained to decisively signal the need for further work to “get it right.” In contrast, while Q and FRich can differ by orders of magnitude greater than 0.5%, BEF scientists appear to have no sound scientific basis for “getting it right” or even for accounting for these measures’ radically diverging assessments of functional diversity. These possibilities are precluded by the facts that Q and FRich both fully qualify as measures of functional diversity and that functional diversity is characterized only as “the” property that is measured by qualifying measures.

The implications of these conundrums are profound. BEF scientists claim that the functional diversity property of an ecosystem is a causal determinant of its ecosystem functioning. Validation of this claim minimally requires knowing the value of this causal variable. Yet there is no independent, biologically grounded basis for adjudicating between the radically differing infinitude of assessments that are on offer.

Faced with this multiplicity of conflicting measures and no sound biological basis for choosing from among them, BEF scientists propose to resolve this radical indeterminacy by “[comparing] their performances” (Clark et al. 2012) and selecting those that are “recommended” (Mouchet et al. 2010, 867) or “most suitable” (Villéger et al. 2008, 2290). They proceed to define a measure’s “performance,” its “recommendability,” or its “suitability” quite straightforwardly in terms of how well it correlates with the productivity numbers found in previously performed attempts to experimentally manipulate species richness (as observed at the beginning of this section).

This method for retrospectively “finding” how productivity is “affected” by functional diversity is a paradigmatic form of “HARKing” (formulating the Hypothesis After the Results are Known)—the scientific embodiment of the Texas Sharpshooter. Facing the side of his barn, that character blindfolds himself, pulls out his six-shooter, and then riddles the barn with holes with a random spray of bullets. Removing his blindfold, he achieves the highest possible correlation of shots to target hits by drawing those targets around the holes so as to minimize their distances from bullseyes. Of course, no one who is aware of how this remarkably high correlation was achieved would place credibility in the Texas Sharpshooter’s story—that he caused this to happen by virtue of his remarkable marksmanship.

Functional diversity researchers also achieve and are quite candid about achieving some high degree of correlation between functional diversity and productivity by retrospectively constructing a “high-performing” measure that “draws” the most advantageously located targets around previously-collected productivity numbers. No one who is aware of how this high correlation is achieved should place credibility in the BEF scientific causal story—that it came about by virtue of functional diversity’s remarkable ability to (in the words of the scientists cited above) “influence,” “control,” “enhance” or be a “key factor to maintain” ecosystem functions and services.³⁷ It is difficult to explain how BEF scientists gave credence to this story without, once again, referring to their ubiquitous claim that conservation of biodiversity is of paramount importance on account of its supposed causal impact on ecosystems (Section 1).

6 The ecosystem service rationale for conserving biodiversity

Throughout the more than two decades that BEF researchers have claimed to have evidence for the thesis that biodiversity is a major causal determinant of ecosystem functions, these scientists have routinely expressed their conviction that these efforts secure “scientific” warrant for conserving biodiversity. It is therefore remarkable that, to my knowledge, none of these scientists and no conservation organization has articulated a coherent argument in support of this conviction.³⁸ Instead, the passages quoted in §2.2 and in Section 5 exemplify what is ubiquitous: Right on the heels of warning that declines in biodiversity will cause declines in ecosystem functioning and with no intervening logic, they then claim that this decline in functioning entails a decline in ecosystem services, which conservation of biodiversity can prevent.

Because much of the world’s thinking about biodiversity and its conservation is beholden to this routinely expressed idea, it is important to see if some coherent argument for it can be spelled out. What follows is an attempt to do that by trying to think of all the steps that seem indispensable for arguing that, as scientists and conservationists continually suggest, biodiversity’s conservation is warranted on the grounds that its diminishment will diminish ecosystem functioning and consequently also ecosystem services. As in earlier sections of this essay, this one references productivity as a representative ecosystem function.

Empirical Premises:
• 1. (P1)

  1. Higher levels of biodiversity in ecosystems elevate their productivity; lower levels reduce it.
  2. This is the central causal thesis of BEF science that this essay has discussed.
• 1. (P2)

  1. P1 applies to the world’s unmanaged ecosystems because the causal effects of the appearance and disappearance of species in them is sufficiently similar to their random selection in experiments.
  2. P2 has drawn substantial prior critical comment. Doubts arise from evidence that sequences of species disappearances and introductions in actual ecosystems are not at all random but rather appear to depend on a variety of factors, including how the presence of any given species affects others (Wardle 2016, Srivastava and Vellend 2005, Solan et al. 2004, Vandermeer et al. 2002, Fridley 2001).

Normative Premises (normative terms are italicized):
• 1. (P3)

  1. An ecosystem’s empirically observable higher levels of productivity mean that it is higher performing in the normative sense that it is better at meeting a standard for how it ought to perform.
  2. The argument’s normative conclusion requires a premise like P3, which defines a general norm for how an ecosystem ought to perform in terms of how productive it is rather than some empirical claim about (say) higher productivity numbers.
  3. Obviously, some ecosystems are more productive than others. But ecosystems do not resemble automobiles for which standards of performance are based on specifications that indicate the degree to which they fulfill their human-designed purposes. Such specs ground the claim that your Porsche Spyder is higher performing than my Volkswagen “Bug” with respect to acceleration. Similar standards also apply to human-designed agricultural systems and may ground claims that their greater productivity makes them higher performing. But there exists no similar, biology-based specification that would ground norms for the performance of natural ecosystems.
• 1. (P4)

  1. The higher performance of more highly productive ecosystems (according to P3) is specifically due to their providing higher levels of service.
  2. It is well known and I am not the first to observe that P4 (which the argument requires to hold quite generally) is routinely contravened. Blooms of algae in aquatic ecosystems and proliferation of kudzu in terrestrial ecosystems make them extraordinarily productive. In these and many other cases, high levels of productivity are responsible for—in the non-causal sense of “constitute”—disservices.
• 1. (P5)

  1. An ecosystem’s provision of services is good by virtue of serving the interests and satisfying the desires of persons willing to pay for them.
  2. P5 is the cornerstone principle of economic valuative thinking, which presumes that a measure of a thing’s goodness is the degree to which persons vouch for it as desirable. P5 may be questioned most centrally because many people desire and vouch for their desire with a willingness to pay for things that are, overall, bad. One only need consider the dire consequences of desire for petroleum products and palm oil.
• 1. (P6)

  1. Ecosystems that provide higher service levels are better.
  2. The argument requires P6 in order to make the supposed ability of biodiversity to enhance ecosystem services a reason to conserve it. However, P6 follows from P5 only by assuming that the goodness of a thing is generally proportional to how much of it there is. But more is generally not better. That is amply illustrated by mundane facts such as that it’s better to stop eating when you’re full.
• 1. (P7)

  1. An ecosystem’s goodness preeminently consists in its provision of services.
  2. P7 asserts that the econometric, service-providing capability of an ecosystem overshadows all other goodness-conferring factors and therefore settles the question of whether or not it is good overall. If there are any grounds for thinking that it is true, I am unaware of any. Consideration of its combination with P8 (just below) casts doubt on there being any.
• 1. (P8)

  1. Conservation ought to promote ecosystem services by undertaking projects that make ecosystems as high performing as they can be in this service-providing way.
  2. P8 asserts that an opportunity to increase an ecosystem’s service levels engenders a presumptive obligation to bolster its service-providing capabilities. Like P7, P8 on its own is a questionable normative principle. In combination with P7, P8 encourages disregard for whatever else might be good about an ecosystem. In other words, it affords no consideration for species, populations, and organisms that either make no evident contribution to any service or that are responsible for disservices. It therefore arguably counsels that the promotion of services trumps eradication of organisms, if that is what it takes to underwrite strongly desired services. It also welcomes terraforming practices, from the addition, removal, and modification of soil and nutrients to the transformation of major land and water features, if these measures would ratchet up performance.
• 1. (P9)

  1. We ought to act so as to promote higher levels of biodiversity (and counter lower levels of biodiversity).

Conclusion:
• 1. (C)

  1. We ought to conserve biodiversity.
  2. That we ought not to allow levels of biodiversity to diminish is a straightforward corollary of P9.

There may be other ways to construct the sought-for argument and their details may vary. But all of them must bridge the gap from the causal premise about biodiversity to a normative one about services and from there to service provision as the preeminent object of conservation. Because of that, I believe that the version offered here exposes the fragility of assumptions and logic, which cannot be avoided in arguing that that biodiversity ought to be conserved lest ecosystem services be attenuated. Even aside from P1, which, this essay has argued, lacks credible evidence, multiple other assumptions are questionable and multiple steps appear to be logical missteps. If that is so, then the long-standing conservation mission of BEF research, which, for so long has worked so hard to secure P1, was always doomed to fail—even aside from failure of the empirical mission to secure that premise.³⁹

7 Perspective: Implications for biodiversity research and conservation

Summing up: The enormous and enormously influential program of BEF research has been a decades-long mission to find evidence for the thesis that biodiversity causally determines ecosystem functions. That empirical investigative mission was pursued in the service of another, conservation, mission to “save” biodiversity. Both appear to have been undermined by multiple mistaken assumptions that led to multiple missteps. If many of the defects, in retrospect, seem obvious, then the blindness of the scientists to them may well be explained by supposing that their emphatic commitment to these dual missions made them unable to say “no” to the question of whether evidence actually supported their faith in biodiversity as a principal determinant of ecosystem functions.

In short, the BEF research program may be one of those uncommon yet not so rare historical episodes in which deep commitment to an idea from outside science commandeered critical evaluation of the evidence and subsequently led science off the tracks. In this case, the extra-scientific idea that derailed BEF science is the arguably noble one of saving biodiversity. But that idea is morally hollowed out by making it ride, not on whether the many different organisms whose existence is at stake can simply live their lives, but rather on how capably they serve people.