Cognitive neuroscience is yet to produce applications of major clinical impact. If its relative immaturity is to blame, we need merely wait. But if its approach is fundamentally ill-suited, we could be left waiting forever. We must therefore consider how well the means of cognitive neuroscience support translational ends. Such consideration cannot be expected to emerge spontaneously from the field itself, for neuroscience evolves under the selective pressure of supposed understanding, not the collateral of mechanistic insight translation is widely perceived to be. Nor may we presume the obstacles to translation to be peculiar to each cognitive subfield and unlikely to be illuminated by a general analysis: it is possible they lie within the proximal, cardinal steps common to all of neuroscience. Here we examine this possibility, show it to be overwhelmingly likely, and outline how neuroscience must change if it is to deliver real-world patient impact.

Most societies give primacy to the individual person, imposing collective interests only with reluctance. This is especially true of healthcare, where the object of clinical action is archetypally the individual and the group only secondarily. To take a striking example, we could overnight revolutionize population outcomes in acute stroke by intervening with thrombolytic therapy at the kerbside, bypassing delays that hospital transfer for diagnostic computed tomographic scans inevitably introduce ( Wardlaw et al., 1997). However, no matter how compelling the population statistics, such a manoeuvre is rendered unconscionable by the resultant death or greater disability of the 10% of patients with primary intracerebral haemorrhage ( Qureshi et al., 2009). Even where the stakes are less sharply polarised, it remains difficult to implement any treatment whose individual benefit is only crudely probabilistic, for all interventions have a cost: both personal and financial. Moreover, since populations merely summarise effects on individuals, the greater the individual variation, the lesser the population-level impact. Both constitutively and politically, translational success or failure is thus critically dependent on our ability to individualise our interventions.

How is individuality determined? Consider by way of illustration that most personal part of the body, the face ( Figure 1). Though one feature may sometimes be uniquely idiosyncratic, to distinguish a face from another generally requires the conjunction of many features, even when all redundancy is eliminated. Such irreducibly high intrinsic dimensionality is conveniently captured by the notion of minimum description length ( Rissanen, 1978) – intuitively, the most compressed complete description of a system. This quantity sets a hard limit on the minimal complexity of any model that must distinguish one state or instance of a system from another to perform its task. No matter how clever the mathematics, a machine vision model tasked with (say) classifying the sex of a face will always perform badly when starved of input features because no small subset of features contains the necessary information; conversely, even a relatively unsophisticated model with sufficient capacity will perform well, given enough data ( Parkhi et al., 2015; Schroff et al., 2015; Zhou et al., 2015). It should come as no surprise that face coding in the primate brain takes a high-dimensional approach, deriving identity by projecting a multiplicity of features onto a compacted representational space ( Chang & Tsao, 2017). Now our concern is not individuation simpliciter but the individuation of causal mechanisms of predictive or prescriptive utility. For this we need a causally constrained extension of the concept of minimal description length: what we here term a minimal causal field. To see how this is specified requires a brief examination of biological causality.

We have a natural intellectual predisposition to causal models with two cardinal features: economy and seriality ( Hacker, 2007). This is a consequence partly of reasoning by analogy and partly of practicability. The intelligible, mechanistically pellucid processes we observe in the non-organic world and exploit in the machines we build tend to have few parameters of causal significance, arranged sequentially. It seems natural to apply the same approach to biology, indeed inevitable, for a causal model with (say) a thousand parameters is intellectually intractable. When we insist on identifying necessary and sufficient links within a more or less serial chain, it is because no other option has been open to us.

But whereas this notion of causation is adequate for understanding simple, serially organised systems, it does not scale with complexity. In complex systems, where a multiplicity of factors is jointly brought to bear on the outcome, each individual factor becomes an insufficient but necessary part of a set of factors that are unnecessary but sufficient for the result: an INUS condition ( Mackie, 1974). To give an adequately explanatory account it is necessary to specify a causal field of many such INUS conditional factors that interact in complex ways (see Figure 2).

Do neural systems require such a complexity of causal specification? Consider the far simpler behaviour of artificial neural networks, such as deep-learning architectures in which layers of laterally connected units are hierarchically arranged in an end-to-end error-minimising stack ( Goodfellow et al., 2016; LeCun et al., 2015). Taking the input-output transformation produced by such a network as its “function”, we can test the causal contribution of sets of network nodes by examining the functional consequences of deactivating them, essentially performing artificial neural network lesion-deficit mapping ( Adolphs, 2016; Rorden & Karnath, 2004). When a trained network is subjected to such drop-out ( Gal & Ghahramani, 2016; Le Cun et al., 1989; Srivastava et al., 2014; Wan et al., 2013), the degradation of any output is gradual, and often proportionate with the mass of deactivated nodes but varying with their identity in a complex manner that precludes the identification of a "critical" node, or even a clear ranking of the material contribution of individual nodes. Causality is constitutionally distributed in a way any conventional description simply cannot capture; only a causal field specification will do ( Mackie, 1974).

The widespread use of drop-out in the deep-learning literature shows causally distributed architectures learn complex input-output transformations better than other systems examined to date ( Goodfellow et al., 2016). They are also more robust to damage, an important consideration for any biological system. However, there is no need to appeal to plausibility in our argument: to the extent that a node contributes to function it must be causally relevant. It is inconceivable that the observed complexity of real neural systems is merely epiphenomenal to a much simpler underlying causal organisation. In any event, since we cannot assume the minimal causal field is small, we need to consider how to model it when it is irreducibly large.

In seeking to understand the causality of any complex system, we must distinguish between causally relevant and incidental variation. Though rarely acknowledged, the approach to making such a distinction depends critically on a cardinal assumption about a system’s structure. If we assume the organisation of a particular brain network is fundamentally the same across people—i.e. it is monomorphous—individual variation may be treated as noise. The population mean will then be the best available guide to the fundamental mechanism and to its expression in individuals. This is an implicit assumption behind the vast majority of studies in cognitive neuroscience where a set of estimates, derived from a small group, are considered to reveal general truths about the brain. But if, at some causally critical level, the neural organisation is not the same across people—i.e. it is polymorphous—individual variation cannot be treated as noise and the population mean will be a poor guide, both to mechanism and individual behaviour (see Figure 3). The distinction between monomorphous and polymorphous organisation is crucial because it radically alters the optimal inferential approach. We suggest the common assumption of a monomorphous architecture of the brain is unjustified—both empirically and theoretically—and must be discarded, for the following reasons.

A neural architecture can be shared across individuals only as far as it is identically specified by the genome, the environment, and their interaction. The constitutive variability of the environment leaves the genome as the primary driver of inter-individual homology. Genomic information content is information theoretically limited by the number of base pairs and the range of nucleotide options at each locus. If we implausibly ( Rands et al., 2014) assume every locus is both functional and material to the operations of the brain, so that no section is redundant, we have only ~6 x 10 ⁹ bits of information, roughly the content of an old compact disc. Even if all this information is used to specify the minimal causal field of a human brain, leaving none for the rest of the body, we remain unable to meet even the most conservative estimates of the brain’s complexity. A commonly offered prenatal estimate, ~10 ¹⁴ bits, derived from the number of synapses in the brain ( Huttenlocher & Dabholkar, 1997; Tang et al., 2001), implausibly assumes a synapse can only encode one bit at any one time, and that neural connectivity is the only differentiator. This is equivalent to treating a neuron rather like a transistor in a modern computer-processing unit, distinguished from its neighbours only by the role assigned to it. In short, we are not faced with an information gap but more an information chasm. The conclusion is that a great deal of the functional architecture of the brain cannot be monomorphous, for the necessary information simply is not there.

The brain cannot violate the laws of physics, so how can complexity arise from so relatively impoverished an initial specification? Theoretically the simplest approach is to inject randomness ( Matsuoka, 1992) at the outset of development, allowing a complex order to emerge downstream through feedback learning.

Such stochastic initiation is evident in normal neural development, where as many cells face an orchestrated death, at great structural and energetic cost to the organism, as survive into adulthood ( Lossi & Merighi, 2003). Seemingly playing a compound game of “Russian roulette cum musical chairs”, developing neurons are subjected to an environmentally dependent selection process, determined only once development is in play. The process is not fully specified in the genome, or else the redundant neurons would never be born. The biologically dominant prohibition of regeneration in the central nervous system, far from being mysterious, is necessary where the organising information emerges during development, and is therefore stored only in the final product itself.

Equally, the ubiquity of neural feedback learning is evident in the way recurrence is so densely woven into the neural fabric. One-way brain pathways are an exception, not the rule ( Bressler & Menon, 2010). It could not be otherwise, for learning—here neural learning—is the only way an order more complex than the initial genetic specifications could conceivably arise.

Now a stochastically-initiated, feedback-learning system, with multiple tuneable parameters, will inevitably have many different solutions for the same target input/output transformation. It is therefore bound to be polymorphous. Crucially, there need be no mechanism for regularising such solutions across individuals to impose a higher, species-level order, for no such order need exist, even if it could be imposed. An organism adapts its structure in response to errors only within its own input-output transformations, not those of others; biology does not do federated learning ( McMahan et al., 2016).

Though our concern is to define the bounds of biological possibility our models must be able to cover, it is natural to seek empirical evidence of biological plausibility. The only credible evidence can come from a system that has been comprehensively characterised. Since our claim is about under-estimating complexity, we may as well pick a simple one. Consider, the gut of the lobster, or rather the stomatogastric sub-circuit, meticulously studied for decades by Eve Marder. Though absurdly simple anatomically, with only 30 neurons, and physiologically, with only regular peristaltic oscillation, the relation between the two is not only complex, but also polymorphous in precisely the way described. The same functional physiology can be arrived at from different individual neuronal “settings”, both across time in the same animal and across different animals ( Marder & Bucher, 2007). We cannot presume that the rules of human functional brain organisation are any simpler.

We must confront the functional complexity of neural organisation before us if translation from mechanisms of disease to rational treatments is to be possible. How do we generate, estimate, and validate polymorphous neural models of potentially incomprehensible complexity?

We have seen that complex, polymorphous systems require irreducibly many variables to achieve individually meaningful predictions. The resultant expansion of the parameter space under-determines models in proportion to the small scale of commonly available data. This familiar curse of dimensionality [25] makes good solutions hard to find and even harder to generalize, for the risk of purely accidental fits increases with the number of parameters.

But we should recognise that dimensionality also carries a blessing. Consider the parameterisations of contrasting dimensionality shown in Figure 1. Such individualisation as our low-dimensional parameterisation may achieve, here the inter-ocular distance, will be strongly dependent on the precision of measurement, for everyone is differentiated along a single dimension. In contrast with a high-dimensional parameterisation, such as a crudely pixelated rendition of the image, the precision of each individual variable is much less important, for the signal is conveyed in the covariance across variables. Crucially, since the structure of the underlying high-dimensional pattern is unlikely to resemble instrumental or other sources of noise, we can achieve greater individualisation with lower quality data. This is intuitively obvious in our ability to recognize faces from noisy, low-resolution images, robust not only to affine transforms of the data such as contrast, zoom, and skew, but also to fairly complex non-linear distortions.

The conventional resistance to using routinely acquired data on the grounds of noise and heterogeneity is only justified where the analysis is low dimensional. When measuring (say) total grey matter volume, it matters that one scanner will generate consistently greater estimates compared with another. But when extracting the high-dimensional variation of grey matter concentration across the brain, such effects will drop out as irrelevant affine shifts that leave the complex, individuating covariance patterns intact.

Perhaps the most important objection to high-dimensional modelling—the scale of the data required—is thus addressable through collections for another purpose, obtained outside a research environment. In the domain of structural brain imaging, the obvious source is clinical imaging ( Frackowiak & Markram, 2015). Since brain imaging is carried out to resolve diagnostic uncertainty towards normality almost as often as away from it, such data need not be restricted to the realm of pathology. Similarly, though smartphones may fall short of the precision of dedicated psychophysical devices, their ubiquity and critical mediating role in life enable the collection of rich, high-dimensional data on a vast scale ( Teki et al., 2016).

Of course, the correct balance between data size and data quality is an empirical question, to be settled case-by-case. But we cannot assume the former must be gated by the latter, and discount a high-dimensional approach simply because a conventional psychophysical laboratory cannot scale to thousands of participants. Rather, we must reconsider what we actually need to know, and what human activity may collaterally disclose it.

What use are high-dimensional models if they are too complex to understand? Where outcomes are highly variable, as is the norm in cognitive neurology, prediction is clinically invaluable, not simply because patients are consoled by accurate prognosis but because interventions need to be guided by their individually predicted responses. If a “black box” predictor is the best guide to a correct choice of treatment actuarially, it would be difficult to justify not following it merely because its operations cannot be paraphrased in intelligible prose.

Moreover, clinical interventions are already primarily driven by “black boxes” - the contents of our heads are a good example. To give a reason for acting is not to specify a cause or to imply an underlying causal model, it is kin with pointing to a latent variable. It is only rarely, where very simple biological systems are concerned, never in the brain, that we have a perspicuous, mechanistic explanatory model available. That a human expert can cite a reason for his actions does not make his decision-making less opaque than that of a synthetic counterpart.

If a system requires a complex model to describe it, then it is complex. Translational science needs to adjust to this emotionally, not hopelessly attempt to change it intellectually. A causal field so intricate it can only be specified as an artificial neural network with a million parameters is explanatory, even if its incomprehensibility makes us hesitate to use a word stronger than predictive. We can no more hope to understand the brain shackled to simple, linear models, than a literary critic could hope to understand Shakespeare applying the basic rules of grammar alone.

Until a decade ago, the foregoing analysis would have been unbearably nihilistic, for we had neither the data nor the computational tools to realise the alternative it urges. The ground is still new and uncertain, yet to be proven capable of supporting the structure we argue it is imperative we begin to erect on it. But if we wish to move beyond discussions of tractability or feasibility into translatable action, we must confront the single most striking fact about the brain - its immense complexity.

The difficulties are all the greater for being distributed across many intellectual, technological, even political domains, reaching deep into the foundations of the very notion of biological understanding. A cognitive neuroscience recast in the form we propose will have more in common with meteorology than horology. If so, then it will be because the fundamental nature of the brain has compelled it, for what we urge here above all is to let the data, not our own brains, speak first. And if effective prediction supplants defective understanding as a result, those outside the field, whose lives cognitive neuroscience and cognitive neurology seek ultimately to serve, will appreciate the exchange.

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