A theoretical physicist's journey into biology: from quarks and strings to cells and whales

In October 1993 the US Congress, with the consent of President Clinton, officially canceled the largest scientific project ever conceived after having spent almost $3 billion on its construction. This extraordinary project was the mammoth Superconducting Supercollider (SSC) which, together with its detectors, was arguably also the greatest engineering challenge ever attempted. The SSC was to be a giant microscope designed to probe distances down to a hundred trillionth of a micron with the aim of revealing the structure and dynamics of the fundamental constituents of matter. It would provide critical evidence for testing the 'Standard Model' of the elementary particles and their interactions, potentially discover new phenomena, and lay the foundations for a Grand Unified Theory of all of the fundamental forces of nature, thereby giving insights into the evolution of the Universe from the Big Bang. It was to be over 50 miles in circumference and accelerate protons up to energies of 20 trillion electron volts, eight times greater than that of the Large Hadron Collider now operating in Geneva that was recently in the limelight for discovering the Higgs particle.

Its demise was due to many, almost predictable, factors, including budget issues and the state of the economy, political resentment against Texas where the machine was being built, uninspired leadership, and so on. But one of the major reasons for its collapse was the rise of a climate of negativity towards traditional big science and to physics, in particular. This took on many forms, but one that many of us were subjected to, was the oft-repeated pronouncement [1] that 'while the nineteenth and twentieth centuries were the centuries of physics, the twenty-first century will be the century of biology'.^{1 ,2} Even the most arrogant, hard-nosed, physicist had a hard time disagreeing with this, but what incensed many of us was the implication, oftentimes explicit, that there was no longer any need for further basic research in this kind of physics since we already knew all that was needed to be known! [2] Sadly, the SSC was a victim of this misguided thinking.

At that time I was overseeing the high energy physics program at Los Alamos where we had a significant involvement with one of the two major detectors being constructed at the SSC. I was a theoretical physicist (and still am) whose primary research interests were in fundamental questions concerning the elementary particles, their interactions and cosmological implications. My visceral reaction to the provocative statements concerning the diverging trajectories of physics and biology was that, yes, biology will almost certainly be the predominant science of the twenty-first century but, for it to become successfully so, it will need to embrace some of the quantitative, analytic, predictive culture that has made physics so successful; biology will need to integrate a theoretical framework based on underlying mathematisable or computational principles with its more traditional reliance on statistical, phenomenological and qualitative arguments. Needless to say, I knew almost nothing about biology and this outburst came mostly from arrogance and ignorance.

Nevertheless, I decided to put money where my mouth was. I was in my mid-fifties and becoming increasingly conscious of the inextricable encroachment of the aging process and the consequential finiteness of life. I come from a long line of short-lived males so it seemed natural to begin my foray into biology by learning about aging and mortality. Since these are among the most ubiquitous and fundamental characteristics of life, I presumed that almost everything was known about them. To my great surprise I learnt that, not only was there no accepted general theory of aging and death, but that the field, such as it was, was relatively small and somewhat of a backwater. Furthermore, few of the questions that would be natural for a physicist to ask seemed to have been addressed. For example, where does the scale of human lifespan come from? Why is it of order a hundred years and not a thousand, a million or ten, and how is this related to the microscopic time scales of complex molecules constituting our genes and respiratory enzymes? And why do mice, made of pretty much the same stuff as we are, live for just 2–3 years whereas elephants live for up to 75, despite both having approximately the same number of heart-beats in their lifetimes? What, in fact, would constitute a quantitative, predictive mechanistic theory for aging?

It seemed to me that, if biology were a 'real' science (meaning that it was like physicsǃ), then I ought to be able to pick up an introductory biology text-book and find in its discussion of the basic features of life, a quantitative mechanistic theory of aging which would include an analytic calculation showing why we live for about 100 years, as well as answering the sorts of questions posed above. No such luck, nor any hint that these were questions of interest. This came as quite a surprise but it stimulated me to begin pondering the question of aging and mortality, beyond mere philosophical reflections, during interludes between grappling with quarks, gluons, dark matter and string theory.

At around this time I came across the wonderful classic, On Growth and Form, written almost 100 years ago by the eminent biologist D'Arcy Thompson [3]. He begins his tome by quoting Kant's observation that 'chemistry......was a science but not Science......for that the criterion of true Science lay in its relation to mathematics'. Thompson discussed how there now existed 'mathematical chemistry' (thereby elevating chemistry to Science, with a capital S), but that biology had remained qualitative, without mathematical foundations or principles, implying that it was still just 'science' (with a lower case s). Despite the extraordinary progress made during the intervening century, I began to discover that the spirit of Thompson's characterization of biology still has significant validity.

I surmised that to understand how a system ages and dies, whether a mammal or an automobile, one first needs to understand how it stays alive. This led me to think about energy, entropy, maintenance, damage and repair but, most importantly, it led me to metabolism, Kleiber's law and, by extension, to allometric scaling. I learnt that, despite the extraordinary complexity and diversity of life, many of its most fundamental and complex phenomena, from cells through multi-cellular organisms to ecosystems, scale with mass in a surprisingly simple and systematic fashion³ [4–6]. These scaling laws are typically power laws whose exponents approximate simple multiples of 1/4. The best known is Kleiber's law for metabolic rate, which exhibits a 3/4 exponent over an astonishing 27 orders of magnitude. Similar 'laws' hold for almost all measureable traits and life-history events ranging across all taxonomic groups and include metabolic rates, growth rates, DNA nucleotide substitution rates, genome lengths, tree heights, cerebral grey matter and lifespans.

Here was an area of biology that was manifestly quantitative and, at the same time, expressed a spirit of 'universality' beloved by physicists. It had attracted the attention of eminent biologists such as Huxley, Haldane, and Thompson, but had eventually been eclipsed by the reductionistic molecular revolution. In the 1980's several excellent books³ had summarized what was known about allometric scaling though no general theory had, as yet, been developed [4–6]. This very much surprised me since these laws seemed quite remarkable providing a possible window onto underlying emergent principles of biology. After all, each organism, each sub-system and organ, each cell type and genome, had evolved by natural selection with its own unique history in its own ever-changing environmental niche, so naively, one would not have expected any systematic behaviour to emerge, but rather huge variance reflecting historical contingency and the randomness implicit in natural selection. Yet, almost any measurable quantity scales in a remarkably systematic and regular fashion, strongly suggesting that generic underlying dynamical processes were at work constraining natural selection. The predominance of 'universal' quarter-power scaling across all scales and life forms and the existence of approximate invariant quantities surely tells us something fundamental about biological systems. It opens a possible window into underlying emergent laws of biology and to the conjecture that the generic coarse-grained behavior of living systems obeys quantifiable laws that capture their essential features.

As a physicist this looked like a wonderful problem to think about, especially given my morbid interest in aging and death and that even lifespans scale systematically (albeit with large variance). It was clear that whatever was at play had to be independent of the evolved design since the same laws were manifested by mammals, birds, plants, crustacea, cells, and so on. This led to the idea that networks might be the key since a commonality of all life is that it is sustained by hierarchical fractal-like networks which have evolved at all scales to support and sustain the huge number of localized microscopic units constituting an organism. Functionally, biological systems are ultimately constrained by the rates at which energy, metabolites, and information can be supplied through these networks. It was proposed that scaling laws and the generic coarse-grained behavior of biological systems reflect constraints inherent in generic physical and mathematical properties of these networks.

As I was struggling to develop a network-based theory for the origin of quarter-power scaling, a wonderful synchronicity occurred; I was serendipitously introduced to James Brown and his then student, Brian Enquist. They too had been thinking about this problem and had speculated that network transportation was a key ingredient. Jim was (and still is) a distinguished ecologist (he was president of the Ecological Society of America when we met) and was well known, among many things, for his seminal role in inventing 'Macroecology' [7]. He had become associated with the Santa Fe Institute and it was through SFI that the connection was made. Thus began 'a beautiful relationship' with Jim, SFI and Brian and, by extension, with the ensuing cadre of wonderful post-docs and students that worked with us.

The collaboration, begun in 1995, has been enormously productive, extraordinarily exciting and tremendous fun. But, like all excellent and fulfilling relationships, it has also been a huge challenge, sometimes frustrating and sometimes maddening. Jim, Brian and I met every Friday beginning around 9.00am and finishing around 3.00pm with only short breaks for necessities. This was a huge commitment since we both ran large groups elsewhere. Once the ice was broken and some of the cultural barriers crossed, we created a refreshingly open atmosphere where all questions and comments, no matter how 'elementary', speculative or 'stupid', were encouraged, welcomed and treated with respect. There were lots of arguments, speculations and explanations, struggles with big questions and small details, lots of blind alleys and an occasional aha moment, all against a backdrop of a board covered with equations and hand-drawn graphs and illustrations. Jim and Brian generously and patiently acted as my biology tutors, exposing me to the conceptual world of natural selection, evolution and adaptation, fitness, physiology and anatomy, all of which were embarrassingly foreign to me. Like many physicists, however, I was horrified to learn that there were serious scientists who put Darwin on a pedestal above Newton and Einstein.

For my part, I tried to reduce complicated non-linear mathematical equations and technical physics arguments to relatively simple, intuitive calculations and explanations. Regardless of the outcome, it was a wonderful and fulfilling experience. I particularly enjoyed being reminded of the primal excitement of why I loved being a scientist: the challenge of learning and developing concepts, figuring out what the important questions were and occasionally being able to suggest answers. In high energy physics we mostly know what the questions are and most of one's effort goes into trying to be clever enough to carry out the highly technical calculations. In biology I found it to be the other way round: months trying to figure out what the problem actually was and what needs to be calculated, but, once that was accomplished, the actual mathematics was relatively straightforward.

It took almost a year to get the concepts and mathematics straight, but ultimately we showed how the 1/4 power scaling laws follow from underlying principles embedded in the dynamics and geometry of space-filling, fractal-like, branching networks, presumed to be optimised by natural selection. A sampling of early papers can be found in [8–11]. These ideas lead to a general quantitative, coarse-grained predictive framework for addressing many problems across the entire spectrum of biology including plant, animal and tumor vascular systems (flow rate, pulse rate, pressure, and dimensions in any vessel), metabolic rates and growth curves (for both healthy organisms and tumors), aging and mortality, sleep, cell size, DNA nucleotide substitution rates, the organisation and dynamics of forest ecosystems (size, density and energy distributions of leaves, branches, trees), and the number of RNA molecules and mitochondria in cells. Reference [12] is a summary review written for biologists whilst [13] is a non-technical review written for physicists. Part of this body of work has since become known as 'the metabolic theory of ecology' [14].

In addition to a strong commitment to solve a fundamental long-standing problem that clearly needed close collaboration between physicists and biologists, a crucial ingredient of our success was that Jim and Brian, in addition to being excellent biologists, thought like physicists and were appreciative of the importance of a mathematical framework grounded in 'first principles' for addressing problems. Of equal importance was their appreciation that, to varying degrees, all theories and models are approximate; the challenge is to identify the important variables that capture the essential dynamics at each organizational level of a system thereby leading to a calculation of their average properties. This provides a coarse-grained 'zeroth order' point of departure for quantitatively understanding specific biosystems, viewed as variations or perturbations around idealized norms due to local environmental conditions or historical evolutionary divergence.

I later learnt that Jim and Brian were the exception rather than the rule. Despite some of the seminal contributions that physics and physicists have made to biology, there seems to remain a general suspicion and lack of appreciation of theory and mathematical reasoning among many biologists. Some years ago John Maynard Smith told me that one of his early papers included equations and that it was subsequently rejected by a referee who declared that 'theory' had no place in biology. We too have received similar treatment by a referee; fortunately, a wise editor over-ruled the recommendation and our paper has since received over 500 citations.

Physics has benefited enormously from a continuous interplay between theory and experiment, a great example of which is the recent discovery of the Higgs particle. Physicists take for granted the concept of the 'theorist' who 'only' does theory, whereas, by and large, biologists do not. A 'real' biologist has to have a lab with equipment, assistants and technicians who observe, measure and analyze data. Doing biology with just pen, paper and lap-top simply doesn't cut it. There are, of course, areas of biology, such as biomechanics, genetics, and evolutionary biology, where this is not the case. I suspect that this situation will change as the era of big data and intense computation encroach on all of science and we aggressively attack some of the big questions such as the brain and consciousness, environmental sustainability, cancer, and, of course, aging and death. However, I agree with Sydney Brenner's provocative remark [15] that 'Technology gives us the tools to analyse organisms at all scales, but we are drowning in a sea of data and thirsting for some theoretical framework with which to understand it....We need theory and a firm grasp on the nature of the objects we study to predict the rest'. It is amusing to note that Brenner begins his article with the astonishing pronouncement that 'Biological research is in crisis'.

Many of us recognize that there is a cultural divide between biology and physics, sometimes even extending to what constitutes a scientific explanation as encapsulated, for example, in the hegemony of statistical regression analyses in biology versus quantitative mechanistic explanations characteristic of physics. Nevertheless, we are witnessing an enormously exciting period as the two fields become more closely integrated, leading to new inter-disciplinary sub-fields such as biological physics and systems biology. The time seems right for revisiting D'Arcy Thompson's [3] challenge: 'How far even then mathematics will suffice to describe, and physics to explain, the fabric of the body, no man can foresee. It may be that all the laws of energy, and all the properties of matter, all.....chemistry....are as powerless to explain the body as they are impotent to comprehend the soul. For my part, I think it is not so'. Many would agree with the spirit of this remark, though new tools and concepts including closer collaboration may well be needed to accomplish his lofty goal.