Chapter 13
Epilogue: Toward a Quantitative Theory of Oncology
Medicine is both art and science. As promised in the introduction, this book has focused primarily on the scientific side of the medical subfield of oncology. Specifically, we explored applications of mathematics, primarily dynamical systems, to cancer biology and treatment. We have attempted to give readers a glimpse of a few major research threads in the developing field of mathematical oncology, with an emphasis on seminal work, applications to treatment, and biological background and motivations.
The growth of the field in the last 10 years alone precludes any attempt on our part at a comprehensive survey, and for this we owe many of our colleagues, whose work we deeply appreciate, an apology. We hope that anyone who feels slighted in these pages will recognize and take comfort in our attempt to give students the tools necessary to study and place into context any work we have omitted.
But in addition to these conscious (and unconscious) omissions, this book is missing something vital, because the field itself is missing a critical piece connecting the art and science of medicine. We realize that this sounds like hyperbole. It is not. As we pointed out in Chapter 1, medical practice is considered evidence-based when the art is informed by science. Science’s main product is theory. Here we use “theory” not in the journalistic sense of a hunch or shot-in-the-dark, but in the sense expressed by the U.S. National Academy of Sciences as “[a] well-substantiated explanation of some aspect of the natural world that can incorporate facts, [natural] laws, inferences and tested hypotheses” [19, p. 2], or in the substantially similar but more complete expression by Gerald Holton and Stephen Brush [11, p. 27]:
[A theory] is a conceptual scheme we initially invent or postulate in order to explain to ourselves, and to others, observed phenomena and the relationships among them, thereby bringing together into one structure the concepts, laws, principles, hypothesis and observations from often very widely different fields.
In other words, theory expresses our current understanding of the natural world and is generally “well-substantiated.” When we say that science informs the medical art, we mean that medical practice refers primarily to the best theory currently available.
And here we find the missing piece. Medicine largely lacks coherent, quan-titative—or better, mathematical—theories. One may wonder how we can say such a thing at the end of a book full of medical theory couched in mathematics, but the key word in the claim is coherent. Scientific medicine simply has not produced mathematical theory applicable to broad areas of medicine. To be clear, we presume no sort of “grand unified medical theory”; indeed, such a pretension seems, to us, preposterous. But what has become glaringly obvious to us while putting this text together is the ad hoc manner in which mathematical models are applied to biological and physical phenomena relevant to medical oncology. And we thoroughly expect that deepening the connections among traditionally disjointed theoretical constructs will increase the power theory will have to inform medical art.
In this day and age, one may counter-argue that medicine, and oncology in particular, needs no coherent mathematical theory. Medical oncology already boasts one of the best theories in all of medicine, expressed by Hanahan and Weinberg as the “hallmarks of cancer,” a list of necessary and sufficient phenotypes a cell must acquire to become malignant [9, 10]. The theory is completely coherent, highly successful, becoming increasingly comprehensive and yet devoid of mathematics. From a more general perspective, medicine looks toward genomics for its theory, and to argue that genomics is not a sufficient source of coherent theory is to argue against the dominant intellectual tradition of early 21st century biology. But this is precisely what we argue here. In fact, we go so far as to claim that genomics is the opposite of theory. Theory identifies patterns within chaos. Genomics generates chaos.
The general genomics program, as applied to a given species, attempts to generate a consensus sequence for the entire genome of that species, characterize all or most variation in homologous DNA sequences among individuals, and identify the function(s) of all functional DNA sequences. Clearly this is an ideal. However, as of this writing the genomic program has produced draft genomes, with accounts of variation, for humans—both modern and Neanderthal—many important human pathogens and an array of species of varying importance to human health. And, as a generator of information and knowledge, the genomics program has enjoyed many outstanding successes. Genomics has identified hundreds (or more) of genetic variations— genotypes—associated with cancer progression, pathogenesis and treatment resistance, some of which we exemplify in this book. Genomics has shown us broad patterns of gene regulation, like upregulation of ribosome structural genes, that led to new hypotheses about the biological nature of the disease [5, 6, 13]. Most importantly, it has unveiled the fundamental complexity of life at the level of macromolecules. Genomic organization, for one thing, is not as originally envisioned. The early notion of “one gene, one molecule” (i.e., protein) is deeply flawed—there appear to be around 20,000 traditional coding genes in the human genome, but our cells make more than 100,000 proteins by traditional transcription and translation, let alone other molecular products of transcription, like rRNA, iRNA, eRNA and others. Furthermore, the idea that a gene—however one wishes to define such a thing—occupies a specific locus in the genome is also contradicted. Even the most traditional of genes is regulated by enhancers scattered in remote locations of the genome. To give a single, medically relevant example, one genotype causing lactose persistence in humans—i.e., expression of the enzyme lactase-phlorizin hydrolase, which declines significantly as individuals with “adult lactose intolerance” age—is not determined by the sequence of the LCT (lactase) gene. Rather, the persistence mutation1 is found more than 10,000 base pairs upstream of the LCT promoter in a gene called MCM6. The “normal” gene product of MCM6 has nothing to do with lactose metabolism. However, a region within it, where the mutation is found, acts as an enhancer for LCT. This sequence in MCM6 is therefore a very real part of the LCT gene, although tradition says it is not. This tradition is likely to be abandoned as the dominant role of enhancer and other regulatory regions becomes more clear (see, e.g., [1, 20]).
As these few examples illustrate, genomics has been successful in that it has forced us to reorganize our thinking—that is, it has forced us to build theory to explain the cascade of new observations. But this theory has been by and large ad hoc and essentially qualitative. Nevertheless, the successes have given medical science a case of “-omics fever,” a proliferation of research programs attempting, like their genomic parent, to produce enormous lists of all intracellular proteins (proteome), RNAs (transcriptome), smaller molecules (metabolome) and molecular interactions (interactome), among other “-omes.”
As useful and interesting as they are, such gobs of data are not theory and therefore are not considered an end product by the research community. The main theoretical attacks employed in the classical -omics program involve cataloguing and cross-referencing all the data, with some attempt to identify patterns (bioinformatics), and an attempt to understand the cell from an engineering perspective, in which one identifies the general behavior of sets of interacting molecules without slogging through all the details of every interaction (systems biology). The product of the systems biology program would be what is now dubbed the “systeome,” another list, this time of all systems in the cell, their properties and their connections to other systems. Beyond this, the ultimate end point—the final theory—generated by this program is only ever vaguely expressed at best. The literature expresses little discomfort with the end goal being yet another list—there seems to be an assumption that eventually we will hit on a list so simple that the patterns will be obvious from inspection. But at some point we must move beyond lists. One such path might be thought to lead to a brute-force integration of the “systeome” into an immense computational program simulating all molecular activities within a cell.
Neither of these end points—another list or a brute-force simulation—are satisfactory. The former is obviously not an end-goal. At some point we have to integrate the elements of the list—molecules or systems or whatever—into a comprehensible formulation, one also capable of describing variation among the 200 different cell types in a healthy mammalian body, not to mention all pathological cells. And while a complete simulation of the cell would without question be such an integration, it is not practical. Certainly, such a simulation at the molecular level is absurd. It would require estimates of the number of each chemical species as they vary over time. Due to intracellular concentration and compartmentalization, these concentrations would be best represented as random variables, requiring stochastic characterization in the models. In addition, all parameters governing all possible dynamic interactions among these molecules would have to be accurately assigned. If molecular interactions require on average p unique parameters to be correctly modeled in a single cell, and each molecule interacts on average with n others, then one must accurately estimate on the order of p(n − 1) 105 parameters to simulate only protein interactions in a single cell. Even if p and n are modest (10 or less), an accurate model of the proteomes of the 200 types of cells in the healthy human body could easily require hundreds of millions to billions of parameter estimates before one even begins to address the transcriptome, the metabolome or any other -ome. More would be needed to characterize diseased cells and pathogens. And we have not even mentioned intracellular interactions, which are clearly critical in many if not most disease states.
This is chaos (in the literary, but probably also mathematical, sense). Detailed modeling of chaos like this has never, in the history of science, been the way forward. Recognition of this fact was one factor motivating the systems biology program, which in part attempts to represent cascades of molecular interactions as individual “systems” with relatively simple inputs and outputs that can be easily modeled. And, although this program has generated insight and testable explanations or descriptions (the primary goals of theory), how these systems are to be integrated into simple patterns, common themes, understandable descriptions and explanations that fit together into a more-or-less comprehensive narrative (the ultimate goal of theory) remains an open question.
One should not mistake our message. We claim that -omics and systems biology programs have immense value. One must have an accurate, clear view of the chaos before one can begin to discern patterns. Hence, our claim above that genomics generates chaos means that it provides the fodder needed to sustain theory-builders. Systems biology is a step in the right direction. However, at some point we must begin to emphasize a mathematical and computational program that rises above the ad hoc models of the past and connects them in a single, descriptive and explanatory framework.
Luckily, classical biology has such a theoretical framework ready-made— evolution. Another general lesson we learned while putting this book together is that the mechanisms of evolution, particularly natural selection and genetic drift, arise either explicitly or implicitly, but always naturally, in nearly every explanation of cancer etiology, pathogenesis and treatment. This includes both empirical and theoretical studies, and this book provides many examples of the latter. Revealingly, in an astonishing number of cases, when researchers recognized the evolutionary theme in their own results, they gave every appearance of reinventing Darwin’s wheel. For example, Darwin’s evolutionary insight is more frequently referred to as “mutation” than “natural selection,” especially in the empirical literature. Also, many researchers avoided the well-defined, well-understood term “genetic drift” in favor of a new term they themselves coin, usually built around either “random” or “stochastic.” Imagine reading a research article in which the authors never use the word “cell,” but talk instead about “living boxes” (equivalent to calling drift, “random change”) or using the word “phenotype” to mean a DNA sequence (equivalent to conflating mutation with selection). If they otherwise describe and explain everything accurately, we might conclude that the researchers correctly identified a classic, well-known pattern but for some reason did not know what to call it. This is the situation we find in so many studies of cancer biology and treatment. Evolution is so obvious to these researchers that, for whatever reason, they fail to couch their explanations in classical terms, even though they get the explanation right.
Observations like these, and the ubiquity of evolutionary themes in this book, suggest that evolution can serve as a unifying, quantitative theory of oncology, and we are by no means the first to hit on this suggestion. That evolution, and natural selection in particular, underlies malignant transformation and treatment resistance are old, well-established ideas [14, 18, 21]. But the last decade has seen an explosion of interest in evolutionary oncology [2, 3, 4, 7, 8, 12, 15, 16, 17]. These references (and more), and indeed this text, make clear that evolution touches essentially every aspect of oncology— etiology, pathogenesis, tumor progression, morphology, prognosis and, perhaps most importantly, treatment. And the concept of evolution even subsumes the beautiful theory of Hanahan and Weinberg—cancer hallmarks are phenotypes that are caused by evolutionary forces, primarily natural selection and perhaps genetic drift. These traits then alter tumor ecology by changing the environment, both locally (in tissues within and immediately around the tumor—it’s microenvironment) and globally (the host physiology). We suggest, therefore, that cancer theory should explicitly strive to build an evolutionary narrative that connects genetic and genomic alterations with phenotypic traits and their interactions with tumor ecology. We say explicitly because this appears to be the path the field is taking naturally. However, many cancer researchers appear not to realize it, treating evolutionary ecology as a fringe idea instead of the core notion of oncological theory.
Finally, we observe that this theory “narrative” will be written in the language of mathematics. Evolution, by definition, is dynamic. Mathematics, including numerical schemes implemented on computers, provides the most powerful tools ever devised by humans to handle the theories of dynamic processes. Without doubt, evolutionary theory applied to oncology and medicine in general promises to produce not only a coherency to scientific medicine, but also beautiful new mathematics.
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1Note that we call lactase persistence a mutation even though it is considered the normal, healthy state. The state we think of as the “disease”—adult lactose intolerance—is conserved among non-human mammals and therefore probably the ancestral state in humans. Indeed, the majority of humans alive today are “lactose intolerant.”