WHY THE CANCER MOONSHOT PROGRAM WOULD BENEFIT FROM MORE THEORY AND PHYSICS

The cancer moonshot program was supposed to be a game changer in cancer research. But the recommendations (text here) that the advisory panel of experts released earlier this month, filled with well-intended and carefully thought-through proposals, were greeted as a success for its “focus on the shovel ready low hanging fruits”. Does this attitude honor the name of this ambitious cancer program and the spirit that Joe Biden instilled? Low hanging fruits are the ingredients for recipes to cook more of the same, to stay the course.

Breakthroughs, as history of science has taught us, is the child of the marriage between new technologies and new theories. The latter is about thinking very hard about fundamental principles. We have poured hundreds of millions in technology and data collection but have neglected the theory of cancer. Most cancer biologists cannot even fathom the very existence of a theory of cancer because for decades now they have abnegated the power of thinking. Thinking is cost-effective: A few million dollars spent in promoting thinking about fundamental principles of cancer could multiply the value of the 100s of millions of dollars spent on (rather thoughtless) data collection with new technologies.

Theoretical physics, not statistics, not engineering, not computer science, could teach biologists how to think about fundamental principles of something. Some thoughts below.

Biologists sitting on piles of ‘omics results have data but no ideas. Physicists sitting in their office have ideas but no data. Can we combine the two to create a group of scientists who have ideas AND data? Such research groups would benefit cancer research. But this is more challenging than it sounds — but not impossible.

I would like to offer some elementary reasons for why I think cancer biology is in urgent need of an influx of ideas from physics, and in particular, theoretical physics. My claims can only be uttered by a biologist for I will essentially state that current biologists do not “think” –and being an experimental biologist by training will protect me from the suspicion of self-serving bias in this advocacy for theory. (Conversely, it will expose me to the accusation of treason from the physics-bashing bio-blogosphere (here and here)

Deep sequencing has replaced deep thinking in biology

In modern life sciences a deepening dichotomy has developed that splits scientists into two broad epistemic groups: there are people who have ideas but not data (the thinkers and theorists), and there are people with data but no ideas (the vast majority of cancer biologists). I would say, perhaps 90% of researchers actively involved in cancer genome sequencing projects, such as NCI’s TCGA program, belong to the latter group. Deep sequencing has replaced deep thinking. Scientists in these two epistemic groups inhabit almost disjoint spheres of research operation and cultures. It is then obvious that combining these two groups will establish the desired configuration of “having ideas AND data”!

Unfortunately, the surge of well-meant attempts to promote interdisciplinary approaches to cancer, nicely epitomized by NSFs recent PHYSICS & CANCER initiative or NIH’s recent PSOC (Physical Sciences-Oncology Centers), do as much to expose the fundamental incompatibility of these two epistemic cultures as they unite disparate approaches. The challenge we face in achieving a synergism between physicists and cancer biologists lies in a rarely articulated but prevailing asymmetry: while those who have ideas but no data crave for data, those with data but no ideas do not appreciate what they lack: they contempt theories or are even not aware of the very existence of “deep thinking”. They question the very notion that any meaningful knowledge can come from reasoning in the abstract alone. We witness a historical reversal of roles: the biologist’s proverbial “physics envy” has transformed into the arrogance of empiricism which now comes in the extreme form of exclusively data-driven explanation. Here, formal hypotheses and theory take a backseat. Conversely, the physicists’ notorious intellectual arrogance has ceded to the hunger for data. The recognition that now time is ripe to test long-held hypotheses has made them eager to reach across the disciplinary divide.

That biologists “do not think” is an exaggerated statement –made for the argumentation sake. Biologists, of course, do think: they think rigorously about what control experiments to perform to separate out confounding effects, about what sample size is needed to achieve statistical significance, and about what is the best measurement method; they think about how best to analyze their data to find statistically robust patterns, etc. They ‘reason’ that knocking out gene X will prove its postulated critical role in process Y. Thus, all of contemporary biologists’ intellectual activity is invested in menial problems that serve to support the process of observation and to cement the “mechanistic role” of their favorite protein beyond doubt and to achieve publishable results. There is no “deeper” thinking about the existence of principles that would explain why something is the way it is (and not otherwise) and about the generality of such explanations (for a certain class of systems). Rigor has moved from scholarly reasoning to data collection.

Reflection versus reflexes

Thus, I use the term ‘deep thinking’ here, hopefully without sounding condescending, just as an operational shorthand for a type of academic thinking that I accuse experimental biologists of ignoring, suppressing or perhaps, even being incapable of: the reasoning about general, elementary principles and laws that govern biological phenomena and hence explain them, without considering the many distracting and obscuring idiosyncratic details. Such thinking that aims at formulating theories that can predict entire classes of behaviors, not specific instances, does not come natural to biologists. The last major achievement of such thinking in the life sciences was in macro-biology, most prominently epitomized by Darwin’s theory of evolution, followed but population genetics that led to the Modern Synthesis. At the level of micro-biology, which deals with molecules and cells within one organism, Conrad Waddington was one of the leaders in the attempt to move beyond description and to formulate general principles. And here is a little irony: The physicists who launched the molecular biology revolution were still open to general principles: Max Delbruck mathematically formulated the concept of attractor states in cells in 1948. But alas –the tender buds of such efforts were brutally crushed by the arrival of molecular biology that physicists brought to biology. Molecular biology brought us a different type of explanation — a huge success for science, certainly, but at another front of advance in understanding life that many had hoped for. Reflection (“What are the fundamental principles behind the universal tendency of cancer to progress?”) was replaced by reflexes (“There must be an oncogene to explain this malignant trait!).

felix qui potuit rerum cognescere causas

In contrast to the quest for general principles and laws that represent the rerum causas, molecular biology has evolved its own epistemic habits with an idiosyncratic scheme of explanation that departs from that of all sciences, not only the natural but also the social sciences, by lacking any formal theory –not even a desire to develop one. I think, this is quite unique. The sole explanatory principle that makes molecular biologists happy are “molecular pathways”, the embodiment of causation, that they celebrate as “mechanistic understanding” — their rerum causae. N. Tinbergen and E. Mayer called this kind of explanation of a phenotype, ‘proximate’ causation, contrasting it to the ‘ultimate’ causation that applies to entire classes and in physiology is best represented by the Darwinian principle of selective advantage –a general principle. Proximate explanations, or their equivalents in molecular biology, are embodied by a molecular mechanism, the “molecular specificity” which elates biologists (“Wow! — Wnt signaling is involved in cancer drug resistance”). The biological infatuation with the concept of ‘specificity’ of a causal mechanism is almost unknown in physics and directly opposed to the theoretical physicists’ emphasis on the generic, if not the universal. I would contend that knowledge of a molecular mechanism, however concrete and specific, does not constitute understanding but is merely a description of an observation at a lower level. (Granted, this may have utility for drug development — see below). The Lucretian school’s notion of ‘felix qui potuit rerum cognescere causas’ is thus relative.

For those physicists not familiar with the operation of the mind of a broad class of contemporary “non-thinking” biologists, let me illustrate this in the following way:

Let’s assume we are all scientists from an automobile-free planet, arriving on planet Earth on an expedition. Enthralled by the sight of the moving cars, the biologists among us would experiment with them and soon find out that the deeper you press the gas pedal, the faster the car moves, and proudly announce the causal relationship that explains why cars move. The physicists in the expedition would consider this a mechanistic detail and prefer to understand the thermodynamics: why is it possible at all that a vehicle moves forward, without apparent external help, and that given some conditions (fuel tank+gas pedal engaged+…) it has to move, but also that fuel efficiency has a theoretical limit? Not understanding all the parts that they see when opening the hood, the physicist would opt to ignore them and instead develop a theory of the kind of the Carnot cycle — which offers the ultimate explanation for why it is possible that cars are auto-mobiles (to a well-defined extent). The biologists would then respond: That is not useful because it does not tell me what I need to do to make this car drive.

The rise of proximate explanations and of molecular concretism

Why do current biologists espouse observation and description of mechanistic causes but eschew “deep thinking” about principles? This has of course not always been so — just read any famed or not so famed biologist’s work of the pre-molecular biology era when reasoning was not relegated to the discussion section of experimental papers. Over the past decades, with the success of molecular biology, life sciences have, through education, training and self-selection of its members, thrown out the culture of thinking. The unfathomably powerful techniques of molecular cloning, which has given us a new looking glass to see the molecular events underlying biological processes, has not only obviated the need for abstraction (because now actually you see concretely what explains your observation) –but has also led to a complacency in reasoning about principles as ultimate causes. For instance, hardly a molecular cancer biologist would ask what is behind all those common properties of cancer, such as the inexorable development of drug resistance, no matter in what type of cancer and to what type of treatment — a set of universal features which I find quite stunning. Instead, they prefer to emphasize how every tumor type, even every tumor, is different. Some even suggest that cancer is not a class of disease but consist of many diseases. This relieves them from the duty of identifying common, more abstract principles.

We cannot stay the course

But can understanding general principles also be useful? Take the examples of the internal combustion engine. Carnot’s thermodynamic principles, albeit at a high level, tells us that there is a theoretical limit for fuel efficiency. Despite formidable success over the past decades, we cannot keep pushing up fuel efficiency of combustion engines. We realized that we cannot stay the course but needed to look outside the box -which led to electrical cars. Cancer biologists are unaware that there could be (and likely is) a limit to the therapeutic benefit of hitting cancer harder and harder with more “precise” drugs. They cannot fathom fundamental principles, such as perhaps cellular entropy, evolutionary dynamics, resilience, etc. that may set a limit to our efforts to selectively kill a tissue gone rogue that has coopted the fundamental principles that makes life possible in the first place, without also killing its very similar sister tissue that has subjugated these principles and established stable cell societies for the common good: to endow the biosphere with healthy replicating macro-organisms.

The comfort of taking refuge in simple, proximate molecular explanations eventually evolved into the active disdain for the quest for ultimate explanations that will involve “deep thinking” and possibly a formal theory. At the height of the success of molecular mechanism in the 1990 (before genomics took center stage) you had to check ‘deep thinking’ at the door before entering wet labs. Empiricism reigned again, its dictatorship powered by the irresistible techniques of molecular cloning. Physics envy was gone. I remember when the journal CELL in its early days, and still in celebration of the revolution of molecular cloning, would not accept manuscripts with equations in it. Who can blame their editors when the vanishing of a black band on an electrophoresis gel provided the irrefutable molecular explanation of an observation. Spoiled by this type of concrete causation epitomized by macromolecules, and embraced by all journal editors, the discipline for rigorous, abstract and formal thinking in biology has become vestigial.

In cancer biology we see a particular ascendance of molecular concretism because it satisfies our natural longing for an immediate explanation of the dreadful facts of life. The identification of as tangible a culprit of cancer as an oncogene has made the search for “deeper” explanations unnecessary. Instead, a proximate molecular explanation comes with the added bonus of offering a concrete target onto which we can more easily project the hope for a therapeutic intervention. Cancer researcher indeed still chase for mutations to explain (and target) each of the “hallmarks of cancer”, the sole innovation being to take down every single “hallmark” with more precision drugs, given in combination. But the near-universally disappointing long-term success rate of target-selective precision therapy defies the mechanistic rationale behind such therapy design, and glaringly exposes a certain deficit in biological thinking or, rather non-thinking. The arrival of omics technologies has pushed biologists further into the province of “having data (-lots of it) and no ideas” — the last straw that killed thinking. Empiricism becomes “discovery science”, and the art of erecting formal hypotheses (not ad hoc “bets” formulated as hypotheses to trick the funding agencies) is now lost.

We don’t need more mathematized phenomenology. We need new theory.

Theoretical physics is the most suited among the “quantitative sciences” to come to rescue and to correct this current intellectual deficit in cancer biology. Yet it is perhaps the least welcomed by biologists among the physical sciences. By contrast, biophysicists (sensu strictiore), computer scientists, engineers, mathematicians are welcome by biologists –because they provide much needed help with instrumentation, measurements and data analysis. These quantitative disciplines have become subservient to molecular concretism: they serve to place the biologists’ hand-waving type of explanation into a quantitative framework but offer no really new perspective from a more encompassing category of thought. Such quantification of proximate causation is necessary but not sufficient. Attaching numbers and some just-so mathematical models to observations does not extend a mechanistic description into the realm of fundamental theoretical principles. A detailed description of the functional form of how the gas pedal depression relates to the acceleration of the car is still just an ad hoc, proximate explanation without general validity. Such models will be outdated with the arrival of self-driving cars — while the physics still holds. It is mathematized phenomenology, not theory.

But this is precisely the type of quantitative sciences that NCI is now promoting. In its well-meant attempt to be comprehensive it lumps data engineers and tissue engineers in the same basket as theorists. Not all “dry-lab scientists”, as the experimental (“wet-lab”) biologists call them, are scholars in pursuit of pure understanding. (And of course there is still a minority of solid experimentalists who eschew high-throughput data collection and espouse careful, hypothesis-driven experimentation). Thus, it is not only for the quantitative modeling of our observations that we cancer biologists need the help of physicists. Instead, a close collaboration aimed at developing a theory of cancer is what we should seek. Only a theory will pave the way to the equivalent of the electric car –the concept outside-the-box of squeezing out the last theoretically possible increase in gas mileage of internal combustion engines through clever engineering hacks here and there –an attitude embodied by “precision oncology”. The habitual celebration of just a few months of life extension for cancer patients achieved by a new drug reflects our commitment to stay the course and to double-down on existing approaches and our obliviousness of anything beyond. But to achieve the equivalent of the electric car instead of tweaking the combustion engine, in cancer treatment we need to understand the fundamental principles of how drugs kill tumors –not just the “molecular mechanisms” that many journal editors are obsessed with and mistake for ultimate understanding. The only thing that can pave a path for a radical departure from the existing path forward, yet is still grounded in rigorous scientific principles, is to have a theory. A theory is the outline for a map of uncharted territory.

More theory, not more tweaking is needed

We biologists do not master the art of erecting a testable theory anymore. It is because we have lost such scholarly facility that we should welcome physicists who are at home in this domain of intellectual pursuit. While it is clear that knowing a causative molecular pathway is more useful than knowing what is the deeper reason for a universal behavior of cancer cells, much as knowing how to operate the gas pedal is more useful than understanding the Otto cycle of combustion engines, the utility of understanding fundamental principle in cancer should not even be a question. The unconditional, genuine curiosity-driven quest for understanding nature is part of the imperative of science, and harnessed by formal theory such natural intellectual urge will help us navigate unexplored lands without losing scientific rigor. It must complement the current narrow pragmatism in cancer research that has as its sole guide an imagined, wished-for destination on a dreamed-up map. Thus, there is much in terms of research culture that cancer biologists can learn from theoretical physicists. I found it utterly sad when a leading cancer biologist proudly indicated that they are driven by the (noble) desire to cure patients but have no curiosity about the underlying biology. This is the recipe for staying the course. If we are to do everything we can using science to help cancer patents, then we also should do everything we can to do good science. Despite the best of intentions for cancer patients, the Blue Ribbon Panel, which advises the President’s Cancer Moonshot Task Force, appears to be not interested in advancing the science of cancer as its first list of recommendations has abundantly made clear. It excelled in designing the optimal path forward on the same course. It lacked the imagination to look beyond doubling down on staying the course.

The deficits in the “culture of thinking” in cancer biology presented here can best be corrected by some infusion of theoretical physics. Thoughtful theorists would not only provide the specific knowledge for unraveling the fundamentals of the phenomenon of cancer but more urgently, would import their epistemic culture to experimental biology. But there is a danger: that the purist culture gets lost and instead a theoretical physicist acquires the local customs of the new land she has immigrated to. Many a colleague of mine who I thought were typical cancer biologists turned out to have been theoretical physicists in their early life. In entering the space of empirical cancer biology, some physicists may also have checked their “deep thinking” at the door and over-adapt to the culture of formulating proximate, easily fundable hypotheses. Such assimilation may be due to self-selection of those physicists who prefer data-driven hand-waving and eschew reasoning about fundamental principles and who therefore have switched to biology. Yet we must now hope that there exist theoretical physicists who will enter cancer biology with the conscious and resolute intention to bring their way of thinking to cancer research. They won’t cost much and they will enrich cancer biology by occupying a still available, but hidden niche and become the new breed of cancer researchers who will one day harvest the (high hanging) fruits fostered by having both ideas and data.

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This is a revised version of a post in response to NSFs Physics and Cancer blog in 2013.