# Misleading models in mathematical oncology

March 5, 2014 10 Comments

I have an awkward relationship with mathematical oncology, mostly because oncology has an awkward relationship with math. Although I was vaguely familiar that evolutionary game theory (EGT) could be used in cancer research, mostly through Axelrod et al. (2006), I never planned to work on cancer. I wasn’t eager to enter the field because I couldn’t see how heuristic models could be of use in medicine; I thought only insilications could be useful, but EGT was not at a level of sophistication where it could build predictive models. I worried that selling non-predictive models as advice for treatment would only cause harm. However, the internet being the place it is, I ended up running into David Basanta — one of the major advocates of EGT in oncology — and Jacob Scott on twitter. After looking through some of the literature, I realized that most of experimental cancer research was more piecemeal than I expected and theory was based mostly on ad-hoc mental models. This convinced me that there is room for clear mathematical (and maybe computational) reasoning to help formalize and explore these mental models. Now we have a paper applying the Ohtsuki-Nowak transform to studying edge effects in the go-grow game prepped (Kaznatcheev, Scott, & Basanta, 2013), and David and I have a project on chronic myeloid leukemia in the works. The first is a heuristic model building on top of previously developed tools (from my experience, it is rather uncommon to build directly on others’ work in evolutionary game theory and mathematical oncology) and the other an *abductive* model using a combination of analytic and machine learning techniques to produce a predictive tool useful in the clinic.

Two weeks ago, I was excited to read Philip Gerlee’s post bemoaning that mathematical oncology “still lacked that defining publication where the use of mathematical modelling was clearly tied to a clinical change benefiting patients. Or in other words, an instance where mathematical oncology has been proven to make a difference”. Unlike me, Philip has training and extensive experience with mathematical oncology, and it was reassuring to know that he noticed a similar focus on heuristic models. His observation that the prevalence of networks and intra-tumoral heterogeneity as ideas in cancer research owed their origin to mathematical models was a comfort; we aren’t complete omphaloskeptics, some of our ideas are having a direct effect on the experimentalists and practitioners. Finally, this means that there is a goal to aim for: build a predictive model that is useful in the clinic. Lofty, but relatively clear.

As I was preparing to write a reply to Philip’s post, I returned to it to find that Heiko Enderling suggested Michor et al. (2005) as a counter-example. The paper looked at the dynamics of chronic myeloid leukaemia, fit a system of ODEs to patient data, and argued that *imatinib* does not deplete leukaemic stem cells. This was a double surprise for me. First, the paper was on CML and from Nowak’s group. Nowak is probably the most frequently cited research on TheEGG, how did I not come across this in my literature review during the IMO workshop? I guess I really shouldn’t be surprised at holes in my litt reviews anymore, they are far too common. Second, is the venue — *Nature* is not known for mathematical papers, in fact if you look at how they handle theoretical computer science or the story of /u/spgarbet on reddit you might even say Nature Publishing Group is anti-math:

Our lab submitted a paper to Nature on cancer. One comment back from a reviewer, “You used a math formula. The nuances of math may be lost on Nature’s audience.” !!!

The paper was on implications of variance in an exponential growth model and why this is important in cancer progression.

Hence, you can imagine that my reading was a mix of excitement, worry, and skepticism. In the end, I have to disagree with Heiko and Philip, I don’t think mathematical oncology made any direct clinical changes, in fact, I would go so far as saying that the mathematics was completely irrelevant to this paper, at best it was a just-so-story with no predictive power.

A nice feature of Michor et al. (2005) was that it incorporated a careful analysis of experimental and clinical evidence, something I don’t often see in the evolutionary game theory literature at least, where the connections are largely analogical or qualitative. They saw empirically that patients given *imatinib* fell into two broad groups: those for whom BCR-ABL levels in the peripheral blood dropped to very low levels (remission), and those for whom they decreased but the returned. They concluded — without mathematics — the the latter developed resistance through mutation. At this point, we are not getting much beyond the obvious, I guess it is conceivable that there could have been two other groups: ones for which BCR-ABL levels increased or stayed level after treatment, however, since the drug had passed FDR testing by that point, it seems like doctors would already know how to check for these cases before trying *imatinib* (or after a very short time) and thus such cases would not be present in the sample.

Among the patients whose BCR-ABL levels dropped to very low levels, Michor et al. (2005) note two further empirical observations. First, Bhatia et al., (2003; see also Ross et al., 2010) conducted bone-marrow biopsies in some patients and detected high levels of cancerous stem-cells even after complete BCR-ABL remission in the peripheral blood. This supports the current (and the 2005) standard of care, which is to continue treatment indefinitely; this is one of the things David and I want to address in our work. However, some patients still stopped taking *imatinib* after achieving low levels of BCR-ABL in trials or due to adverse side-effects, leading to the second observation: the patients quickly relapsed to high levels of BCR-ABL in the peripheral blood (Cortes et al., 2004; Higashi et al., 2004). The obvious conclusion to draw based on this limited empirical evidence is that *imatinib* stops cancer cells in the peripheral blood, but does not destroy cancerous stem-cells in the bone-marrow. Notice that no math was required.

The first hint of math comes when we start to look at the dynamics of the level of BCR-ABL in patients that achieved remission. When plotted on a log-scale, the BCR-ABL levels appear as an elbow graph. Declining with a steep slope at first, and then at an “elbow” switching to a more gradual slope. Although this does start to use mathematics, it is hardly mathematical modeling, but it does suggest that if you were to try to build a mathematical model of this relying on exponential decay, you would need at least two compartments with one some cross-talk between them (like one feeding into the next).

Michor et al. (2005) follow this insight (well beyond where they need to) by mathematizing a four-compartment model with stem cells, progenitors, differentiated cells, and terminally differentiated cells inspired by mouse models (Spangrude et al., 1988). That is four differential equations per cell type, and one cell type for normal cells, one for cancer cells, and one for resistant cancer cells. The cancer stem cell ODE is coupled to the resistant cancel cell with a mutation flow from the former to the latter based on a parameter *u*. It is not clear if the normal stem cell ODE is coupled to the other stem cell types (cancer and cancer resistant) or not, but since they leave a whole ‘homeostasis function’ unspecified in both the text and SI. No other couplings are present, and everything else is either exponential growth or decay. Kind of like the model /u/spgarbet had rejected from Nature; maybe this is why any equations are restricted to an insufficiently specific set at the end of the methods section and the SI.

Overall, this results in a model with 16 to 25 parameters plus an unspecified researcher degree of freedom in the ‘homeostasis function’ (although if it does not introduce coupling between the cell types, it is more or less irrelevant). The difference between 16 or 25 depends on if the patient became resistant to imatinib or not, note that this is only known after-the-fact, before seeing an increase in PCR-ABL values while on imatinib, the Michor et al. (2005) model has no way of predicting resistance it. The model is fit to individual patient data and some parameters that are drawn either from the clinical data or hand-picked to make the results nice; for comparison, a typical patient in their data set (judging from figure 1) has approximately 7 data points of PCR-ABL measurements over a 12 month period. In other words, about half the parameters are completely free.

As von Neumann’s famous saying goes “with four parameters I can fit an elephant, and with five I can make him wiggle his trunk.” The same thing appears to be happening here. We have our pre-modeling purely empirical belief (1) “that long-term imatinib treatment does not deplete the cell population that drives this disease”, and (2) that imatinib treatment cannot be stopped without relapse. A model with many free parameters is built to achieve this effect, and then a few more parameters and 4 differential equations are added if we want to wiggle the tail that is *imatinib* resistance.

For me, this is not convincing procedure, but more of a cargo-cult of mathematics — adding equations without using them to actually guide our understanding and conclusions. For mathematical oncologists, it means that there is still work to be done in writing that defining publication Philip is asking for. More importantly, for patients with CML, we have empirical evidence (Mahon et al., 2010; Ross et al., 2010) to tell us that at least the second pre-modeling belief is probably not true, and we can hope to discontinue *imatinib* in at least some patients without relapse. The task remains to predict, hopefully with the aid of mathematical oncology, in which patients this is safe possibility.

*Header image is an adaptation of the header from Warburg’s Lens blog of pre-prints in mathematical oncology.*

### References

Axelrod, R., Axelrod, D. E., & Pienta, K. J. (2006). Evolution of cooperation among tumor cells. *Proceedings of the National Academy of Sciences*, 103(36): 13474-13479.

Bhatia, R., Holtz, M., Niu, N., Gray, R., Snyder, D. S., Sawyers, C. L., … & Forman, S. J. (2003). Persistence of malignant hematopoietic progenitors in chronic myelogenous leukemia patients in complete cytogenetic remission following imatinib mesylate treatment. *Blood*, 101(12): 4701-4707.

Cortes, J., O’Brien, S., & Kantarjian, H. (2004). Discontinuation of imatinib therapy after achieving a molecular response. *Blood*, 104(7): 2204-2205.

Higashi, T., Tsukada, J., Kato, C., Iwashige, A., Mizobe, T., Machida, S., … & Tanaka, Y. (2004). Imatinib mesylate‐sensitive blast crisis immediately after discontinuation of imatinib mesylate therapy in chronic myelogenous leukemia: Report of two cases. *American Journal of Hematology*, 76(3): 275-278.

Kaznatcheev, A., Scott, J.G., & Basanta, D. (2013). Edge effects in game theoretic dynamics of spatially structured tumours. arXiv: 1307.6914v2.

Mahon, F. X., Réa, D., Guilhot, J., Guilhot, F., Huguet, F., Nicolini, F., … & Rousselot, P. (2010). Discontinuation of imatinib in patients with chronic myeloid leukaemia who have maintained complete molecular remission for at least 2 years: the prospective, multicentre Stop Imatinib (STIM) trial. *The Lancet Oncology*, 11(11), 1029-1035.

Michor, F., Hughes, T., Iwasa, Y., Branford, S., Shah, N., Sawyers, C., & Nowak, M.A. (2005). Dynamics of chronic myeloid leukaemia Nature, 435 (7046), 1267-1270 DOI: 10.1038/nature03669

Ross, D. M., Branford, S., Seymour, J. F., Schwarer, A. P., Arthur, C., Bartley, P. A., … & Hughes, T. P. (2010). Patients with chronic myeloid leukemia who maintain a complete molecular response after stopping imatinib treatment have evidence of persistent leukemia by DNA PCR. *Leukemia*, 24(10): 1719-1724.

Spangrude, G. J., Heimfeld, S., & Weissman, I. L. (1988). Purification and characterization of mouse hematopoietic stem cells. *Science*, 241(4861): 58-62.

Don’t know what to say Artem. I am hoping that you won’t be disheartened by this paper. It’s true that we still have way to come. The positive part is that there is a lot more willingness from biologists and medical doctors to consider mathematical models. But still, many of them are still somewhat reluctant to learn much about the models. It’s tempting for some biologists to think of mathematical models as some sort of formal way to describe what they already know instead of taking advantage of the hypotheses generation possibilities.

I am not necessarily disheartened by a lack of a definitive paper. I think I largely agree with Jacob’s comment on Philip’s post; the role of mathematical oncology must be increminental and there is nothing wrong with that. I expect that instead of a definitive paper there will be at some point a definitive textbook that will help distill the essence of mathematical oncology and introduce cancer as a problem domain for more mathematicians, and mathematical tools as a way toward insight for clinicians.

I don’t think this paper is using math to describe something they already know formally. I would actually be fine if mathematics was used to systematically describe and classify what is already known in biology. In fact, I think this is precisely the thing that cstheory can offer biology. This paper is just making an ad-hoc mathematical facade, or as you very accurately call it: a decorative mathematical model. To me, it seems that the intent is neither to formally codify the prevailing knowledge (and alternative hypotheses)

norto generate new hypotheses.I am always one for promoting hypothesis generation as a goal for models. However, I think that I am also starting to change my mind on using machine learning for prediction in this context. Of course, we can’t approach the problem with complete blind data (of the sort I ridiculed before), but instead some sort of ‘myoptic data’: specify a reasonable-ish mechanistic hypotheses class (as we do with our models of CML) but then don’t assume that we know what the terms of our model mean in the ‘real world’ and just fit them with standard ML terminology (which doesn’t depart from this 2005 paper) but with the direct and

immediate goalof making clinical predictions (whichdoesdepart from the 2005 paper).Of course, this sort of prediction will not be grounded in theory, but it is not like we have a sufficiently well established theory to even hope for grounding predictions. In the long term, such an approach will stall, but in the short term it can build respect for mathematical oncology as a directly useful field and try to bridge the language gap between experiment and mathematical theory, Once some of these languages barriers are broken down, I think it will be easier to convince people that it is worthwhile to use mechanistic models to build new hypotheses, or to carefully codify existing knowledge.

Reblogged this on CancerEvo and commented:

Artem writes about what I could describe as a ‘decorative mathematical model’. A decorative model is what you find in certain biological journals where the mathematical model is not meant to drive the biological experiments nor to derive a new understanding of the biological data. I am not sure that the paper he describes fall in this category (I have not read the paper in detail) but his observations are useful to any mathematical biologist: a complicated mathematical model with lots of parameters produced after the experiments have been performed is unlikely to be too useful.

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