I am entering my 3rd year of a PhD at MIT/Harvard Medical School, and after finishing classes and doing full time research for some time now, it is now time for an assessment of how the cancer biology field operates and some thoughts on how PhDs work in cancer bio.
To put it bluntly, cancer research is a few pioneers swimming in a sea of bullshit. Every month there are some interesting papers, but a cynical insider could point out that despite record funding year after year, the majority of scientific output consists of the same boring characterization studies with little novelty.
But this post isn’t a rant about the sad state of cancer research and in fact the point I am trying to make is that this environment paradoxically makes it the perfect place to do a PhD.
To start, I’ll describe the types of projects that are commonly given to early stage graduate students.
The big goals in cancer research are the following:
These three areas are closely intertwined and many labs work on aspects of all three. These three goals are often what papers come back and finish with, yet can be far removed from what is achievable in a PhD.
A more realistic view for how to think about projects comes from the ‘style’ of the lab you join. These styles are dependent on the types of work that get produced and have variable timelines, potential for collaboration, and intensity of workload.
Primary categories of academic output come in the following:
Profiling papers: this is where groups will do a lot of single cell or spatial profiling on patient samples, typically leveraging clinical sample acquisition expertise. These types of projects are done by labs with a lot of research funding or relationships with industry, as they have long timelines and are expensive to execute. These projects don’t require a lot of thinking and in my experience, don’t actually discover much new information. However, they are valuable to the field at large in that they provide data for researchers with hypotheses to download and check if what they believe to be true is actually true. For example, an easy way of verifying expression of a set of genes in a certain cell type would be to query a single cell atlas instead of generating that data yourself. Students that undertake profiling projects have the certainty of knowing that the resulting paper will be high impact without needing a specific hypothesis to play out. However, the threat of competition and limited ability to think critically and be responsible for asking questions can lead to a stressful PhD experience without much scientific development.
Mouse modeling papers: genetically engineered mouse models are generated to study the impact of a specific gene in great depth. Mouse models are often generated to study and characterize the function of genes with a known role in disease (e.g. commonly mutated genes, highly differentially expressed genes, and genes where there is substantial other preliminary data). Not all labs do mouse work, as maintaining a robust colony is expensive. However, as certain labs become known for the study of specific genes or pathways, they begin to accumulate or generate the appropriate mice. You can derive cell lines/organoids from these mice, using these for mechanistic work. If you do a drug study, you can characterize the microenvironment, do spatial/single cell, and get survival/drug sensitivity data in pretty short order. The mice take a while to generate but if you are able to walk into a situation where they are already there, the path to project completion can be straightforward.
Applying X to Y: this class of papers commonly arises as a hypothesis generating exercise, and usually by groups that focus on a particular biological phenomena or technology. For example, groups that study metabolism can find an application in almost anything, ranging from therapeutic resistance, to metastasis, or cellular state/function. These projects offer an open slate to explore and ask questions, perfect for a PhD student that is not afraid of building from first principles. The downside is that you could spend a lot of time forcing a connection that might not be there or that might not be that significant.
Characterization papers: these papers describe the effects of a specific drug in the preclinical or even clinical setting. These are typically industry sponsored studies where you can perform comprehensive characterization of drug effects on any aspect of tumor development or progression. These studies are very hypothesis generating and can be used to find mechanisms of drug resistance and/or mechanisms of efficacy. Opportunities to do this are hard to come by and can be competitive, but are almost always high impact as these drugs are going into patients. It would be rare for a graduate student to lead such a study independently, as these require abundant resources and a thorough experimental load.
Hypothesis testing: I think these are the most beautiful types of papers, essentially where you have a phenotype and you figure out why and how the phenotype arises. These don’t require any collaborations or even extensive resources, just astute observation and well designed experiments to turn theory into fact. I think these are the ideal projects for grad students. Hypothesis testing projects teach you how to gain independence and come with the sweet satisfaction of solving a real problem that can provide the motivation for future scientific training. You need some degree of savvy to understand what phenotypes are actually real versus artifactual, as well as the experimental diligence to work through periods of uninterpretable results. However, they provide the ideal open ended discovery problem to grow as a scientist.
Picking and executing on projects is only one part of the PhD. While it is arguably the most important part, unfortunately a lot of your time is spent worrying about other extraneous metrics of success like publications, conference presentations, and various awards. These aspects drive the negative parts about doing a PhD in cancer biology, more than they would in other fields for reasons I will explain.
As I wrote about previously, cancer biology research is overfunded, and paradoxically this leads to an overabundance of mediocre studies. Alongside competition, the rate of publication has increased. Additionally, there are more and more conferences, invited reviews, presentation opportunities, etc., and to fulfill these opportunities, there is a pressure to churn out work that looks productive but doesn’t necessarily address critical questions. I myself am guilty of this, but review and perspective articles are perfect examples. This ‘work’ gets published in high impact journals but is so boring that it can be automated by AI.
A more pernicious flavor of the outpouring of mediocrity is the ‘willful ignorance’ category of papers. This is the phenomenon of people taking already known information and selling it as brand new; or, fitting data to narratives that are already known. There is a tendency to regurgitate dogma by way of using weird normalization techniques or excessive use of GSEA, so that you not only come to conclusions that are ‘safe’ and thus less likely to receive reviewer criticism, but also something that others will want to cite as part of a ‘broader set of evidence’. When people start talking in generalities (e.g. EMT, immune evasion, immunosuppressive macrophages, etc), people stop studying the individual genes driving phenotypes. And when you think at a systems level instead of mechanistically, you more further away from identifying better biomarkers or therapeutic targets, which is why we all do this in the first place. The tendency to revert back to established information or themes like ‘heterogeneity’ does not push the field forward.
Transparency is going down the drain. Experiments are becoming more technically difficult and expensive, making direct experimental replication often a non-starter. As a result, conclusions from papers are essentially just taken at face value and if your goal was to publish quickly, you can just say your data is good enough and not explicitly mention limitations or things that went wrong with an experiment. Or you use clever language to hide your limitations if a reviewer makes you do it. Of course this doesn’t work if you want to publish truly groundbreaking work, but as I mentioned, many people are just treading water so simply publishing and moving on is good enough to sustain funding and an academic career.
Finally, there is an abundance of “me too” science where if you have money or access to samples or certain collaborations, you will be able to win. I see the majority of cancer research as a pay to play type of ecosystem where you don’t necessarily need to have novel ideas in order to make an impact. Whether this is good or bad is sort of a philosophical question. On one hand, its great that there are obvious studies to do that push the field forward and don’t require a stroke of genius from any individual researcher. On the other, the ease of taking this path of hitting singles and doubles could divert the attention of people trying to hit home runs.
The four downsides I wrote about are double edged, in that the arena of overfunded mediocrity, low transparency, and low originality does provide a terrific training ground for an astute graduate student.
First, mediocrity teaches you to discriminate between good vs bad quality work. We are living in a world where the motivated individual can find evidence for anything; essentially any statement can be made and supported. For example, if you type in any gene into PubMed, you can find some link to cancer, and for any random gene, you might find evidence of it being an oncogene in some contexts or a tumor suppressor in others. Remember that ChatGPT or whatever new language model people are using is training on this entire corpus of data, no matter if the work is good or bad. We live in the information age where curation of data or new information is far more important than the quantity of ideas. AI is simultaneously less creative and has worse intuition than a seasoned scientist. Wading through the ‘sea of bullshit’ provides a direct path towards developing intuition. There are certain parts of life where more information can unexpectedly lead to worse decisions, and science can be one of those places. As a grad student, you will inevitably hear a talk that really strings together critical observations and leads to a compelling idea with high likelihood of patient impact. Learning how to do this yourself distinguishes you as someone capable of productive independent thought, from others who are only capable of spewing redundancy from the latest GPT. How to develop the ‘style’ or ‘taste’ of a productive scientist comes directly from experience. You need to be able to trust but verify and that is what a cancer biology PhD gives you.
Secondly, the research in cancer biology is ultimately goal based and is thus inherently cross-disciplinary, providing students with a broad base of technical expertise. There are many places to borrow knowledge from. For example, many pathways from development or wound healing are relevant to cancer and concepts can be directly applied. To study KRAS resistance in pancreas cancer, you can make analogies from studying BRAF inhibition in melanoma, as it’s the same MAPK pathway. By studying one type of cancer, you can develop an intuition for other areas of biology. Additionally, biology provides a playground for exploring the relative strengths and limitations of using certain technologies or techniques to answer questions. Is scRNAseq really much better than 4-color immunofluorescence? A PhD in cancer biology will teach you when it is and when it isn’t. Beyond the silly technical point, the broader lesson is in how to evaluate new and shiny things at face value and deriving from first principles what new opportunities can provide for you.
Finally, developing treatments for disease is arguably the most difficult task that humans have been able to succeed at. Cancer is still not cured and this creates a big hairy audacious goal for students to think about without the goalposts shifting too quickly. This provides space for students to think hard about problem selection without having to worry about getting scooped in the near term. Your time is limited and problem selection is the most high leverage way of making the most of your time. Pick a PhD field where you have the flexibility to think about problem selection.
Ultimately, science will move forward without you, no matter what field you choose. The fulfilling parts are developing your personal sense of scientific style and taste, while identifying the qualities of people you want to work with in the future.
Cancer biology does a good job at addressing these criteria, offering enough complexity to be interesting, enough mediocrity to develop taste, and enough people to find friends.