A device for seeing cancer better
I had left medicine for technology development with one question: could we build something like an MRI scanner that maps cancer cells with enough molecular detail to tell the clones apart, and use it to choose treatment?
When I started my postdoc in 2006, next-generation sequencing and molecular barcoding looked like the answer to everything. Capacity seemed unlimited and the implementation easy. It was irresistible.
My first projects were on human iPS cells, which arrived in late 2007 with a simple promise: turn skin cells into stem cells, then into whatever cell type you need. Differentiation in a dish was noisy, and neighboring cells could be strikingly different. Expression-profiling methods averaged everything into one profile, smearing together cells each setting off down their own path.
But the cells weren’t random. They grew into embryoid bodies that partly mimic an early embryo organizing axes in space. Our measurement threw that space away. To the engineer in me that looked like an opportunity: single-cell, spatially defined measurement, in 3D, across development.
Biggest bang for the buck
What I could do was stain cells. My first proposal was the obvious one: label antibodies against proteins that mark developmental states, cell signaling and the reprogramming factors, and read them out over rounds of sequential hybridization. Proteins were where the biology was.
Then the antibody order arrived. Conjugating DNA to each antibody was slow and fiddly, the results were uneven, and every antibody had to be titrated on its own. Forty was hard. Four hundred was unthinkable. The antibodies had biology on their side. They didn’t have scale.
I switched to multiplexed FISH. DNA oligos were cheap per probe and scaled with oligo arrays and PCR. Quietly, my goal shifted from profiling stem cells in place to exploiting cheap, massive multiplexing. But every redesign of a 1,000- to 20,000-oligo array cost thousands of dollars, and single-molecule FISH needed its own optimization.
I changed tack once more and decided to sequence the RNA directly, inside the cell — not for any deep scientific reason, but because the whole thing could be primed with a single random hexamer, a reagent that cost several dollars instead of tens of thousands.
Did it work?
Three years later, it worked. We converted RNA to cDNA inside fixed cells, amplified each copy into a bright spot, sequenced the spots in place with commercial sequencing chemistry, imaged them over many cycles, aligned the images and decoded the Morse code of each spot. That became FISSEQ [1].
At each fork, I picked the experimental approach that fit a postdoc’s timeline and a lab’s budget, not necessarily the one most likely to lead to biological insight. The results were still proof of concept: exciting, “transformative” academic claims, rather than the boring kind of result you could take to a patient today.
I don’t think I was that unusual. Grants, papers and postdoc clocks all reward novelty, and novelty is cheapest where multiplexing is cheapest. We measured what was cheap to measure, then built stories around it.
Back to the beginning
Sydney Brenner said that progress in science comes from new techniques, new discoveries and new ideas, probably in that order. It is also true that the techniques you get are the ones you can afford. Today, I’ve gone back to where I started: protein markers of cell type and the processes that keep cells running and responsive to treatment.
What changed isn’t the biology. Proteins always had it on their side. What changed is the cost. Antibody panels are more common, recombinant production makes them reproducible, and designing new binders from scratch is becoming routine rather than heroic.
Boring is OK
Looking back over two decades, I’ve made my peace with an unfashionable conclusion: boring is OK. Well-validated markers. The same assay, run the same way, at different sites. Results cheap enough to repeat on thousands of patients instead of a beautiful dozen. None of it makes a splashy figure. All of it scales. And scale is what medicine needs next. Care that learns from every patient only works if the measurements are boring enough to run on all of them.
I still want my clinical scanner for cancer cells. I just think the road there is paved with boring.
Sources
- Lee JH, et al. Highly multiplexed subcellular RNA sequencing in situ. Science 343, 1360–1363 (2014).