PCP addict

No — I’m not talking about phencyclidine or angel dust but instead PCP as an abbreviation for three words: phenomenon, curiosity and paradox.

My 1973 edition of Webster’s New Collegiate Dictionary defines a phenomenon as “a rare or significant fact or event,” a curiosity as “one that arouses interest especially for uncommon or exotic characteristics,” and a paradox as “a tenet contrary to received opinion.” I’m always on the lookout for any PCP worthy of study. Once I find a good one, I see the opportunity to make a discovery.

Before discussing ways of finding PCPs, let’s first question the value of this strategy.

With respect to practicality (careerism), this approach is a bad idea. Committing to a project that is unusual, exotic or contrary to opinion is not easy. Granting agencies tend to choke on ideas that are new, different or a challenge to conventional wisdom. They want us to add incrementally to the existing knowledge base; they want to know that what we propose in our grant applications will work. Nothing I’ve ever known for sure will work and proceeded to do has added anything of significance. If a project is perceived as likely to succeed, building on what already is known and accepted, it is far more digestible to most review committees than a project seeking to challenge dogma or break new ground.

Were it up to me — and as I have admitted over and over, it is not — I would never fund a research project that did not do one of two things. A worthy project should either question our existing assumptions or propose an uncharted pathway directed toward an unexplained biological phenomenon.

Knowing that my advice is antithetical to the status quo, I start with the truth-in-advertising warning that the thoughts presented herein are anti-professional. Follow this advice, and you are almost certain to get your grant application triaged.

PCPs abound in biology. They hit us in the face without even looking for them. Some may defy conventional wisdom and be paradoxical, others may constitute little more than weird curiosities, and still others may rest on a newly observed phenomenon of interest.

I bump into PCPs on a regular basis. Here are several examples that I thought of without getting up from my chair.

Starting with the phenomenon category of the PCP triad, I recount a conversation I had recently with my colleague, Betsy Goldsmith. Betsy is interested in how cells respond to changes in osmotic pressure. Much to her surprise, Betsy found an enzyme that is pressure sensitive and involved in a signaling cascade that responds to extracellular osmolarity. How crazy and cool is this? An enzyme that is pressure sensitive! Betsy sticks her enzyme in a test tube, pumps up the pressure, and the enzyme activates magically. Talk about a cool phenomenon!

Moving to the curiosity category, I turn to a gene my lab has studied for a while – the gene encoding a transcription factor that we call neuronal PAS domain protein 3, or NPAS3. The NPAS3 gene has ridiculously large introns. Two of the introns span nearly a million base pairs. Geez, it takes the RNA polymerase II enzyme five to 10 hours simply to transcribe the gene from end to end. Other genes are big, so the whalelike size of NPAS3 introns is not all that perplexing. Cool and unexpected is the fact that the introns of the NPAS3 gene contain hundreds of ultraconserved elements 100 to 300 base pairs in length. These elements have been conserved for upward of half a billion years, going back to the evolutionary time when our ancestors diverged from teleost fish.

The intronic sequences of the NPAS3 gene are conserved to an extent equal to the handful of exons that encode the polypeptide sequence of the NPAS3 protein. If we knew nothing about exons, introns, proteins — nothing about the central dogma of molecular biology — yet were able to sequence and comparatively align the NPAS3 genes from dozens of vertebrates, evolution would be telling us to pay just as much attention to the ultraconserved intronic elements of the NPAS3 genes as to its protein-coding exons. This is a curiosity.

I’ll close with a paradox. Several years ago, my trainees and I stumbled onto the fact that low-complexity sequences associated with many DNA and RNA regulatory proteins can polymerize into amyloidlike fibers. Intuition and certain experimental observations led us to hypothesize that there might be biologic utility to LC sequence polymerization. Whether we are right or wrong on this remains open to question. The paradox that is clear, however, is that the amyloidlike fibers polymerized from LC sequences are labile. This is crazy. As visualized by electron microscopy, LC amyloids look just like pathogenic amyloids that are rock solid and at the heart of many forms of neurodegenerative disease. How can two amyloid fibers look the same yet be entirely different with respect to lability?

I happen to believe that these three PCPs are pregnant with discovery. That is the good news, and that is what causes me to adore my job. The bad news is that I can’t be sure that studies of Betsy’s pressure-sensitive enzyme, the ultraconserved intronic elements of the NPAS3 gene or our labile amyloids will illuminate our understanding of biology. Instincts tell me they will, but these are the sorts of projects that most grant review groups would automatically reject – the technical hurdles might be way too high, or our instincts may simply be dead wrong.

PCP projects are risky. We all know this. What if our system of grant funding, instead of betting on sure winners guaranteed of incremental advance, instead demanded that each funded project aim at a unique phenomenon, curiosity or paradox? A small fraction of the annual budget of the National Institutes of Health is indeed devoted to high-risk, high-reward projects — perhaps 1 percent in aggregate. Why do we not devote a higher fraction of biomedical research funding to crazy exploration?

The success rate of PCP-funded projects would be modest. Many would fail. By contrast, the small number of wins might accelerate our understanding of how biological systems actually work. The careers of scientists crazy enough to expend their shot on the goal of a four-year period of grant funding on a wild and crazy project might well decay and die on the journey. Despite this risk, I’m thinking that the line for those bold enough to give PCP a try might be long.

Steven McKnight Steven McKnight is president of the American Society for Biochemistry and Molecular Biology and chairman of the biochemistry department at the University of Texas-Southwestern Medical Center at Dallas.