The Minimal Publishable Unit: Building a Scientific Story One Layer at a Time
During my postdoctoral training with Dr. Edward Benjamin Thorp, we developed an approach to scientific story building that we called the Minimal Publishable Unit, or MPU. The idea was simple: at any point in a project, you should be able to identify the smallest complete scientific story that could be published in a rigorous, respected journal in your field. Not the highest-impact journal you think you can reach. Not the dream version of the paper after three more years of experiments. A solid, defensible story that contributes something meaningful and could be submitted now.
That MPU becomes the foundation. For strategic reasons, sometimes that is the paper you publish. But more often, it gives you something equally valuable: a clear view of what is missing. What is the next question that would make the story stronger? What experiment moves the work from observation toward mechanism? What takes it from mechanism toward physiological relevance? You fill that gap, reassess the story, and identify the next one. With each iteration, the MPU gets stronger and the potential ceiling for the paper gets higher. Instead of designing a project around a journal, you build the science one layer at a time and let the depth of the eventual story determine where it belongs. For me, most strong scientific stories have four major components.
First, there needs to be an in vivo phenotype. We study physiological processes, and my training in the Department of Physiology at Dartmouth College instilled an appreciation for placing molecular and cellular findings within the larger context of systems biology. A pathway can do something interesting in a dish, but what does it mean for the organism? Does manipulating it change disease? Does it alter physiology? Does it matter in vivo? Those questions anchor the rest of the story.
Second, we look for human relevance. In our laboratory, this has often involved post-mortem human specimens, sometimes in relatively small and exploratory cohorts. I don't expect every mouse experiment to be perfectly reproduced in humans. But whenever possible, I want evidence that the biology we are studying exists in human disease. Ultimately, we are trying to understand, prevent, and treat diseases in people, not mice. It is often joked that we have cured heart disease a thousand times in mice. The frustrating lack of equivalent progress in humans is exactly why establishing some degree of human relevance matters.
Third, and perhaps most importantly, we pursue mechanism. This is an area where Ed had an enormous influence on my development as a scientist, reflecting in part what he learned during his own postdoctoral training with Dr. Ira Tabas, and it is something I try to pass on to my trainees. For us, mechanistic studies often mean reducing a complicated biological system into its component cells, pathways, and proteins so that we can understand how the pieces actually connect. Other laboratories do this beautifully in vivo through sophisticated genetic models and other approaches. The tools can differ. The principle does not. My PhD committee member Dr. Charles Wira once told me that you want a scientific story that is a mile deep and an inch wide, not a mile wide and an inch deep. That has stayed with me. It is relatively easy to keep adding observations. Another pathway. Another cell type. Another association. It is much harder, and much more valuable, to keep asking why. Connecting the dots is more meaningful than accumulating them. To me, one truly mechanistic study can be worth ten associative ones.
Fourth, when the biology allows it, we ask whether it can be therapeutically targeted. I am a biomedical scientist, so eventually I want the work to come back to human disease. Has the mechanism uncovered something tractable? Can manipulating it improve physiology or disease outcomes? Can we move beyond describing what goes wrong toward testing how we might fix it? This is also where collaboration has been invaluable. I am not a chemist or bioengineer, but we have been fortunate to work with bioengineers and biopharmaceutical partners whose technologies and therapeutic platforms allow us to ask questions that our laboratory could never answer alone. Good collaboration lets everyone bring what they do best to a problem.
Not every paper needs all four pieces. Some questions do not have an immediate human parallel. Others address biology where the potential human implication is itself the long-term goal, transplantation tolerance, for example. And none of this captures all the variables that ultimately determine where a paper lands. Novelty matters. Timing matters. How clearly you communicate and sell the science matters. Who you are probably matters. And whether we like admitting it or not, luck matters too. The MPU isn't really about publishing the minimum. It's about always knowing what your story is. Build the smallest rigorous version. Identify the gap. Fill it. Then ask again what is missing. In vivo physiology gives the biology context. Human relevance gives it purpose. Mechanism gives it depth. Therapeutic targeting gives it a path forward. Then you keep building until the science tells you the story is ready.
