These words, spoken by John at a small and long-forgotten seminar, have stuck with me ever since, have influenced my scientific life profoundly, and I believe succinctly sum up John's scientific philosophy.

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I'll walk briefly through what I know of John's history before I met him. I found it amusing just now, when I googled John and found next to nothing, which is very much what one would expect. John is an acquired taste, one that takes a long time and a certain mind-set to appreciate. But those who appreciate him have generally been strongly moved by him.

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John grew up in Iowa, in a family of Norwegian descent. He was very bright, and skipped a grade or two, starting at the University of Chicago a few years earlier than most. Following his Scandinavian routes, he went to medical school in Uppsala, where he met his wife-to be, Britt. They would be together the rest of his life.

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After John completed both an MD and a PhD in Uppsala, they moved to Seattle 1960 for him to take up a position at the University of Washington. The early part of John's career was focused on cholesterol metabolism and transport in blood. His major contribution was the discovery of lecithin-cholesterol acyl transferase (LCAT), which plays an important role in the packaging of cholesterol into lipoprotein particles in blood, for their eventual transport to liver. One researcher who was in the field at that time told me that this was the "second biggest" contribution to our understanding of cholesterol metabolism, behind Brown and Goldstein's work on LDL receptor.

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While following this path, John was always "listening" to Nature. That's how he did science. He did not wring information out of Nature by force, he set up scenarios in which Nature would tell him in its own time. This paid off twice in big ways in his cholesterol research. First, by his discovery of platelet-derived growth factor (PDGF) with Russell Ross. As I understand it, they were preparing their own serum for their cell culture experiments, and they changed the centrifuge used for sedimenting the blood cells away. This change caused the serum to have more activity than the old serum (or less activity, I'm not sure which, but it was different). Many would view this as an irritation, and figure out a way around it. John realized that Nature was trying to tell him something. Eventually, they realized that the difference was in how many platelets remained in the serum (or how many got lysed in the process) and they purified PDGF this way, a major growth factor.

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The second discovery was protein prenylation. As I understand it, they were tracking cholesterol traffic by feeding cells a radioactive cholesterol precursor, but they kept getting an irritating amount of the label in something that wasn't lipid. Again, they could have ignored this, but Nature was screaming in John's ears. He teamed up with Mike Gelb in a very fruitful collaboration. They tracked down a protein (lamin B) that was covalently modified by an intermediate in cholesterol synthesis (farnysol).

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I joined John's lab in 1991. I could have easily gone elsewhere, but by a twist of fate. I came out to Seattle in June of 1990, three months before my first year of graduate school was to start, in order to take physical chemistry over the summer. While doing that, I got a job in John's lab, working with Rosen Lemaitre. When the PhD program started in the fall, I decided to continue on in John's lab for my first 3-month rotation. The decision was much more one of not-knowing-what-to-do than of enthusiasm. I knew that John was special in some way, but didn't really get him or what he was trying to do. It wasn't until the last two weeks of my rotation that I finally "got it". Had I not spent the summer in his lab as well, I would never have reached that point.

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What I "got" was John's current research passion — phospholipid heterogeneity in mammalian cells. Why do cells have hundreds of different phospholipids, varying in head group and fatty acyl chains in a dizzying array of combinations? John's idea was that each one of these lipids would have subtly different packing properties, preferring to be next to certain other lipids or proteins, making "domains" in the membrane. The nature of these domains evolved in John's mind over the time I was in the lab (1991-1997), eventually becoming small (maybe only a few molecules) and highly transient entities that could re-organize dramatically at the slightest change to the system (like binding of a protein to the surface, or enzymatic modification to a single lipid such as phosphatidylinositol phosphorylation or phospholipase activity). This led to the idea that lipid signaling processes on the plasma membrane could be much more than simply the modification of that individual lipid, but could cause longer-range changes in what's-next-to-what. In other words, a wholesale change in the membrane.

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It is at this point that I must bring up the concept of the "John Unit" (JU), formally defined as one hour spent conversing with (by that, I mean listening to) John talking about science. Over the years, I logged many, many John units, in all sorts of places. Most often, in the hall outside the lab. Once or twice, however, I logged at least a half JU standing in the men's bathroom, with bemused people coming in and going out.

Through these JUs, I eventually got what John was thinking. These were deep ideas, and not necessarily testable ones at the time (or even now). The Units ended up painting a picture for me, a beautiful one. I modify his original quote:

"Nature is painting a picture for us. It is right before our eyes. If we would only open them and see it…"

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At the end of my first year of graduate studies, I found myself in a quandary about which lab to join for my thesis work. I did rotations in two more labs: very good labs, with much more matter-of-fact researchers. These labs had lots of graduate students, and good histories of getting students through. In contrast, I believe only one student had actually graduated from John's lab in his 30+ years, and she had taken 8 or 9 years. Clearly, it would not be a good "business decision" to join John's lab. In fact, it would be a terrible one. BUT, that's the lab I wanted to join. I asked another professor, Dave Teller, what he thought and he said this. "You do science because it's funner than fun. You should go to the place you have the most fun." The choice was obvious at that point.

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Had I not spent both the summer and the fall in John's lab, I would have never "gotten it". It took that much time for John's ideas to sink in. He didn't make it easy to understand, you had to get there yourself.

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John was approaching his questions about membrane domains in two ways. He had Cindy Nist Reynolds doing long-term work, watching cells re-model phospholipids. This work has never seen the light of day, which is a shame because it is profound. If you force a cell to make a certain type of phospholipid that is out of balance from its usual mix, it will very quickly re-model this lipid to the one it wants. This re- modeling mostly concerns the fatty acyl groups on the lipid, a subject that still today few if any people (to my knowledge) have the courage to tackle, but that has the potential to be fundamentally significant. Essentially, the results suggest that this intricate mix of fatty acids and head groups on membrane lipids is certainly not random, and must be that way for the cell to function correctly.

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John also had Ken Applegate modeling lipid-lipid interactions. This was not something that was routinely done at the time, and Ken found that lipids containing poly-unsaturated acyl chains probably prefer certain conformations that would make them pack more tightly than saturated chains, which ran counter to the prevailing ideas. I am not sure what the field thinks now, or whether they have thought about it at all. Once again, the key thing here was that John was "listening" to Nature. He was modeling the lipids that actually exist in Nature (with one saturated and one poly-unsaturated chain) rather than the lipids that most biochemists studied (either both chains saturated or both chains mono- unsaturated).

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I think the field still hasn't gotten to the point where John was back then. Had John been another type of person, he might have beat the drum loudly on these ideas, made the most of the evidence he had to support them, and pushed the ideas into the mainstream by force of character. That simply was not John. I think he was frustrated about not being able to test his ideas in as much detail as he would want, and thus kept many of them to himself (and those absorbing JUs from him). This is a shame, but I don't think it could be any other way. Had John been more of a self- promoter, he would have never had the ideas. They live on in me and in a few others.

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A couple of other things about John's way of thinking about science. I was told by many during my scientific training "don't fall in love with your models! They are usually wrong, and will take you down the wrong road." John's philosophy was almost diametrically opposed to this: fall in love with your models. Nurture them, turn them over in your hands lovingly. But, all the while you are testing them critically. The second you get clear evidence that you are on the wrong path, change the path. You need to have the sense to be able to balance the love of your model with what the data are telling you. The benefit of falling in love with your model is that, even if it is wrong, you will have taken a wonderful journey with it, and will have probably learned a lot in the process.

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Another thing about John is that he changed my thoughts about "the age of genius". It is often said that genius only happens when you're young. Before your mind gets slowed down by the weight of a million-and-one practical things. John is proof against that idea. John kept his mind young and playful. It is a choice: whether or not to keep it that way.

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Which brings me to John's legacy. When people ask where I did my PhD and I say John's name, the overwhelming majority of people look at me blankly. Sometimes I will say that he might be the least known member of the National Academy and of HHMI in the history of either organization. Those who do know him, however, always smile when they hear his name. Michael Brown and Joe Goldstein had a saying in their lab: "Read Glomset's papers. They may seem odd now, but in ten years they will be crucial". I got my post-doc position with Tom Pollard on the strength of his respect for John. The people who knew him respected John deeply, and they were generally people respected by all.

John once described his scientific life to me as "blessed". He started his research career at a time when there was more money than people. He got his first NIH grant with no preliminary data. He proceeded to publish zero articles in his first grant period, and got his grant renewed on the first try anyway. About the time when NIH dollars were getting tight, Ed Krebs got him involved in the Howard Hughes Medical Institute, at the time a nice thing but not the lucrative funding source it became later, and John reaped the benefits of that.

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I have frequently lamented the fact that the timing of my research has not been nearly so blessed, with tight pay lines, fierce competition, and most significantly a push to be "translational". I am often told that my work is supposed to lead directly to medical benefit, which is a reasonable demand considering we are spending taxpayer money that has been given to the NIH. Some of us believe, however, that too much emphasis on this path is counter-productive, because the curiosity-based researcher moves faster than the translational researcher (being able to use the best system to answer a particular question, rather than the most medically relevant). More importantly, the curiosity-based researcher tends to discover the "big" things, because they can let themselves go off the chosen path to follow their nose. In other words, they are "listening to Nature" in a way fundamentally different to that of a translational researcher.

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A few years ago, I was in a minor career crisis. Things were going reasonably well on paper. I was surviving, getting grants, and had a pretty good reputation in my field. But I was not having fun. I was trying to figure out "who I was" as a scientist, and trying to figure out ways to be translational. I was trying to collaborate a lot (somewhat a necessity if one wants to be translational) and was hating it. I really found it very counter-productive.

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In any case, I was in this crisis — I wasn't having fun. I would think to myself  "Woe is me! Why can't I have a career like John's?" I then realized that this was really a mind-set, and didn't have to be governed by the times. In the last five years or so, I have stopped focusing on trying to be anything other than a curiosity-driven cell biologist, trying to make discoveries that interest me. This has actually worked better for me, resulting in more grant money and higher profile publications. It also has been way more fun. I owe that to John.

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I'll end with a non-sequitur. A story that I will remember always, and one of the very best lines I've ever heard a man utter to a woman. John and Britt had the lab out to their place on the Olympic Peninsula (Dabob Bay). After dinner, Britt was trying to organize a big group photo. John was talking away to somebody and not looking at the camera. Exasperated, Britt said "John, look at ME!" John turned to her and said "With pleasure". It brought the house down. I am still waiting for a situation in which to use that line!

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I have been extremely lucky in my scientific mentors. My two biggest influences apart from my parents have been John and my post-doc advisor, Tom. John has influenced my life for the better, and I would not be where I am, both scientifically and personally, without him.