It started with a casual remark over coffee. It was the late 1990s, and I was the sole magnetism postdoc in the ferroelectrics group of Karin Rabe at Yale University. “It’s a pity there are no magnetic ferroelectrics,” one of my lab mates said to me as we guzzled espresso, “because then we could collaborate.” “Woah! Is that really true?” I thought. “And if so, why?” This soon became, to me, the most interesting question in the world—so much so that when, a few months later, I took my assistant professorship position at the University of California (UC), Santa Barbara, I abandoned my safe, carefully thought-out plan, and instead embarked on a single-minded hunt for magnetic ferroelectrics. Even when I learned that functional materials elder statesmen Robert Newnham and L. Eric Cross had called magnetic ferroelectrics “the ultimate impropriety,” I remained undeterred. At the time, I was little aware of the impact my choice would have on the field and on my career.
I did not start my quest in a high-tech way, but it was an effective approach nonetheless, piling encyclopedias of magnetic materials on my small table in my office, alongside the only existing book on ferroelectrics. I soon learned that those crystalline chemical compounds already had a name: multiferroics. There were even some interesting candidates for multiferroism, although none presented the characteristic overall magnetization and all had lousy ferroelectric properties.
Before I knew it, multiferroics were no longer ‘mine’ but had a life of their own, with many multimillion dollar, euro, and yen research programs and thousands of active researchers around the world.
Why these materials were so rare and how to go about designing and producing a good one were not understood at all. Being young and naive, I decided to tackle both questions despite the discouraging odds.
I had some advantages: First-principles electronic structure theory—in which the structure and properties of chemical compounds are calculated by solving the Schrödinger equation—had just matured enough to allow the study of materials that I thought might be good multiferroics candidates. In fact, my postdoctoral training at Yale had involved extending existing electronic structure methods so that they could be used to study magnetic systems—exactly what I needed to predict the properties of new multiferroics.
Armed with this tool box, I was able to create computer models of virtual magnetic ferroelectrics and study their properties. I could even simulate the metamorphosis of ordinary ferroelectrics into magnetic ones. My hunt progressed by calculating, thinking, and calculating some more, until, in 2000, I was ready to publish what I felt was at least a partial answer to the question, “Why are there so few magnetic ferroelectrics?”
Around that time, I also discovered, however, that having so much scientific fun has a downside. Solving difficult problems takes time, and my midtenure review pointed out that my publication record wasn’t as strong as it needed to be. Also, when you work in a field that no one else is working in, your publications don’t garner a lot of citations. Kind mentors shook their heads and advised me to start doing something more mainstream—quickly.
Thankfully, the National Science Foundation was adventurous enough to accept my funding proposal and support my theoretical work, so I didn’t have much time to worry about my career prospects. Eventually, my research reached the point where I wanted to see my predictions tested by synthesizing multiferroics in the lab.
I thus embarked on an international pretenure “lecture tour” during which I proselytized about the emerging field and sought the right collaborators. My enthusiasm rubbed off, and some excellent experimentalists soon began making structures I had designed on my computer. In 2001, I gathered the courage to organize the first-ever multiferroics session at the American Physical Society's March Meeting, which gave the field a further boost of exposure and momentum. One year later, I was tenured. Phew!
The first big breakthrough came in 2003 when, in collaboration with the group of Ramamoorthy Ramesh (now at UC Berkeley), we succeeded in producing and understanding thin films of what is now the most-studied multiferroic material, bismuth ferrite. This led to a Science paper and an important scientific life lesson: While a thorough theoretical study might motivate a few hardcore enthusiasts, a high-profile publication can really help stimulate a scientific revolution.
As soon as that paper was published, many research groups and industrial labs became interested in working on multiferroics. One lab even claimed that we were wrong; this was stressful at the time, but, looking back, it was a sign that we had found something significant. Before I knew it, multiferroics were no longer “mine” but had a life of their own, with many multimillion dollar, euro, and yen research programs and thousands of active researchers around the world.
The field has seen many more breakthroughs since then. One of my favorites is the identification in 2003 of another multiferroic with the “improprietous” mechanism, showing that they are not as rare as originally thought. On the device front, in addition to the originally envisaged electric-field control of magnetism, the unusual properties of so-called domain walls—internal interfaces between regions of differently oriented ferroelectricity—are proving intriguing and promising. Another important finding is the blossoming of yttrium manganite in unanticipated directions—including the possibility of studying cosmic string formation in the early universe under a laboratory microscope.
Nowadays, I travel the world to lecture, teach, and collaborate. I enjoy discussing our new “most interesting questions” with brilliant students and scientists, many of whom are now good friends. With amusement, I find I have been typecast as “the multiferroics lady” even when I plan to discuss new topics and directions.
Frighteningly, I have reached the stage in my career when young people frequently ask me for advice. My safe and sensible side tells me I should pass along the same good advice that I received: Make a solid contribution to an established field and publish a lot, which will in turn help you become known and respected by your community. Save the high-risk stuff until after tenure. But deep down, I hope young scientists—you—will choose not to follow that advice. I hope that, instead, you will find a question that to you is the most interesting in the world, go after its answer with all your youthful passion, and pioneer your own science revolution.