Andreas, you are honored today with an Impact Paper Award for a paper called “When do changes induce fixes?” What is this paper about?
When software developers make changes to a piece of software, they log those changes in a version control database. And when bugs occur in a program, they are recorded in another database, the bug tracking database. Now, bugs are typically fixed by changing the software, which means that there is an implicit relationship between the bug tracking database and the version control database. Linking the changes to the bugs was not readily possible 20 years ago. We presented an algorithm that was capable of making these connections automatically.
Why has this algorithm proven to be so significant?
These connections enable you to ask, for example, “where in this software project do most bugs occur?” You can also ask, “when did most bugs occur?”, “who fixed the most bugs?”, or “where and when were most bugs caused?” In other words, you can instantly conduct a vast number of empirical analyses of a software project automatically. And because so many people used it, our algorithm later was given a name. It was named after its authors – Śliwerski, Zimmermann, Zeller. It’s the SZZ-algorithm.
Did you already suspect in 2005 that the SZZ-algorithm was going to be a huge success?
It was a small thing at a workshop that we didn’t think much of at the time. We presented an algorithm that worked—wonderful! But after we presented our technique, hundreds of researchers picked it up and used it to conduct empirical studies. Companies like Microsoft and Google also used it and were thus able to determine under which conditions the most errors occurred. In the case of Windows Vista, for example, empirical studies were able to show that many errors were the result of certain management structures at Microsoft.
This is your 11th Impact Paper Award. That is an extraordinary achievement.
It’s funny that all those Impact Papers never won a Best Paper Award. I’ve only won three of those so far. That’s partly because I’ve always enjoyed working in fields and on topics that weren’t yet that big. I found a niche, realized that this niche wasn’t a niche at all, but a huge field—at least to me. Then I kept working on it, and it always took a few years for the topic’s relevance to be confirmed.
So you never let yourself be influenced as much by other people's research?
Ultimately, it’s the same here as everywhere else. You can go with the flow, and then your scientific career becomes more predictable. You make contributions to a field in which many people are already working. That means others understand what you’re doing—they can review and evaluate your work. And, of course, you can make important contributions to science within the mainstream. That’s by no means something to be looked down upon. But you can also say, “I’d rather find a field that’s still largely unexplored.” In that case, you’re more like a scout, while the others advance as part of the big infantry. And as a scout, you head out into the wilderness to see what amazing things there are to discover. That can be very enlightening. But it can also be very arduous, because you have to struggle through the undergrowth. And it’s riskier, too. After all, who knows if you might get eaten by a bear somewhere along the way.
Do scouts in the world of science often get eaten by bears?
Our academic system, which is geared toward high publication output—publish or perish—, tends to reward numerous publications in the mainstream rather than work that is more exotic and that takes several years to gain acceptance. After all, you have to explain and justify your research to the community: “Why are you going in this direction? There is a very clear path that we’re all taking here.” Especially for young researchers just starting out, straying too far from the mainstream is a risk.
Did this distance from the scientific mainstream cause you any difficulties at the beginning of your career?
When I applied for my professorship here in Saarbrücken, I was the candidate with the fewest publications. I had fewer than 10 papers, a ridiculous few. But fortunately, the appointment committee didn’t look at the numbers. Instead, they actually read my papers and realized, “oh, Zeller is doing something completely different that we’ve never seen before in this form.” That’s how I won over the appointment committee and, later on, the reviewers who looked at my work. If there had been a filter based on publication numbers, I would have been dismissed right away.
Has the professorship changed the way in which you publish and conduct your research?
When I took up my professorship, I asked our dean what my measure of success should be: “Am I to write many papers, or secure a lot of external funding, or do something else entirely?” His response was, “no, no, your job is to produce many professors.” So I didn’t have to worry about writing lots and lots of papers; instead, I was given carte blanche to do things that would have a long-term impact. Most of the papers we write still get rejected at first, often by reviewers who don’t share our vision and who say, “those small steps you’re taking toward that vision don’t enthuse me at all.” Sometimes our research is also difficult to explain because we combine elements from different fields, techniques from machine learning with formal methods, for instance. Computer science is a vast and diversified field, and it’s easier for your career if you stay within your own area, because that makes it easier to find reviewers who can assess what you’re doing.
Have you become disillusioned with the academic system along the way?
No. After all, our academic system also knows the concept of tenure, which allows me to be creative and to keep coming up with new ideas. Once you’ve achieved tenure, you can do that without risk and that’s true academic freedom. It’s a great privilege, and it comes with great responsibility. I try to fulfill this responsibility by generating the greatest possible benefit for society. We must create a scientific value that corresponds to the funding we receive.
Looking back, what factors were key to your success in academia?
There needs to be some basic trust in you and, luckily, this trust has always been given to me, both at the university in Saarbrücken and later on at CISPA. This allowed me to focus—purely driven by curiosity—on areas where I saw a lot of potential for improvement I threw myself into these areas and also defined some of them. I’ve been doing this throughout my entire career and luck has always played an important part in all of it, that’s a factor you shouldn’t underestimate. In some ways, I’m a survivor. Many people who, at the start of their careers, want to do something different from everyone else and then keep coming up against their colleagues’ lack of understanding eventually perish. That’s why I can’t say that doing it the way I did it leads to success—I wouldn’t promote it as a recipe for success. It’s a very rocky road at the beginning, and you have to make sure that you can walk it safely.
You’re an important mentor to the PhD students and postdocs in your research group. What is the “recipe” that you try to teach them?
It’s not about publishing a few nice scientific papers for the sake of putting an academic title in your ID card afterwards. It’s about coming up with something really cool. Only once that works well can we tell the world about it. I have high standards when it comes to this coolness. I want my PhD researchers to do something new that has a broad appeal and goes beyond a specific problem, so that it can solve as many problems as possible at once. I’m not interested in just adding another screw to an existing system. Instead, I want to rebuild these systems from scratch. That’s nothing unusual. That’s the standard of excellence that we have across CISPA. I try to instill this excellence in my people, and they also pick it up from their surroundings—CISPA thinks highly of them, and they have to live up to that.
Through Inputlab, you’re involved in a startup in the field of software testing. What role does technology transfer play for you?
My ambition is to create things that not only work in theory but that can be translated into concrete benefits. Not just in principle, sometime in the future—I want to see them taken up during my lifetime and lead to a better software world. That’s also beneficial for the career of my group members. If they aren’t aiming for an academic career, they can start their own businesses or find jobs at the best tech companies. Some of my former group members work at Google, Amazon, Microsoft, or Facebook and are doing great work there.
When talking to you about your research, I often get the impression that it comes with a certain ease.
No, not really. Our research process involves a lot of blood, sweat, and tears, partly because it typically involves developing large systems and prototypes. We struggle just as much as everyone else with the fact that it’s large and complex and that we make mistakes. But when you build a good tool and make it available to the world, you can have a much greater impact than if you simply describe the basic principles of that tool in some paper that ends up gathering dust in a library.
Anyone who follows you on social media learns a lot about your research. Why do you take such joy in science communication?
I like to joke that what I do has to fit into a tweet—I have to be able to explain my scientific work in 280 characters. Breaking down research like that is an art form in itself. It’s also a result of my scouting. I venture out, come back, and say, “There’s a volcanic lake, here are snow-capped mountains, and over there are moose!” That’s how you tell stories around the campfire. And because you’re the first, you can express it in fewer sentences and in a cooler way.
You have won nearly every major award in your field. What do you still want to achieve?
I’ve won 11 Impact Paper Awards, which is almost a little unfair. I was already very happy with three—having achieved three major milestones in my research career meant I’d fulfilled my purpose. But I don’t mean to sound disrespectful. After many years, I’m simply reaping the harvest of what I’ve been planting for some time. And I’m not stopping here. All going well, I want the research that we’re doing right now to be able to win another award in ten years’ time. That’s my ambition.
