First, the responses below are based on my personal experience and opinion. They are domain specific , may not apply in general, and certainly should not be taken as golden rules.
1.Most scientific fields and topics go through historical cycles. It starts with a breakthrough or new demands from the real world, e.g., the aerospace and landing-on-the-moon race during the late fifties and early sixties for the control and system field. There were flurry of activities, discoveries, and applications. This is the first generation. From this point on, the real world are more or less satisfied but continues to support additional research since the subject has yield fruitful results and the real world needs trained workers. The theorists take over, refine and deepen the results, and erect a framework and foundation for the topic. Textbooks were written, faculties were hired , more students educated, and the field continues to bloom. In control and systems this approximately covers the 70s and 80s. However, sooner or later, the field reaches maturity and the third generation stage. At this point, jobs become scarce for new entrants because both the academic and industrial area are already well staffed with trained people not yet retired. Whatever problems that remain are either very hard or irrelevant/unimportant to the real world. People are either doing work amounting to “gilding the lily” or, trying to find new application areas or busily looking for new topics to invent. There are little cross pollination between the theory and the applied domain. Everything is in steady state. This is where control and system field are now. When a new breakthrough happens or new demand arises, the cycle will repeat.
2.So what are the new subjects for people trained in control and systems. Financial engineering, Bio-informatics, manufacturing automation, transportation and energy utility management are all examples and possibilities suggested. However, unlike the aerospace topic 50 years ago, here we must compete with economists, biologist, chemists, computer scientists and other technologists with the same objectives. Nor do we have unique monopoly on knowledge in such subjects. The “perfect storm” that existed half century ago is no longer present.
3.This brings me to my third point. It is useful to change you field or topics of research every now and then for a number of good reasons. I have mentioned these in my blog article “How to do research http://www.sciencenet.cn/blog/user_content.aspx?id=2224 and its Chinese translation http://www.sciencenet.cn/blog/user_content.aspx?id=23438. as well as http://www.sciencenet.cn/blog/user_content.aspx?id=23465 While academia tends to favor “depth” over “breadth” and pays a premium for specialized expertise. There is the danger of too much specialization ( 躜入牛角尖). You began to know more and more about less and less until in the limit you know everything about nothing. Furthermore, technology can easily pass one by. Valuable technical knowledge one day may become worthless the next. Look at what happen to Polaroid and Kodak company in the photographic field and Encyclopedia Britanica in the publishing field. Finally, a new field is like a newly ripened fruit tree. If you are there first, , you can easily pick off the low hanging fruits. Latecomer must work harder. A well known quote from the great von Neumann is appropriate here:
"There is, however, a further point which, I believe, needs stressing. As a mathematical discipline travels far from its empirical source, or still more, if it is a second and third generation only indirectly inspired by ideas coming from "reality," it is beset with very grave dangers. It becomes more and more purely aestheticizing, more and more purely l'art pour l'art. This need not be bad, if the field is surrounded by correlated subjects, which still have closer empirical connections, or if the discipline is under the influence of men with an exceptionally well-developed taste. But there is a grave danger that the subject will develop along the line of least resistance, that the stream, so far from its source, will separate into a multitude of insignificant branches, and that the discipline will become a disorganized mass of details and complexities. In other words, at a great distance from its empirical source, or after much "abstract" inbreeding, a mathematical subject is in danger of degeneration. At the inception the style is usually classical; when it shows signs of becoming baroque, then the danger signal is up. It would be easy to give examples, to trace specific evolutions into the baroque and the very high baroque, but this, again, would be too technical." From Salim Rashid, "John von Neumann and the Scientific Method (Critical Essay)", J. of the History of Ideas, July 2007,
4.Questions have been raised about the gap between theory and application. This gap always existed in any field. But it becomes very pronounced during the third generation stage I mentioned above. On the one hand, most of the pressing problem of industry have been successfully solved. Enough students have been trained to satisfy demand. On the other hand, the majority of the third generation theoretical problems are of little interest to industry. As such mutual disrespect starts.
5.Now, how does one find new problems? In academia you have opportunities to do consulting or industry sponsored research. Such activities are very different from government sponsored research projects. My experience in the US is that industry only care about results and if they are getting their money’s worth. They do not care how many papers you publish and reports you turn out. Such attitude has a wonderfully way of giving you flexibility and at the same time focusing your attention on what really is important. Focusing on the essence also helps you if you want to establish a theory based on such practical work.
I think the above more or less addressed or touched upon most of the requests and questions raised in this first round.
精选
