Nancy Eickelmann profiled ACM Fellow David Lorge Parnas for SEN. The following brief biography serves as an introduction to the interview:
David Lorge Parnas holds the NSERC/Bell Industrial Research Chair in Software Engineering in the McMaster University Faculty of Engineering's Computing and Software Department where he is Director of the Software Engineering Programme. He is also an associate member of the Department of Electrical and Computer Engineering.
Prof. Parnas has previously been a Professor at the University of Victoria, the Technische Hochschule Darmstadt, the University of North Carolina at Chapel Hill, Carnegie Mellon University and the University of Maryland. Parnas has held non-academic positions advising Philips Computer Industry (Apeldoorn), the United States Naval Research Laboratory in Washington, D.C. and the IBM Federal Systems Division. At NRL, he instigated the Software Cost Reduction (SCR) Project, which develops and applies software technology to aircraft weapon systems. He has advised the Atomic Energy Control Board of Canada on the use of safety-critical real-time software at the Darlington Nuclear Generation Station and elsewhere.
The author of more than 200 papers and reports, Dr. Parnas is interested in most aspects of computer system design. In his teaching, as well as in his research, Dr. Parnas seeks to find a "middle road" between theory and practice, emphasizing the identification of theoretical results and notations that can be applied to improve the quality of our products.
Professor Parnas received his B.S., M.S. and Ph.D. in Electrical Engineering from Carnegie Mellon University, and honorary doctorates from the ETH in Zurich and the Catholic University of Louvain in Belgium. Dr. Parnas won an ACM "Best Paper" Award in 1979, and two "Most Influential Paper" awards from the International Conference on Software Engineering. He was the 1998 winner of ACM SIGSOFT's "Outstanding Research Award." Dr. Parnas is a Fellow of the Royal Society of Canada and a Fellow of the Association for Computing Machinery (ACM). He is licensed as a Professional Engineer in the Province of Ontario.
Eickelmann: Elaborate on the work leading up to your
achieving the distinction of ACM Fellow:
Parnas: I don't know why they made me an ACM Fellow. I was part of the first batch and to get started they looked at all the people who were members of the highest scientific societies in their respective countries. I was included as a Fellow of the Royal Society of Canada. The question might be better stated, "Why was I a Fellow of the Royal Society of Canada?" I don't know the answer to that either.
I can talk about some of the work that preceded my nomination. I think my work has often attracted attention because I have always chosen to work on problems that I observed in industrial software development, rather than respond to other people's papers. My first "stint" in industry, in 1969, changed the focus of my work dramatically. I went there with an idea that I wanted to try; looking back I believe it was a stupid research idea. The only comfort for me here is that the same idea reappears in the literature every few years. I had written a paper about this research idea and someone at the company read the paper or heard the talk and invited me to work with them. Shortly after my arrival, the fellow was transferred to another location leaving me nothing to work on and two years left in my contract. They put me in an office with people who were actually doing software development. I was trying to see if I could be helpful but I really didn't have anything to do. At the start all I could do was listen and try to understand.
At one point the company asked me to review a document written by some of the regular employees. I said yes and when I looked at it, I realized the company was nowhere near the point where it could use my research results. Their problems were of a very different nature. They did not have the information that I assumed they would have. It was because of this chance to observe industrial development that I began thinking about decomposing systems into modules and writing specifications for those modules. It was clear to me that they were doing it wrong and they didn't understand why it was wrong. While in graduate school, I had never had a chance to observe how difficult, and important, that problem was. The company thought their problem was that they didn't know how to specify their interfaces but I came to the conclusion that the real problem was they had chosen the wrong interfaces. By choosing the wrong "cut points," they had made their interfaces too complicated. If they reorganized the software, their system could have simpler interfaces and these interfaces would be easier to specify. They were looking at a short-term problem, "How do we write this spec?" I was looking at the long term and concluded if they turned their design "inside out," they could build a better system. The result was not my first paper but they were the first publications that had any impact.
Since then, with one exception, every piece of research I have initiated has been motivated by problems that I see in software development. I resist the temptation to respond to research papers by "I can do it better" research. That doesn't mean that I solve problems exactly as presented to me. Usually, as in the case above, I reformulate the problem thereby changing it from a problem that has no solution (e.g. simple specifications for complex interfaces) to one where we can do something, e.g. simplify the interfaces and then document them.
What are your current research interests?
I have been studying various aspects of software design/maintenance documentation and have been doing that for about ten years. I'd like to explain that a bit because many people who look at my work do not recognize it as documentation. They think we are trying to do more theoretical work on "formal methods." In fact, we are trying to apply mathematical ideas that have been known for decades but have not found their way into industrial practice. Often very subtle changes turn a correct but hard to apply theory into an equivalent approach that is easier to apply.
I became interested in the problem of documentation when I was teaching a course for a telephone equipment manufacturing company. What I enjoy about those courses isn't the lecturing but the discussions during the breaks. The participants were telling me some stories about a telephone switch that started out as unusually well-designed software. When it was new, I used to hear complaints about the switch, not from the manufacturer or their customers but from their competitors (who wanted to know how they could add new features ahead of everyone else). When the switch first came out, the designers had published papers about how they had used my modularity and "uses hierarchy" ideas; that is how I got to know them. Ten years later, I was talking to maintenance programmers who were complaining about what a mess this switch had become. When I talked to them about it, it became clear that the software had become a mess because the designers had not documented it properly. Theyhad lots of documentation but it was too large to be useful, too vague to be helpful, and too inaccurate to be trusted. I thought about the SCR/A-7 documentation, which was almost mathematical although we never formalized it or explained the model behind those documents. The big thing that we did right with the documentation was the use of tables. We had written a document that was precise enough to be used as the basis for implementation but readable enough that non-programmer users had found many errors in the early draft. That's when I began to think that we could make mathematical documentation readable for the average programmer if we used tabular notation. If we thought about what ought to be in each document we could come up with a good documentation model and examples of documentation that were concise, precise, and accurate. I have been working on various aspects of that problem since that time.
My work was also strongly influenced by experience that I gained working in a company that was run by a "fallen professor" who also believed in documentation. His idea was that you would produce an outline of all the documents that you were going to write and then proceed, on a fixed schedule, to complete those documents. He seemed to believe that if you produced all the documents in the specified format, the actual product would appear.
His idea was good as far as it went, but it had a fatal flaw. He specified what sections were required, the names of the sections, and the format of the document. However, he was never able to define the content of the sections. People were writing the same information in every section. Sometimes we could have fun. I recall we were supposed to write a section on the safety of our part of the software. At that time (1969), we didn't know what "software safety" meant, so we wrote jokes like "there are no sharp comments" and "none of the loops can get too tight." What we wrote was accepted without question. We met all the requirements.
I see documents like that today; every time I am asked to look at some project's official documentation, I find that it repeats itself horribly and it is never clear where certain key bits of information should be. Standards like DoD 2167 and its relatives do exactly the same thing; they tell you what sections you need but not what the content should be. This has resulted in expensive arguments about such things what goes in the "A" specification or the "B" specification. To avoid such wastes of time, the first thing we did was to write down mathematical definitions of what would go into each document. The next step was to develop tabular notations that would allow us to write practical descriptions of the mathematical relations that we had defined. After that, we started looking at tools. For example, we can generate test oracles from one of these program documents, then generate test cases and estimate reliability, by comparing a program with what the documentation says it should be. You can make documents formal without making them unreadable. It takes a little longer to write the document but the resulting documents are incredibly useful. Tools can check the tabular notation for consistency and completeness. I've also been looking at visualizing programs, a better form of flowchart. No one teaches flowcharts anymore and for good reason; they are not manageable for a large program. But a very well structured and precisely annotated picture of a program allows some programmers to understand how the program is supposed to work. We are annotating the diagrams with our table thereby adding semantics to the diagrams.
While my main focus has been software documentation, I have also recently started to look at how we can use computer networks better. While some people seem to worship "The Internet," and write "commandments" like "There is only one net," I find the present approach to networks frustratingly stupid. Information retrieval takes far too long. We are not using our technology very well and I am starting to work on what can be done if we impose strict semantic standards on application level network interfaces.
What are your current outside interests?
My family, my schnauzer, bicycling and my work. Occasionally, I write newspaper editorials. A professional education as an engineer can provide insights into topics that are far from engineering and I enjoy writing for the public.
What was the greatest influence on you?
Four people taught me how to do research. Two taught engineering and had little to do with computers; the other two were mathematicians who turned to computing. The four were Everard M. Williams, long-time Head of the Department of Electrical Engineering at Carnegie Institute of Technology (now Carnegie Mellon), Alan J. Perlis, founding Head of Carnegie's Computer Science Department and the first winner of the Turing prize, Leo A. Finzi, an internationally known Electrical Engineering researcher, and Harlan Mills, a mathematician best known for the work he did while an IBM Fellow. I have already written about these mentors in SEN so I don't think I should say more.
What was your greatest influence?
I suppose that my early work on "Information Hiding" has had the most influence but I look around and don't see it being used enough. I see it mentioned in papers, and explained (very briefly) in many textbooks but when I look at real systems, I see that it is not being used in most systems. Too many people get into programmer positions without learning how to use such basic (and frequently reinvented) ideas. As Steve McConnell has pointed out, good object oriented design requires that objects hide something. Unfortunately, most of the O-O code that I have seen hides nothing. The programs look like COBOL programs with a new syntax.
Some people think that the articles I wrote when I refused to work on Star Wars had a great influence but I don't agree. First, I don't want to be known for what I didn't do. Second, I find that bad ideas never die. I predict that it won't be long before the SDI ideas re-emerge from the "black funding" areas where they have been hiding and this huge job creation program is again a subject of vigorous debate.
Who do you think has made the greatest impact on software engineering?
It depends on whether you mean academic research or industrial software engineering. An influential academic would be Edsger W. Dijkstra; you can find much of what is fundamental to Software Engineering in his papers on structured programming, hierarchical system structure, synchronization, and verification. Engineers are taught his shortest path algorithm. However, I don't think his work has changed our software very much; few developers read or understand his work. In contrast, if you look for a single individual who has actually influenced what is done in industry, it would have to be Fred Brooks. "The Mythical Man Month" should be read by every software developer and the nice thing is that it is fun and easy to read. Consequently, many people have read and understood his book. That book has sold more copies each year for twenty years and has had tremendous influence. Somewhere in the middle, you can find Harlan D. Mills. He had many good ideas such as using "program functions" instead of pre/post-conditions. The quality of his work is superior to more widely read work but the mathematical sophistication of his work means that it is largely unappreciated by many people in both industry and academia. Today's Computer Science students learn too little fundamental mathematics and practitioners, who have never been shown how to use it, reject mathematical methods without giving them much thought.
Which computer-related area is most in need of investment by government, business or education?
I think it would have to be software engineering education. First we have to improve the quality of that education. I find that most students receive a poorly structured and random introduction to software issues. They learn a lot of folklore that is too vague too apply and a lot of theory that seems (and often is) irrelevant. Second, we must make sure that people do get a professional education. In a world where you need a license to be a barber, anybody can get a job writing software without any credentials. In the last few years I have devoted much of my time to developing an educational program for engineers who are specialists in software, a program that can be accredited by the professional engineering societies.
One of the things I'm trying to achieve by having software engineering programs accredited is to identify a core body of knowledge shared by all graduates of such programs. When I meet electrical engineers, regardless of where they come from, I can draw a circuit diagram and we have common understanding that allows us to discuss that diagram. While there are many things that all EE graduates know, I cannot name a single topic that is understood by every computer science graduate.
We also need to think about better education for those who do not specialize in software. Many non-computer scientists are spending their lives writing programs. Most of our engineering graduates, i.e. mechanical, civil, materials engineers, are writing programs. Often these are very important programs and, even more often, they are bad programs.
We must not expect miracles or easy solutions. Programming is hard because representing information is difficult; it will stay hard. Improving the quality of software is hard because you need to change how people work. People don't want to change. We can approach them best during their education. Once they graduate it is too late for many of them to change.
What advice do you have for computer science/software engineering students?
Most students who are studying computer science really want to study software engineering but they don't have that choice. There are very few programs that are designed as engineering programs but specialize in software.
I would advise students to pay more attention to the fundamental ideas rather than the latest technology. The technology will be out-of-date before they graduate. Fundamental ideas never get out of date. However, what worries me about what I just said is that some people would think of Turing machines and Goedel's theorem as fundamentals. I think those things are fundamental but they are also nearly irrelevant. I think there are fundamental design principles, for example structured programming principles, the good ideas in "Object Oriented" programming, etc.
What is the most often-overlooked risk in software engineering?
Incompetent programmers. There are estimates that the number of programmers needed in the U.S. exceeds 200,000. This is entirely misleading. It is not a quantity problem; we have a quality problem. One bad programmer can easily create two new jobs a year. Hiring more bad programmers will just increase our perceived need for them. If we had more good programmers, and could easily identify them, we would need fewer, not more.
What is the most-repeated mistake in software engineering?
People tend to underestimate the difficulty of the task. Overconfidence explains most of the poor software that I see. Doing it right is hard work. Shortcuts lead you in the wrong direction and they often lead to disaster.
What are the most exciting/promising software engineering ideas or techniques on the horizon?
I don't think that the most promising ideas are on the horizon. They are already here and have been here for years but are not being used properly. A few years ago, I met an experienced software development manager who had just uncovered a memo I wrote for his company in 1969. He told me, "If we were now doing what you told us then, we would be far ahead of where we are now." The biggest payoff will not come from new research but from putting old ideas into practice and teaching people how to apply them properly. There is much more research to do and we have much to learn, but the priority should be put on technology transfer and education.
What are you doing now?
We've started a new Software Engineering program that I think is the first real SE programme in the world. It is an undergraduate program treated just like the other undergraduate programs in engineering. It is designed to get people licensed by the Professional Engineers and I agreed to direct it while it was getting started.
The trouble with teaching the first software engineering programs is that you don't have any software engineers to teach them. There is a bootstrapping problem because there are no graduates yet. Today's programmers may call themselves "Software Engineer," but most do not have the right to call themselves "Engineer." Most do not know what we expect our graduates to know. The best programmers are self-taught. We very much need Engineers who understand software but they are very hard to find.
Ours is the first software engineering program that wasn't started in a computer science department or in computer engineering. The concept of this department is based on an intriguing idea: consider the meaning of the phrase "software engineering." If you look at the history of engineering, you can see that over the years, different branches have split off from engineering, introducing disciplines such as mechanical, civil, electrical, chemical engineering. As our knowledge of science and mathematics grew, it was no longer possible to teach every engineer all that we knew. We were forced to identify various disciplines within Engineering.
At McMaster, we regard software engineering in the same way. There is a great deal that I believe all engineers should know about software but we only have four years to teach them. We decided to address the problem by treating Software Engineering exactly as we treat Chemical Engineering. That way of thinking leads to a program that looks very different than a conventional computer science program. The conventional program considers software engineering to be a specialty of computer science with a few more courses in software. We view Software Engineering as a specialty within engineering. Our students take most of the standard engineering course. There are 42 required technical courses of which about 19 deal with "core" engineering material and the rest are specialized material that is needed for software engineering. This includes some CS material and a lot of mathematics as well as software design courses that include projects. It is important to understand that this is education, not training. We teach fundamentals throughout. None of our courses center on current products or languages but we use practical tools in the many laboratory experiences that are part of the courses.
Please give us any additional comments for the profile.
What an opportunity for a few "cheap shots." I can't resist. I often hear developers described as "someone who knows how to build a large system quickly." There is no trick in building large systems quickly; the quicker you build them, the larger they get!
I have heard people proudly claim that they have built lots of large complex systems. I try to remind them that the job could have been done by a small simple system if they had spent more time on "front-end" design. Large size and complexity should not be viewed as a goal.
One of my pet peeves about this field is the way that people are confusing software management with engineering. They are completely different. Management is the art of getting things done without knowing exactly what is getting done. No manager can know all the details of what all of the people that they supervise are doing. They must learn how to get something done without such knowledge. This is what they learn when they learn to be managers. Engineers are required to know the properties of their products, i.e. they must know exactly what is getting done.
We need both managers and engineers but we should not confuse the two. Unfortunately, a lot of what I hear discussed as "Software Engineering" is really project management techniques. The science and mathematics that we need are not being taught. In any field, badly designed products make a development project hard to manage. Only when we have good designers will we find effective managers.
Thank you for taking the time to share your thoughts with us.
Profiled by Nancy Eickelmann