From - Sat Mar 20 11:43:02 1999 Received: from cs.columbia.edu (cs.columbia.edu [128.59.16.20]) by opus.cs.columbia.edu (8.9.1/8.9.1) with ESMTP id UAA22763 for ; Fri, 19 Mar 1999 20:59:37 -0500 (EST) Received: from pender.ee.upenn.edu (root@PENDER.EE.UPENN.EDU [130.91.5.20]) by cs.columbia.edu (8.9.1/8.9.1) with ESMTP id UAA11434 for ; Fri, 19 Mar 1999 20:59:31 -0500 (EST) Received: from ee.upenn.edu (slip-32-101-37-54.ny.us.ibm.net [32.101.37.54]) by pender.ee.upenn.edu (8.8.5/8.8.4) with ESMTP id UAA05635; Fri, 19 Mar 1999 20:58:05 -0500 (EST) Message-ID: <36F300DA.B821F676@ee.upenn.edu> Date: Fri, 19 Mar 1999 20:58:50 -0500 From: Roch Guerin Organization: University of Pennsylvania X-Mailer: Mozilla 4.5 [en] (Win95; U) X-Accept-Language: en MIME-Version: 1.0 To: "McKeown, Nick" , "Schulzrinne, Henning" , "Keshav, Srinivasan" Subject: Workshop panel Content-Type: multipart/mixed; boundary="------------2B098C5059D9811E6C5E82F1" X-Mozilla-Status: 8001 X-Mozilla-Status2: 00000000 This is a multi-part message in MIME format. --------------2B098C5059D9811E6C5E82F1 Content-Type: text/plain; charset=us-ascii Content-Transfer-Encoding: 7bit Folks, I have attached to this note the statements that each one of you provided and the one I wrote with some intorductory material on the panel. We have one more likely drop out. Rajiv Ramaswami informed me that his president is visiting their site on Monday afternoon, and he is likely not to be able to make it because of that. Erich Nahum from IBM has agreed to step in at the last minute and will try to provide an "industry" perspective. >From the attached statements, you'll see that we have some general agreements on some of the potential causes of "problem" but have a reasonalby varied range of opinions on where we will end-up. So I have not attempted to modify anyone's statement to ensure greater diversity. I have asked Erich to take a position with minimal overlap with the ones expressed in the statements. Let me know if you have any question. Otherwise, see you on Monday. Thanks, Roch --------------2B098C5059D9811E6C5E82F1 Content-Type: text/plain; charset=us-ascii; name="panel.txt" Content-Transfer-Encoding: 7bit Content-Disposition: inline; filename="panel.txt" PANEL: IS NETWORKING RESEARCH DEAD? Introduction and Roch position Why such a panel? ----------------- Networking is one of the hottest field around and it is probably more popular and relevant than it ever was. One only has to look at enrollment in networking courses, the number of conferences and workshops in related areas, and the number of new technologies (and companies) in the field of networking, to be convinced of this. But every body is concerned that given where we are right now, the only way ahead is down (reminds me of the stock market). Is this only a healthy and understandable reaction following a meteoric rise, or is it a symptom of deeper problems. The disturbing signs -------------------- Reinventing the wheel. Many basic ideas that have been around for quite some time in one form or another are being recycled, often without proper acknowledgement, with only minor cosmetic changes to craft them in more contemporary terms. My personal favorites are the Diff-Serv and MPLS efforts, that while serving a useful purpose, are happily ignoring or repeating work done in telephone networks, in ATM (the evil twin), and many of the early research efforts on high speed networks. Incremental work. Much effort is being spent on addressing engineering problems that arise mostly because of the need to coexist with how things are done today. The problems are hard, important, and certainly require cleverness in addressing them, but they don't go beyond realizing an existing vision. Relevance above all. Much research work is being scrutinized, even before it can start, to determine its potential relevance and whether it has the ability to impact existing systems. Emphasizing relevance is not a bad thing in itself, and is certainly a healthy occasional check, but when it becomes the dominant and first criteria, it can squelch innovation and forward looking developments. Some possible reasons --------------------- The weight of success. By all accounts, the Internet is the biggest thing happening today in the area of technology, and its economic impact is affecting every technical and scientific activity even remotely related to it. Networking "research" is one of the casualties. IETF RFCs are becoming the holy scriptures that no one can question, and going against the flow is likely to get you villified on numerous mailing lists, characterized as decoupled from what matters, and called ignorant of what the hard issues are. Given the level of scrutiny this implies and its impact on potential funding, it is no surprise that researchers get their heads slowly but surely bent towards safer and more immediate problems. Note that this applies to academia as well industry research, although the funding aspects are clearly different (government vs dept vs venture capital). Furthermore, the baggage that every new effort needs to carry (in the name of backward compatibility and the like) can be overwhelming, and yet another deterrent to drastic departures from the established order. The Internet gold rush. With the research community afloat with news of lucrative startups and companies providing substantial compensation to reward successful projects, the lure of a quick return is hard to resist. As a result, many of the new research efforts have either explicitly, or more often than not as a hidden agenda, the goal of striking it rich. This is clearly not an environment conducive to long term perspectives and forward looking agendas. Some glimmers of hope --------------------- We are not done yet. There are plenty of hard problems left in today's networks and solving them will require more than just minor modifications or extensions of existing approaches. Network reliability, service verification, pricing models are areas where we have barely scratched the surface. Managing and characterizing the unwieldy and heterogeneous infrastructure that the Internet has become is yet another area which we barely understand. The focus may be shifting but there is clearly much work left. Some new frontiers. The networking and internet revolution was brought about by a combination of technology discontinuities (transmission, processing), and there are several potential candidates that can yield the same level of disruption for today's networks. Optical and wireless technologies are two that immediately come to mind, but there are others. For example, space may indeed be the next frontier and there are already talks of inter-planetary Internet and the new problems it introduces. But there are plenty of pitfalls ahead. The temptation will remain to develop quick fixes for many of the problems, or to simply extend existing approaches to new environments. Once this has been done, dislodging the incumbent will be close to impossible, and we will remain captive of the vision of a previous generation. --------------2B098C5059D9811E6C5E82F1 Content-Type: text/plain; charset=us-ascii; name="nick.txt" Content-Transfer-Encoding: 7bit Content-Disposition: inline; filename="nick.txt" Panel - Nick McKeown position Title: Is Internet Research Dead? Part I: Why are we asking the question? * Are we looking back with rose-tinted spectacles? "In my day, the Internet research was much better..." * Was there ever a time when more interesting, novel and relevant networking research was being done? Part II: Are we saying that we have all the answers? * There are plenty of seemingly "mundane" areas that still require a lot of research work: mobility, packet-switch design, ... * There are plenty of questions to ask for which we have precious few answers: traffic modeling, network-wide modeling, economic models ... The problem areas may be shifting (maybe), but there is still plenty to be done. --------------2B098C5059D9811E6C5E82F1 Content-Type: text/plain; charset=us-ascii; name="keshav.txt" Content-Transfer-Encoding: 7bit Content-Disposition: inline; filename="keshav.txt" Panel - S. Keshav position Networking research was a good idea until it became relevant :-) Networking has the peculiar property that a networked component has to speak to another networked component for any useful work to be done. Unlike OS research, where an unconnected endsystem incompatible with every other endsystem in the world still demonstrates the utility of an idea, in the networking world, your idea has to be widely adopted in order for it to have impact. For instance, an improved TCP++ that is incompatible with existing TCP would be of little use other than in a tiny testbed. Thus, networking, by its very nature, tends to rapidly promote standards, and once these standards are chosen, it is next to impossible to dislodge them, no matter how broken they are. This is the bane of networking research. For instance, due to the widespread use of TCP/IP, research in TCP is, for the most part, meaningless, unless you can show that your improvement co-exists with TCP. Many years ago, for another instance, I decided that further work in flow control was pointless: if you did not do TCP, to be TCP-friendly, you have to work exactly _like_ TCP, so whats the point. This same lesson is being repeated over and over again in other arenas. As a major example, ATM is dead because in order to succeed, it has to look like the Internet! To sum up, networking researchers working in areas that are substantially standardized have to make a hard choice. Either they pursue their dream, and ignore reality, or they pursue reality, and become mired in the goo of the last 30 years of lousy defacto standards. The alternatives are either to give up on research, or to work on an unstandardized (substandard?) area. We are seeing both. As one looks at Sigcomm proceedings, you see more and more an emphasis on non-traditional research. This is the flight from standards. Or, you see people giving up research, because if you going to be fiddling with existing standards, why not make some money off it. (other panelists, no doubt, will elaborate on this last sentence). Which brings me back to my first observation. As long as networking research was irrelevant, we could all do good work. Now, when the success of the Internet has forced relevance upon us, we are seeing the end of (traditional) research. --------------2B098C5059D9811E6C5E82F1 Content-Type: text/plain; charset=us-ascii; name="henning.txt" Content-Transfer-Encoding: 7bit Content-Disposition: inline; filename="henning.txt" Panel - Henning Schulzrinne position Future of Networking Research In some sense, networking research is doing quite nicely: Infocom, for example, lists roughly 2200 authors, reviewers and TPC members, providing an indication how large the research community has become. Just about every university has a or wants to have a faculty doing networking research, while this used to be limited to a few DARPA sites. Networking courses are regularly among the most popular systems courses in universities, with almost all graduates getting some amount of network technical knowledge, either through OS or specialized courses. The number of seminars, conferences and journals keep increasing, although this seems to be the typical delayed reaction, with signs of bottom-fishing. Threats to research vitality are many: - "Telephone research?" Since probably the 1950s, there wasn't any university-level research on telephone services and "protocols", so that most of today's phone system was developed outside the core network research community. The last time around, there was the physical-level advances and this packet stuff. Is there a large-scale replacement? - Somewhat similar to OS research, the installed-base problems gets worse every year. With OS, you can at least set up specialized computer systems for new tasks. With networks, connectivity trumps everything. See the very slow (compared to predictions) deployment of multicast, IPv6 or RSVP. - As with other CS/EE disciplines, almost all US PhD students are non-US-born. It is not clear that this is a stable operating mode. Only about 15% of computer-science undergraduates continue even for an MS degree. - There is an increasing disconnect between the things that make it into standards and academic network research, as academic participation in the IETF and ITU decrease in both absolute terms and even more in relative terms. - The patent-everything-in-sight mentality has made certain areas basically off-limits. For example, there will be no publicly available Internet telephone code, except possibly by Microsoft, due to G.72x licensing restrictions. Same for MP3 encoders ($25/encoder copy). - Through its success, networking research will have to change from "automobile engineering" to "highway engineering", i.e., from isolated components to infrastructure research. Getting reliable information about the infrastructure is hard, with little reliable data available, beyond aggregrate statistics. - DARPA projects seem to be more narrowly focused on very specialized defense-needs rather than generic network research. There seem to be few resources for creating research-level implementations of common protocols. There seems to be an increasing specialization in research. Exaggerated examples: while the 'east coast' labs used to do a broad swath of networks, this is no longer the case: Lucent switching, layer3 IBM web, data applications Bellcore phone consulting, IP hand-holding AT&T traffic and management Longer term, there is the "mechanical engineering" model: Communications will continue to be an important part of the economy, but the emphasis will be on teaching large number of undergraduates and non-PhD-level development. Networks will become a service course, to some extent like operating systems. You have to know it, but very few people will do true research in it. - --------------2B098C5059D9811E6C5E82F1--