Held October 7, 1998 at

Lawrence Berkeley National Laboratories

Berkeley, CA

In August 1998, the President’s Information Technology Advisory Council (PITAC) issued an interim report on the state of Federal programs sponsoring research in information technology. In brief, the report found that the level of funding did not match the importance of information technology in the national economy and that far too much of the research money was being spent on near-term work rather than long-term research. To remedy this problem, the report recommended that information technology research funding be increased by $1 billion per annum, and that this funding be focussed on four areas: (1) software; (2) scalable information infrastructure; (3) high-end computing and (4) socio-economic and workforce impacts of information technology. The report further suggested that the National Science Foundation (NSF) be designated the lead agency for this research program.

This workshop was held to allow the networking community to give NSF the community’s views on the topic of scalable information infrastructure. The workshop was structured to help NSF respond to the PITAC report, by giving NSF guidance on possible research programs and ways to invest research funding most effectively over the next decade. This report is the primary product of the meeting.

There are a certain set of themes, or cross-field issues, that appeared repeatedly in our discussions of networking research. These issues are not limited to one subfield of networking research but affect a wide range of research activities.

One theme is the need for networking research to stay ahead of various growth curves. For instance, the Internet is growing at a rate of 100% to 200% per year, depending on which metric is used, and has sustained that rate of growth for over a decade. Much as Moore’s law guides the chip industry research and indicates what performance needs to be achieved in what timeframe, these growth curves guide Internet research, indicating what levels of scalability and performance need to be achieved at given points in the future.

A second theme was the importance of classifying work as basic research, or advanced research and development not only when talking about research programs but also when talking about network infrastructure such as testbeds. The workshop felt that both NSF and the general networking community need to distinguish more carefully (both for the community and general public) between networking testbeds, intended to produce basic and applied networking research, and testbeds that are, in fact, infrastructure (indeed, not even development networks) deployed to support the research of non-networking fields.

A third theme was to accept that the communications field has changed and that we need to create new ideas and develop new theory to cope with the new reality. An example of this theme is the need for new models for robust operation which assume that components are stateless and communications paths may fail. Another example is the need to make applications (and their authors) network-aware and capable of working with lower-layer protocols to perform functions such as power and signal management and to improve throughput.

A fourth theme was scaling: scaling in size, scaling in speed, and scaling in diversity. The word scaling was often part of our discussions because so many of the challenges that confront us are caused by, or impacted by, scaling concerns.

The workshop spent a considerable amount of time identifying research areas in need of attention in the coming years. The focus was on topic areas that need long-term attention; areas that would benefit from sustained attention over the next ten years.

One important consensus that emerged from this discussion was that there is a tremendous richness of visions of the future for networking. NSF has a strong tradition of encouraging researchers to bring forward new visions and the research ideas those visiosn inspire. We would like to encourage NSF to continue this tradition, rather than to adopt a programmatic approach which seeks to implement a particular vision. The contrast here is, of course, with DARPA which specializes in creating visions and stimulating outstanding research to realize those visions. The workshop felt that the NSF and DARPA approaches are complementary and that we should work hard to encourage both agencies to continue to do what they do best.

While the workshop developed some visions of the future, we viewed them as thought exercises. We identified visions and asked ourselves what areas of networking research needed attention to make those visions possible. One of the properties of a useful vision of the future was it raised questions in a number of areas.

As examples, here are two of the visions of the future that the workshop discussed:

1. Embedded processors with wireless interfaces. It will soon be possible to embed transceivers (wireless or wireline with megabit per second data rates) within processor chips. This possibility presents the prospect of every embedded processor (of which several billions are sold annually) being connected to the global information infrastructure. We found ourselves confronted with the challenges and opportunities of trillions of end-nodes, constantly reconfiguring themselves as they come into proximity with other nodes. The vision illuminates tremendous problems of scaling, of self-configuration, adaptation and authentication.
2. Information and Computation without Boundaries. Imagine a future in which the entire information infrastructure has no dependencies on physical topologies in communications and no physical barriers, such as firewalls, that limit information exchange. In short, envision a sea of diverse information resources. This vision offers tremendous opportunities for fast reconfiguration and custom computing. (For example, suppose you could custom design your car — a software agent would find the suppliers for the types of parts you wanted, confirm they could be assembled, locate an assembly location, and then present you with an price. Or suppose the global infrastructure tried to optimize information distribution in the network, so that most of the information a particular user might want was stored close to that user’s present location). It also presents tremendous problems of information discovery and coordination. There are serious challenges to providing the right information to the right people in the right form at the right time.

The research areas we identified as particularly in need of attention were:

• Basic Theory. The field of networking has yet to develop the same strong theoretical foundations enjoyed by other areas of communications. Although queueing theory (and other probabilistic techniques), algorithms and signaling theory have been studied for some time, it has been difficult (with notable exceptions) to apply the results to real networks. While some of this problem is caused by the complexity of the task, much of the problem can be attributed to a lack of dialog between network practitioners and theoreticians. There is a need for increased collaboration between theoreticians and practitioners.
• Understanding global behavior. We have a very poor understanding of how the network behaves in aggregate. Valuable research opportunities exist in areas such as self-similar traffic patterns, synchronization effects, and economic models of behavior. It is also important to develop methods (and supporting theory) for achieving robust operation and good performance in a system made up of many unreliable components. Much of this work depends on research to develop better techniques to measure the network, including methods for capturing and anonymizing traffic traces that preserve most vital information about each packet while also preserving confidentiality of user data.
• Design methods and tools. We do not know how to simulate networks that scale to millions or trillions of nodes. But the alternative (actually building such huge networks only to see them collapse) is not acceptable. We desperately need tools to model, simulate and analyze huge networks. Similarly, we need new tools to understand and evaluate what it means for a system (such as a distributed database) to work correctly in huge, and almost inevitably, semi-reliable networks.
• Physics of Networking. The rise of wireless and power-limited devices suggests the need for protocols and systems that are power-aware, that exchange information in power-efficient ways. At the other end of the bandwidth range, the continued demand for greater network bandwidth demands continued basic research into optical, electrical and wireless signalling and switching technologies.
• System Design. How do we continue to build networked systems that perform at the link speeds and network sizes that current growth rates predict we will need? What is the correct mix of ASICs, programmable hardware, and software that gives the best performance and flexibility?
• Software Mechanisms. How do we build and manage distributed systems comprised of billions of nodes (including not just hosts but the routers that interconnect them)? How do we build systems and networks that can at least partially self-configure themselves and operate robustly in the face of inevitable errors? What modularity of function best supports these goals?
• Interoperability. Effective networking requires not only that we move the bits but also that the heterogeneous destinations understand what is in the bits they receive. How can we build systems that ensure that a receiver fully understands a piece of data to have the same information and meaning as the sender intended?
• Models of (In)Security and Authentication. Historically, network security has been studied from the military perspective of absolute security and authentication. An alternative, used by the private sector, is to model security as a cost-benefit issue: how much does it cost to secure information vs. what is the cost of the information being intercepted. What kinds of security systems does the cost-benefit approach yield? How do they differ from the traditional approach and how might they be used in today’s communications networks?

To achieve outstanding research results in these areas, NSF will need to increase its porfolio of funding mechanisms. Success in many of these research areas require team efforts. Examples include assembling a mixed team of theoreticians and practitioners to measure and study network behavior, or creating a three or four person hardware and software team to develop, produce and demonstrate an ASIC. Some of those teams can be assembled at a single institution, but in many cases the teams will be multi-institutional. NSF will need to expand activities such as its Special Projects program to encourage these kinds of research. Note that the workshop believes that these special projects should be researcher-initiated, building on NSF’s tradition of researcher-initiated activities.

Networking research also often requires building custom systems, both in hardware and software. Building these systems can be expensive, especially for hardware. In recent years, the government funding agencies have assumed that industry could be persuaded to supply many of the expensive resources. For truly cutting edge research, however, expecting industry support is a mistake, because the link between the research result and the future financial return is not yet clear. Much as it needs to find ways to support team research, NSF will need to expand its mechanisms to, at least occasionally, support substantially more expensive efforts.

Education and research are closely related. For example, funded research plays an important role in educating graduate students. A recurring concern at the workshop was the tremendous shortage of professors and the great difficulties retaining Ph.D. students in the networking field. It is clear that the networking community, quite likely in conjunction with NSF, needs to address these problems. At the same time, we feel strongly that issue of attracting, supporting and retaining faculty and students, and research activities should be kept distinct; that both the retention and support problems and research problems are sufficiently large that each requires undivided attention.

Finally, there were several concerns about networking testbeds. First, some testbeds are simply development projects assembling high-speed components and do no research (basic or applied). A simple metric to apply is to ask if it is acceptable for the network to be taken down, perhaps for days, as researchers tinker with it. If not, it isn’t networking research and networking research money should not be spent. Second, some testbed plans are exclusive, limiting access. Two forms of exclusion are particularly important. Some testbeds have excluded industrial researchers. Our view is collaboration with qualified industrial researchers should be encouraged. Second, many testbeds do not make it easy to capture and measure traffic. Given that traffic measurements (including full packet traces) are vital tools for networking research and often very hard to get from commercial networks, the workshop strongly recommended that NSF’s default policy be to require any testbed to implement measurement and capture facilities at multiple points in the testbed (with appropriate tools to allow coordinated tracing at multiple locations simultaneously) and to make those facilities available to any qualified researcher.

This workshop should be only the start of a continuing series of activities on the part of the networking research community to respond to initiatives outlined in the PITAC interim (and final) report. The importance of communications in our economy, and the increased level of funding that the PITAC proposes to entrust to us, places an obligation on us to think carefully about our field’s future and about how to invest our resources most wisely.

Dr. Craig Partridge (chair), BBN Technologies (part of GTE).

Prof. Tom Anderson, Univ. of Washington.

Dr. David D. Clark, MIT Laboratory for Computer Science.

Prof. Deborah Estrin, Univ. of Southern California.

Dr. Sally Floyd, Lawrence Berkeley National Laboratories.

Michael Foster (observer), National Science Foundation.

Prof. Michael Greenwald, Univ. Pennsylvania.

Prof. Leonard Kleinrock, Univ. California, Los Angeles.

Prof. Nick McKeown, Stanford.

Prof. P. Michael Melliar-Smith, Univ. of California, Santa Barbara.

Prof. Louise Moser, Univ. of California, Santa Barbara.

Prof. Guru Parulkar, Washington University — St. Louis.

Prof. Jonathan Smith, Univ. Pennsylvania.

George Strawn (observer), National Science Foundation.

Prof. Ellen W. Zegura, Georgia Institute of Technology.