Research in communications networks is a challenging enterprise many find worthy of endeavour. Suppose we have answered “why” to do networking research in the first place and let us move to the second most important question, that of “how”.
Communications research can be seen as having attributes of both science and engineering. I think this also corresponds to the main reasons of “why”; it is interesting on its own (the science bit, just as it is interesting to research the age of universe and the structure of our genes) and there may be a practical benefit for the society (the engineering bit, “I’m doing something useful”). On the one hand, some networking research is very theoretical (i.e. unlikely to benefit any implementation) and yet interesting, just as it is interesting to research the age of the universe and the structure of our genes. On the other hand, the benefit to society best stems from a practically-oriented research.
In this article, I would like to present some ideas for constructing a worthy research topic and research work in the field of communications networks. In particular, we will use network Quality of Service (QoS) research as an example.
3 Strategic Considerations
We have identified the following strategic considerations:
As noted by J. Crowcroft et al. in , the time required to research, engineer and retrofit a specific solution is typically longer than the remaining life-span of the congested core. If research commences only when there is an immediate need for it, it is too late. The ability to envisage future needs is essential here. We will present three drivers of new networks which help in predicting the future.
The lack of attention to non-research issues was the main reason behind the failure of network QoS research. Deployability encompasses various operational (practical) and economical issues.
Given the need for a new mechanism, what is the best thing for it to do? To illustrate the problem, consider that there is a general consensus on the need of QoS, but there is much less agreement on the specific functionality, as seen from the existence of proposals as different as IntServ and DiffServ. We will try to show that functionality is tightly connected to deployability and recommend that a proposed mechanism should maximise benefits subject to constraints given by deployability considerations.
1 – Timeliness
Research must commence a long time before there is a need for it . Obviously, this requires us to predict the future. We shall now look at some examples of how this prediction could be done. The key question is: What causes a need for an improvement? The answer enables us to start relevant research at the right time. In principle, the driving forces are, according to K. Cambron, president and CEO of AT&T Labs :
A) Changing demand
B) Decreasing entropy
C) Changing technology
A – Changing demand
This includes volume of traffic, but also its type, patterns, emergence of new applications. As an example, let us take a look at GoogleTech talk by Van Jacobson . Jacobson reviews the history of telecommunication networks, the success (disaster) of TCP/IP and finally argues that our current networking protocols are inadequate, because they were designed for a conversational network, where 2 people/machines talk to each other, while today over 99% of network traffic comes from a machine acquiring named chunks of data (web pages, emails). The main point is we are doing dissemination over a conversational network, which has numerous inefficiencies. That was an example of a driving force behind new networks – a change in demand.
B – Decreasing entropy
This term is used in  to describe the ability of a network to deal with new problems. Cambron argues that in order to meet new demands, changes to the network are made and “every design choice removes a degree of freedom, solving an immediate problem, but eliminating potential solutions to other problems that lie in the future”. At some point the network becomes incapable of dealing with new demands and must be replaced by a new network.
C – Changing technology
Obviously, the increasing bandwidth of core and access links has a fundamental impact on when and what QoS is needed.
2 – Deployability
The failure of QoS research to deliver a practical solution is ascribed to researchers’ lack of attention to practical issues. Most of all, it is the lack of feedback from operational networks environment (or the unwillingness of academia to interact). An excellent example of some practical problems is . Here we list some key points.
- Rift between networking operations and protocol design.
There seems to be a range of difficulties in the operational network that researchers have never heard of and therefore will not consider in their design. The list includes complexity from the configuration point of view, proneness to operator error, debugging tools, incremental deployability and so on.
- Complexity. In , G. Bell argues that IP multicast defines the limit-case for deployable complexity. Quoting ,
“Eventually, we concluded that implementing IP multicast required a substantial commitment of engineering resources, and that it would inevitably impair the stability of unicast routing due to the need for frequent OS upgrades and intrusive testing. Many enterprises do not have the mandate, or see a justification, for making this commitment.”
A good example of operational issues arising with the deployment of QoS is Davie’s 2003 paper “Deployment experience with differentiated services “.
(Network administrators will not risk destabilising their network)
“Solutions require path paved with incentives to motivate diverse agents to adopt it, implement it, use it, interface with it, or just tolerate it. Without that path you’ve wasted your time”.
The bottom line that justifies QoS research from the economic point of view is that QoS provides network operators with a means to extract value from their network by charging for different level of service . However, this mere fact does not guarantee embracement by operators and QoS research must account for all practical issues to become successful.
For an in-depth analysis of different political and socio-economic forces in the Internet, see  by D. Clark et al. and .
Note on deployability
The ease at which one can deploy an idea depends very much on the network layer in question. It is easy to deploy a novelty at the application level, but very difficult at Layer 3, and nearly impossible on layers below that. When choosing a research topic while aiming at its practical impact, one could take this dependency into consideration. (There are probably many people of the calibre of Google guys Larry Page and Sergey Brin working on lower layers, but it takes a Cisco-sized company to make a difference there.)
3 – Functionality
Researching and engineering particular mechanisms can be seen as finding the best trade-off between functionality and operational feasibility. For example, it is fairly established that the most desirable feature in the current Internet is to have some QoS notion on an end-to-end basis (i.e. from source to the destination, across domains). However, if the research community were asked what the QoS should be, there would not be a certain answer. Guaranteed performance metrics? Differentiated service? How differentiated? Simple congestion feedback?
Perhaps the answer should be: The most beneficial solution subject to time and deployability constraints.
To propose and conduct research in networking requires profound and wide understanding of the theoretical and practical constraints involved therein.
We have identified 3 critical considerations: timeliness, functionality and deployability, presenting a few points that can help in assessing them. We argued that design should maximise benefit subject to practical constraints stemming from deployability issues.
On the case of QoS research functionality on its own is only a small bit in the recipe for success. Only proposals fully respecting real-world issues have a chance to make it to the operational network.
For those not yet in a position to make judgements about its future development and the operational and economical aspects and are forced to invent a research topic (such as a PhD student with a freedom/requirement to come up with a topic), an alternative safe approach is possible:
- Choose a research area according to your interest, opportunities to contribute or instinct.
- Spend several months reading and writing simulations to obtain a profound understanding of the problem in question.
- Find a point of potential improvement and propose the improvement. From there on you can slowly start getting the whole picture, while working and contributing.
I hope this article provides some rough guidelines as to what to look out for when commencing a research project in the area of communications networks.
 Jon Crowcroft, Steven Hand, Richard Mortier, Timothy Roscoe, and Andrew Warfield. Qos’s downfall: at the bottom, or not at all! In RIPQoS ’03: Proceedings of the ACM SIGCOMM workshop on Revisiting IP QoS, pages 109–114, New York, NY, USA, 2003. ACM Press.
 G. K. Cambron. The next generation network and why we’ll never see it. Communications Magazine, IEEE, 44(10):8–10, 2006.
 Van Jacobson. A new way to look at networking, 2006. Google Tech Talks. http://video.google.com/videoplay?docid=-6972678839686672840&q=van+jacobson&pr=goog-sl.
 Gregory Bell. Failure to thrive: QoS and the culture of operational networking. In RIPQoS ’03: Proceedings of the ACM SIGCOMM workshop on Revisiting IP QoS, pages 115–120, New York, NY, USA, 2003. ACM Press.
 Bruce Davie. Deployment experience with differentiated services. In RIPQoS ’03: Proceedings of the ACM SIGCOMM workshop on Revisiting IP QoS, pages 131–136, New York, NY, USA, 2003. ACM Press.
 K. C. Claffy. Top problems of the Internet and how to help solve them, 2005. http://www.caida.org/publications/presentations/2005/topproblemsnet/topproblemsnet.pdf.
 David D. Clark, John Wroclawski, Karen R. Sollins, and Robert Braden. Tussle in cyberspace: defining tomorrow’s internet. In SIGCOMM ’02: Proceedings of the 2002 conference on Applications, technologies, architectures, and protocols for computer communications, pages 347–356, New York, NY, USA, 2002. ACM Press.
 L. Burgstahler, K. Dolzer, C. Hauser, J. Jahnert, S. Junghans, C. Macian, and W. Payer. Beyond technology: the missing pieces for qos success. In RIPQoS ’03: Proceedings of the ACM SIGCOMM workshop on Revisiting IP QoS, pages 121–130, New York, NY, USA, 2003. ACM Press.