Research and Publications: A Personal Perspective

Research and Publications:A Personal Perspective Bo Li Hong Kong University of Science and Technology Microsoft Research Asia

Outline • What about research? • How much does one have to learn? • PhD research • What is procedure of publications? • How to write technical papers?

Research is easy! • You have done this many times in course projects • Take a known problem, and apply a known technique • Obtain results, and write a report

Research is difficult! • Is it technically correct? • Does it make intuitively sense? • Is it publishable, where and why? • Does it offer some insights beyond what we have known? • Does it have any impact? • …

Research • There are basically four types of research works: • New problem and new solution • New problem and old solution • Old problem and new solution • Old problem and old solution

Research • Case I comes rarely, perhaps something you could only wish, once a life-time experience • Shannon theory • Cases II and III are the ones that you should target for • Packet scheduling: weighted fair queuing • Geographical routing in ad hoc networks • Case IV is where you can start • Plenty of out there under the category of “Yet another paper on … “

Where do ideas come from? Drink a beer, relax, ideas will come to you The ideas fall from the sky! Understanding the existing works, build upon that incrementally

Where do ideas come from? • Ideas in most cases come from the deep understanding of a subject, and possess of broad knowledge • This is not a technical training, i.e., this is not about solving a bipartite graph, or differential equations • This is about relating them to real world problems • This is about providing new insight beyond known • This is about your creativity!

Research: What is it? • Research = Re (repeat) + search • Much of the research has been built upon existing works, therefore a thorough understanding of those is the basis • Too many smart people in each area, so if an idea seems to be too good to be true, it likely is -> rethink that again • Each idea needs iterations: what is it? why has it not been done? what is the logical connection with the existing approaches?

Research: Engineering Problem • Each solution to an engineering problem is only a trade-off; it is not a cure for all, it definitely has side-effect. • Networking coding • Potential capacity gain under loaded system • Is it really? Is there any alternative? What is the penalty for doing so? Can we handle that in system design? • P2P • Facilitate the voluntary file sharing • Can this be extended beyond that?

Case I: Adaptive Video Multicast • The need for multicast - efficiency • Multiple-unicast Multicast • Fundamental problem: users’ heterogeneity and network dynamics

Case I: Adaptive Video Multicast • Layered video encoding and transmission • Cumulative layered coding (Scalable coding) • Base layer: most important feature, low rate, low quality • Enhancement layers: progressively refine quality

Case I: Adaptive Video Multicast • Existing solutions • Multiple multicast tree, each for a layer • Receiver adaptation: user’s joining and leaving groups (receiver) • Adaptation is performed at receivers only: fixed layer rates and limited num of layers • Fundamental Problem • The mismatchbetween the fixed sending rate and the dynamic and heterogeneous rate requirement from receivers

Case I: Adaptive Video Multicast

Case I: Adaptive Video Multicast • End-to-end adaptive video multicast • Optimal rate allocation for each layer: formulation and solution • End-to-end transmission protocol and whether TCP friendly • Complexity analysis • Practical issues: feedback explosion (sampling), RTT estimation (open and closed loop)

Sample References • B. Li and J. Liu, “Multi-Rate Video Multicast over the Internet: An Overview,” IEEE Network,(17)1: 24-29, January-February 2003. • J.-C. Liu, B. Li and Y.-Q. Zhang, “Adaptive Video Multicast Over the Internet,” IEEE Multimedia, (10)1: 22-33, January-March 2003. • J. Liu, B. Li, and Y.-Q. Zhang, “An End-to-End Adaptation Protocol for Layered Video Multicast Using Optimal Rate Allocation, IEEE Transactions on Multimedia, (6)7: 87-102, February 2004.

Summary • Identify a general category of problems • The idea should be intuitively simple • Publications can be “easier”

How much does one have to learn? • I have learnt all the mathematics, and I am loaded • Discrete algorithms, partial differential equations, dynamic control, probabilistic modeling, information theory and etc. • I still don’t have a clue what to do in research. • Where in the world is research topic?

How much does one have to learn? • I have read all papers out there from journals and conferences • Can I do research now? • There is no way you can cope with all of them • Majority of the published works are junks, and can cause brain damage and can be misleading

The minimum needed for research • Logical thinking, after all we are in engineering world • Basic skills • You have to know the Dijstra algorithm in order to understand the OSFP (?) • the ability to learn • Life long learning process, esp. in CS

The minimum needed for research • Abstraction. Take a problem, you have to know • What is/are the fundamental problem(s) • You have to see both “forest and trees” • What have been done, why? • What are seemingly undoable? • Understand your strength and weakness

The minimum needed for research • Open mind • We are not dealing with math problem in that there exists perfect solutions • Engineering solutions are subject to argument and debate, i.e., each solution is a trade-off, and it only works in a constrained environment • Critical mind • When you read others, it is equally important to understand what circumstance that it does not work as in which it works • If you can not identify such scenario, you are not understanding the problem

Case II: Proxy Placement • How to place the proxy (mirror sites) in the internet • B. Li et al., “On the Optimal Placement of Web Proxies in the Internet,” Proc. IEEE Infocom'99 • ACM Communications Review (2001) cited as the 1st ever work on this topic

Case II: Proxy Placement • Formulation: graph theory problem, k-median problem: given N nodes, how to select K nodes to place the content so certain optimal criterion can be met • For general graph, this is NP-hard • For tree, we solved this using a known dynamic programming technique • This turns out to be the fundamental problem for object replication in DB, which has been cited over 300 times since then

Sample References • J.-L. Xu, B. Li and D. Lee, “Placement Problems for Transparent Data Replication Proxy Services,” IEEE Journal Selected Areas in Communications, 20(7): 1383-1398, 2002 • A. Vigneron, L. Gao, M. Golin, G. Italiano and B. Li, “An Algorithm for Finding a k-Median in a Directed Tree,” Information Processing Letter, 74(1-2): 81-88, 2000 • B. Li, “Content Replication in a Distributed and Controlled Environment,” Journal of Parallel and Distributed Computing, 59(2), pp. 1-21, Nov. 1999

Summary • Finding a problem is more important, and difficult than solving a problem • You need out-of-box thinking

PhD Research • Make a plan earlier, for 3-4 years • The research topics must be of current interest, and state-of-the-art • Don’t work on packet scheduling, and IEEE 802.11 MAC protocol  • Beating the performance of Ethernet is like kicking a dead horse! • It has to be something that within your capability • You need to understand your strength and weakness, and be realistic (don’t shoot stars) • You should know your interest, self-motivation is one of the single most important factors

PhD Research • Read top 10 or 20 papers in the area • Understand the basics, fundamental problems, and open issues • Think and read • Put all papers into perspective • Start from a small yet concrete problem • Build you skill and confidence • Discussions generates ideas

Reading • Top conference or workshop first • ACM Sigcomm, ACM Mobicom, IEEE Infocom • IEEE ICNP, IWQoS, MobiHoc • Second tier conference only for reference • IEEE Globecom, ICC • Avoid bad conferences • Regional, and less reputable ones • Read journal papers only it has not been published else where, or when it contains more detailed and complete treatment

PhD Research • Focus! • Don’t over-estimate your ability • Don’t diversify too much • Start with small idea(s), publish in an easy conference in the 2nd year • Working plan: target at 2 conferences (20 or less acceptance rate) and one journal paper per year (in 2-3 years) • The thesis is a collection of the papers • So you need to have a focus!

Research Topics • Theoretical vs. practical • Can this be related to a real world problem • Engineering approach • It should have a clear boundary • Focus on what can or/and can not be done • Don’t lose the bigger picture • Tree and the forest • How does it help to solve one or more pieces in the bigger problem

PhD Research • System works • System work usually involves team efforts • Building from scratch is a dangerous thing • The prototype has to demonstrate significance in that either this is a proof of a concept, or demonstrate the feasibility • Less than 5% chance being useful, yet worth the investment for technical break through • Theoretical works • Theoretical work usually provides an elegant solution to a generalized problem • The significance can be greatly enhanced if practical insight can be drawn

Advisor/Mentor • Choosing an advisor could be the single most important factor for your research • Understanding the general problem, the ability to identify the significance and yet another • Personal and professional relationship • Junior vs. senior, hands-on or hands-off • Regular guidance vs. direction • Independent and close collaboration • Group or individual effort • Time, efforts and experience

You really need an Advisor/Mentor • Can a rabbit eat a dog, fox and wolf?

You really need an Advisor/Mentor • Punch line It really does not matter what the topic is, and what you are doing, all it matters is who your advisor is

Example I: My PhD research • What you need is a jump start for confidence building • A. Ganz and B. Li “Performance of Packet Networks in Satellite Clusters,” IEEE Journal on Selected Areas in Communications, (10)6: 1012-1019, August 1992 • Be objective, don’t lose the bigger picture • The research topics are both important and not so important • The research works in PhD study is simply a training process, be realistic. • Usually the most productive period for one’s career is within the 5 years’ after one’s PhD

Example II: My student • Jiangchuan Liu • Who has written close to 20 top journal papers since 1999, largely on video multicast • Assistant Professor at Simon Fraser Univ., former with Chinese Univ. of Hong Kong. • Won the prestigious Hong Kong Young Scientist award in 2003, given to one individual annually by Hong Kong Institute of Science (HKIS) • Sometime direction is all a student needs

Collaborations leads to Productivity • Working with the right people • Skill complementary • Same interests • Working with smart people

Case III: Cellular Networks 7 3 1 6 4 1 4 5 5 2 7 7 3 1 3 1 6 6 4 1 4 5 2 2 7 1 3 1 6 4 Frequency Reuse Pattern for N=7 Number of cells per cluster: Frequency Reuse Factor, If total of S channels available, Each cell can be assigned k channel If M clusters within the system, the total system capacity:

Case III: Cellular Network • There were several fundamental problems in cellular network when moving to multi-service environment • Bandwidth within a cell have to be shared • Erlang assumption (Poisson arrival and exponential sojourn time and exponential call duration time) fails due to data traffic • Gaussian approximation for a cell capacity fails given the cell is small …

Case III: Cellular Network • Relaxing Erlang, by considering heavy tail long range dependency LRD) distribution, i.e., Pareto distribution • Failed since 1997

Case III: Cellular Network • Gaussian approximation • Particle movement and diffusion equation • S. Wu, K. Y. M. Wong and B. Li, “A Dynamic Call Admission Policy with Precision QoS Guarantee Using Stochastic Control for Mobile Wireless Networks,” IEEE/ACM Transactions on Networking, (10)2: 257-271, April 2002.

Summary • Working on hard and open problems • Persistence pays off

Summary • The idea has to be simple, this is a hard lessen we have learn • 10 years of research on ATM are pretty much a waste • Internet • POTS or PSTN

Conference Paper • Start earlier for a conference submission • Deadline is the best drive for making progress • What make a good paper: content and writing! • Clear, convincing, simple and good English • This is a never-ending optimization process, do this within the time and page limits • Review process 5/30 rule • 5 minutes - Abstract, introduction, figure and conclusion • 30 minutes – understand 90% of the paper

Journal Paper • A good conference paper (10%-25% acceptance rate) can be submitted to a journal, with 30% new results • Report more complete and focused results • Give yourself a deadline • Be patient with the long review and re-review • At the earlier stage of one’s career, don’t quit if asked for major revision • But don’t do seemingly impossible

What does a reviewer look for • New problem or new solution? • Are the main results significant? • Is the paper technically correct? • Does the paper provide a fair assessment of its strength and limitation? • Is the paper clearly written, thus accessible to general readers? • Are the references adequate? • Is the paper appropriate for conference/journal? • …

Research and Publications: A Personal Perspective