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  • Information for Authors | acm sigcomm
    An extended submission policy appears in the SIGCOMM FAQ and describes how to submit and review a conference version of a workshop paper ACM has defined policies on double submission as well as plagiarism and self plagiarism Upcoming Deadlines ACM Internet Measurement Conference 2016 Los Angeles California USA http conferences sigcomm org imc 2016 index html Abstract Registration Deadline 5 May 2016 Paper Submission Deadline 12 May 2016 Dates 31

    Original URL path: http://sigcomm.org/for-authors?destination=node%2F183 (2016-04-25)
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  • SIGCOMM Education Blog | acm sigcomm
    on I got several interesting questions about the latter both during the talk and in the weeks following the talk Given this I thought I would devote this column and perhaps parts of future columns to putting my ideas on problem selection into words I suspect what I write below will generate more questions than answers in your mind Don t hold your questions back though Write to me at guru sigcomm org BIN problems I like to work on BIN problems which are research problems that are B ig in scope I mportant in terms of their potential for intellectual or practical impact and N ebulous in terms of how to approach them It is hard to precisely define BIN problems but here are examples of BIN problems that I worked on that may give you a sense of what I m talking about How to design an evolvable Internet architecture How to model and mitigate network complexity And how to exercise software defined control over network functions Why am I attracted to BIN problems Pick one of the examples above say control over network functions NFs The scope is Big different networks use different subsets of NFs and there are many different kinds of NFs out there The problem appears Important the industry is starting to think about this From a research standpoint there appear to be few studies that offer systematic answers Thus the potential for impact on both practice and research exists The Big ness of scope and the Nebulous ness of approach mean naturally that the field is wide open i e there is no immediately obvious answer here There are many places to start approaching this problem and many potential ideas issues to consider For example do we simply control routing to NFs Does it make sense to control internal state How about dynamic context NF logic Algorithms How to deal with NF diversity I hope this example gives you a sense as to why I think BIN problems are so cool they keep your mind constantly jogging And if you succeed the pay off can be huge In what follows I will try to address two questions that may arise regarding such problems Are BIN problems risky Some of you may wonder if this is too much to take up Where do you start Which thread s do you explore first What if your exploration fails It may also be the case that the BIN problem you picked doesn t seem hot this isn t exactly true for network functions there s a lot of buzz surrounding them these days but this concern may arise more naturally for other topics such as network complexity or the Internet s evolvability I would argue that the situation is quite the contrary First note that once you ve picked a reasonable starting point control over internal NF state in the example above you ve rooted a version of the problem and this immediately makes things less vague From this point on it is like any other research problem in terms of the likelihood of finding something tangible But the I mportance aspect means that whatever you find has a big likelihood of having impact The impact could be intellectual in nature your work could spur others to build similar perhaps better systems but your system will be the first Or you may hit the nail on its head right away in which case you could directly impact practice As you explore things may turn out to be not what you started out hoping for But the thing about BIN problems is that there s enough room for refinement e g maybe you started out by casting too wide a net around NFs and your initial experience taught you that focusing on say distributed control across multiple copies of an NF is still Big and Important and now it s also less Nebulous Finally BIN problems naturally lead to bodies of work The many threads to explore at each starting point and the different potential starting points themselves often map on to distinct but related research projects problems In depth exploration of one particular starting point and associated threads often gives you enough context to explore in a more focused fashion other starting points and associated threads How to work on BIN problems Crucially as a student how do you know something is Important Also you may not be able to judge if the scope is Big enough or perhaps it too Big And related to this is the question of whether your problem statement is clear enough for you to start coming up with meaningful solutions You don t have to fight these battles alone Working on BIN problems is not something you could or would want to do sitting behind locked doors To clarify scope and to pin down a problem statement I strongly encourage you to talk to your advisor about your idea in case you haven t noticed advisors love to hear bold and fresh ideas from you more than having you simply do what you are told Talk to others in your research group including both professors and students Then talk to others in the broader networking area perhaps when you bump into them at conferences also consider inviting yourself to go give a talk some place and chat 1 on 1 with people there about your BIN idea your advisor could be of help in setting up such a rendezvous In particular talking to practitioners is quite valuable here and this set includes your local campus network operators researchers at industry research labs engineers at major online service providers etc The initial reaction you get may make you feel like you are wasting your time I have in the past had people tell me I was crazy to work on something or that what I was working on was not relevant But this is actually constructive feedback in the sense that what may be happening is that your pitch for the problem needs refinement Go back to your notepad and come up with a better framing of your problem And then repeat the process above Approaching BIN problems doesn t necessarily have to be top down i e you don t have to start with a BIN problem Often you may find yourself working on a concrete and interesting problem Perhaps you have a couple of papers on that already It is a good idea to stop there and ask Is the scope of what I am working on bigger than what I ve looked at in my 1 2 papers so far And you should be open to the fact that broadening the scope may require a different approach one that is necessarily nebulous at the beginning than what you re currently exploring Working on BIN problems can take time In particular getting the right initial intuition nailed down could take a year perhaps more All the things I mentioned above talking to people gathering feedback going back to the notepad can appear to drag things out too But once you have the right intuition and given the experience you ve gathered along the way you re going to be unstoppable References 1 On future proofing networks http www cs wisc edu akella talks conext keynote web pptx Guru s Column Various Student Questions Posted on 2015 12 04 11 28 by admin ACM SIGCOMM Student Mentoring Column Aditya Akella UW Madison Topic Various Student Questions I ve received several interesting and varied questions from students all over the world Thank you for the warm response In this issue I have hand picked a small subset of questions to answer Many thanks to Brighten Godfrey UIUC and Vyas Sekar CMU for contributing their thoughts Do write to me with more questions or follow on questions to the ones below Job search related Question Say I am starting a company after my graduation And assuming that my company has failed or has been acquired by another company will my startup acquisition failure have any negative impact on academic industrial positions later Answer Brighten Godfrey One of the most important steps to succeeding at research is learning that repeated failure is part of the natural process of doing risky work Experiments don t turn out as expected good papers are rejected start ups fizzle As a result in general you will be measured more by the most impactful successes you have than by failures That said there is often a disadvantage to taking time off from academia there s a gap in your publication record your research looks a bit older and so on In some cases a startup could be viewed less as a gap and more as a positive extension of your research for example if the startup was based on your work Q After Ph D the highest academic job one could get is a tenure track professorship And most advisors help gear graduates for that end If one could not get a tenure track professorship the next closest academic position is a teaching professorship assuming that the candidate has interests in teaching What are the other possible academic positions that fall between a research and a teaching professorship with no tenure grant overheads from the former and minimal no teaching load from the latter A Aditya Akella Vyas Sekar The answer depends on which country you are considering as the overall system and framework for tenure track research faculty can vary quite significantly In the USA many academic institutions have non tenure track research scientist positions also called by other names such as research professors or research associates Such positions don t generally have mandatory teaching obligations although many research scientists do take up modest teaching loads However grant writing is a big part as research scientists are generally expected to raise money to support their research programs and themselves In other words most academic jobs require you to do at least two things out of research teaching and grant writing Paper writing related Q What is the most important section of a submission say to Sigcomm I e Is there a particular section I should pay attention to spend most time writing A Aditya All sections of a paper are important Each section adds a different facet to a paper s overall contribution That said as a reviewer I tend to look for a strong motivation section This is usually section 2 of the paper A good motivation section clearly states the problem using compelling examples and data to motivate why the problem is relevant important and why it is hard It also sets out requirements for the solution highlights challenges in designing the solution and puts the paper s claims in the context of related work Thus it is totally worthwhile to spend time framing polishing this section Q I have a paper that has been rejected multiple times Should I give up on it or send to a lower tier venue A Brighten That s a tough question Sometimes you know there s something good there and even at a somewhat lower profile venue it can get noticed Other times you Arxiv it and move on to your next great idea But is there perhaps a third option that even after you have seen and understood the feedback from reviewers you still believe the work is impactful enough for a top venue A paper that I consider one of the most important of my career so far was rejected four times before being accepted at a top venue on the fifth submission That can only happen if the authors and especially the leading PhD student really believe in the vision and persist in improving the work Q A recent program committee commented that I needed to evaluate my idea using more realistic traces My work is theoretical in nature and I have proved strong theoretical guarantees backed by a small set of experiments on a real prototype using toy workloads What additional value do experiments with realistic workloads add A Brighten Aditya At a conference like SIGCOMM or NSDI this reflects the taste of the community to see real artifacts whereas a conference like SPAA or PODC might be open to work where the contribution is foundational theory Realistic workloads answer different questions than theoretical analysis A strong theorem may bound performance in the worst case or it may show expected performance under certain assumptions about the operating environment A real prototype system evaluated with realistic workloads can demonstrate performance in typical cases that people actually care about in the real world Crucially it can show that the system building and other operational difficulties that inevitably arise but don t always appear in a theoretical model don t invalidate the main insight result Q How does one write a good introduction abstract for a paper A Vyas Aditya I don t think there is one good answer and it depends both on the type of paper e g measurement vs algorithm vs position paper and the person writing it We evolve and develop an individual style of writing a good introduction in terms of both the language and presentation That being said a good introduction should generally answer the following questions paraphrasing Jim Kurose s advice http www net cs umass edu kurose writing intro style html 1 Why is the problem important 2 What was challenging in solving the problem and or why did prior work fall short 3 What was your key insight and why is it interesting 4 What are the main punchlines in terms of system algorithm performance that advances the status quo Crucially you need to keep practicing your writing Don t leave the part of writing up the abstract introduction to your advisor draft it yourself You will eventually become great at churning out perfect introductory sections Ph D Advice on Managing Your Advisor from greatresearch org Posted on 2013 09 01 21 21 by Anonymous Hello Everyone Hamed Haddadi the Information Service Director for SIGCOMM has found some of my posts over at How to Do Great Research quite worthwhile to read and has suggested that I cross post some of the content on the SIGCOMM blog I ll point you over to the blog for the full content but I ve posted a teaser below The genesis of the blog is a course for incoming Ph D students that Professor Alex Gray and I designed at Georgia Tech and have been teaching for more than five years To our surprise a lot of helpful information on the Ph D is out there but it s not really consolidated in one place We began collecting helpful information and filling in the gaps with our own material this fall as much of the material has coalesced I am putting the material into written form on a blog You ll be able to read posts such as the one below throughout the fall term I expect the flood of posts this fall may become a trickle in the future but hopefully once the initial information is seeded we ll also enrich the information we have with guest posts The course has a variety of twists and turns that we devised such as assignments to generate cross disciplinary ideas time management exercises a mock program committee etc If anyone is interested in more of the course materials or wants to talk to me more about this concept I m all ears Thanks and happy reading Nick Feamster Managing Your Advisor cross posted from How to Do Great Research With the new academic term almost upon us several of my students started to put together a list of practical advice for incoming students including various niceties such as how to gain access to the lab how to get accounts how to submit reimbursements and so forth I wanted to contribute to the list of advice and I figured I could offer some value by giving advice to new students about how to gain traction on their research as quickly as possible This post is the first in a series of a few posts on that topic in this post I will cover the topic of managing your advisor The notion of an advisor is an interesting concept for many new Ph D students Incoming graduate students typically have one of two backgrounds some come straight from undergraduate studies and hence may have never had a manager or a boss overseeing their career others have spent some time in the workforce and have decided to return to the university and begin a career in research and hence have some notion of what it is like to have a manager An advisor student relationship is unique though and will be a new experience for both types of incoming students The relationship is similar to a manager relationship but has several differentiating features First your advisor is often a collaborator on equal footing Although an incoming Ph D student is not yet a peer of his or her advisor the goal is that by the end of the Ph D process the student and advisor will be peers In this sense the Ph D is a true apprenticeship My students don t work for me they work with me Second your advisor is not a manager in the strict sense but is literally an advisor You are in control of shaping your own graduate career from what you choose to work on to who you work with Your advisor should be a catalyst and facilitator for your success and should not be treating you as an employee or hired labor Although some research contracts have deliverables you should be suspicious of any advisor who wants to constantly hold you to tight deliverables as it will constrain your autonomy and creativity that type of advisor will

    Original URL path: http://sigcomm.org/blogs/education (2016-04-25)
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  • Guru's column: ACM SIGCOMM Student Mentoring Column | acm sigcomm
    depends on the outcome of this discussion and not directly on the scores in the reviews and the discussion may change a reviewer s opinion of a paper in either direction Often but not always reviewers update their reviews if the discussion changes their opinions For papers that made it to discussion authors are often provided with a discussion summary This summary may be the best signal for what determined the paper s fate So read the summary carefully Now back to the question Note that rejections happen routinely to the best researchers among us A key reason is that most top conferences reject over 80 of their submissions as there is often limited room in the program Realize that not all venues use the same scoring scale and even those that use the same scales have very different submission pools Importantly scores are only part of the equation on what papers ultimately get accepted into the program High scores from one or two reviewers may indicate niche excitement about the paper but the paper also needs to be calibrated on other fronts and there are really multiple dimensions to this For example relative excitement with respect to other papers in play whether there is someone championing the paper or the high scores are just lukewarm the expertise of the reviewers how many papers the conference is willing to accept within a reasonable program etc Don t get hung up on the scores It is often important try to debug what happened and understand why the paper was rejected Be brutally honest with yourself are the scores high or are they a mixed bag or even just middling Crucially does your approach have an Achillies heel that a reviewer called out Or is there just limited excitement about the problem you re solving In the former case armor yourself against the objection considering whether to do this right up front in the introduction later in the design section or elsewhere in related work Ask your advisor for help armoring yourself against technical limitations or related work if you re unsure In the latter case think about other applications of your approach and consider proposing them right up front in the introduction Take the positive feedback as encouragement take reviewer concerns seriously instead of dismissing them and try and push it over the bar the next time Q What do you look for in a paper to accept reject it A There s broad consensus in our community that choice of problem is a key factor That is to say is the problem that you ve chosen to work on timely pertinent to application to the field and intellectually deep It is important to orient your writing to highlight these aspects After that we are looking for the quantum of contribution to knowledge that your submission contributes The goal of research is to expand our body of knowledge and so we are judging your paper on how effectively it does just

    Original URL path: http://sigcomm.org/content/gurus-column-acm-sigcomm-student-mentoring-column (2016-04-25)
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  • Guru's Column: Various Student Questions | acm sigcomm
    reading it For instance if you are reviewing for a conference journal you really need to do an in depth read during the third pass The same applies if you are planning to work in the same general area as the paper or if the paper is highly relevant to your current work In both cases it may also help to take detailed notes and jot down your thoughts critiques during the in depth pass This may seem onerous at the beginning but over time you will notice that you re getting very efficient with each pass taking lesser time On the other hand if you are doing a quick survey to understand the state of art then you may do only the first second passes Generally speaking the only way to become more efficient at something is practice So read as many papers as you possibly can A Few More Publication related Questions This appears to be a popular topic with many different questions I ve attempted to address a handful of them below and will return to the others in future columns Q Is X a good venue to publish at A The student had actually asked about a specific X which I decided to anonymize the purpose of this column is not to answer questions about particular venues but to offer general advice To that point here is a general set of guidelines in choosing what conference venues to publish in Are the leading researchers in your field publishing at this venue Look at prior years programs to understand this How visible impactful are papers at this venue Are these papers cited a lot Lookup papers published at the venue over the past 2 3 years in Google Scholar Were some of the seminal papers in your field published here Are these papers you d put on your must read list Do your peers advisor publish or want to publish here It doesn t hurt to ask directly Is the PC composed of well recognized members of the community e g people whose papers you read In addition to hinting at the quality of reviews and feedback you would get this also tells you whether the venue will be well attended and by relevant folks because in most cases members of the PC do submit to and attend the conference Q Why do networking conferences seem to go through these fads every few years multicast DHTs peer to peer datacenter networking and now SDN A Hey don t leave out quality of service ad hoc networking and the Internet of Things But seriously this happens in most fields of research and technology not just networking Hence the hype cycle 8 In general these things are also driven by where the industry is headed or most focused technology trends as well as funding agencies areas of priority If you want to know what these hot topics are at the moment there are a few different sources you can

    Original URL path: http://sigcomm.org/content/gurus-column-various-student-questions (2016-04-25)
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  • Guru's Column: BIN Problems | acm sigcomm
    NF diversity I hope this example gives you a sense as to why I think BIN problems are so cool they keep your mind constantly jogging And if you succeed the pay off can be huge In what follows I will try to address two questions that may arise regarding such problems Are BIN problems risky Some of you may wonder if this is too much to take up Where do you start Which thread s do you explore first What if your exploration fails It may also be the case that the BIN problem you picked doesn t seem hot this isn t exactly true for network functions there s a lot of buzz surrounding them these days but this concern may arise more naturally for other topics such as network complexity or the Internet s evolvability I would argue that the situation is quite the contrary First note that once you ve picked a reasonable starting point control over internal NF state in the example above you ve rooted a version of the problem and this immediately makes things less vague From this point on it is like any other research problem in terms of the likelihood of finding something tangible But the I mportance aspect means that whatever you find has a big likelihood of having impact The impact could be intellectual in nature your work could spur others to build similar perhaps better systems but your system will be the first Or you may hit the nail on its head right away in which case you could directly impact practice As you explore things may turn out to be not what you started out hoping for But the thing about BIN problems is that there s enough room for refinement e g maybe you started out by casting too wide a net around NFs and your initial experience taught you that focusing on say distributed control across multiple copies of an NF is still Big and Important and now it s also less Nebulous Finally BIN problems naturally lead to bodies of work The many threads to explore at each starting point and the different potential starting points themselves often map on to distinct but related research projects problems In depth exploration of one particular starting point and associated threads often gives you enough context to explore in a more focused fashion other starting points and associated threads How to work on BIN problems Crucially as a student how do you know something is Important Also you may not be able to judge if the scope is Big enough or perhaps it too Big And related to this is the question of whether your problem statement is clear enough for you to start coming up with meaningful solutions You don t have to fight these battles alone Working on BIN problems is not something you could or would want to do sitting behind locked doors To clarify scope and to pin down a problem statement I

    Original URL path: http://sigcomm.org/content/gurus-corner-bin-problems (2016-04-25)
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  • Guru's Column: Various Student Questions | acm sigcomm
    closest academic position is a teaching professorship assuming that the candidate has interests in teaching What are the other possible academic positions that fall between a research and a teaching professorship with no tenure grant overheads from the former and minimal no teaching load from the latter A Aditya Akella Vyas Sekar The answer depends on which country you are considering as the overall system and framework for tenure track research faculty can vary quite significantly In the USA many academic institutions have non tenure track research scientist positions also called by other names such as research professors or research associates Such positions don t generally have mandatory teaching obligations although many research scientists do take up modest teaching loads However grant writing is a big part as research scientists are generally expected to raise money to support their research programs and themselves In other words most academic jobs require you to do at least two things out of research teaching and grant writing Paper writing related Q What is the most important section of a submission say to Sigcomm I e Is there a particular section I should pay attention to spend most time writing A Aditya All sections of a paper are important Each section adds a different facet to a paper s overall contribution That said as a reviewer I tend to look for a strong motivation section This is usually section 2 of the paper A good motivation section clearly states the problem using compelling examples and data to motivate why the problem is relevant important and why it is hard It also sets out requirements for the solution highlights challenges in designing the solution and puts the paper s claims in the context of related work Thus it is totally worthwhile to spend time framing polishing this section Q I have a paper that has been rejected multiple times Should I give up on it or send to a lower tier venue A Brighten That s a tough question Sometimes you know there s something good there and even at a somewhat lower profile venue it can get noticed Other times you Arxiv it and move on to your next great idea But is there perhaps a third option that even after you have seen and understood the feedback from reviewers you still believe the work is impactful enough for a top venue A paper that I consider one of the most important of my career so far was rejected four times before being accepted at a top venue on the fifth submission That can only happen if the authors and especially the leading PhD student really believe in the vision and persist in improving the work Q A recent program committee commented that I needed to evaluate my idea using more realistic traces My work is theoretical in nature and I have proved strong theoretical guarantees backed by a small set of experiments on a real prototype using toy workloads What additional value do

    Original URL path: http://sigcomm.org/content/gurus-corner-various-student-questions (2016-04-25)
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  • Ph.D. Advice on "Managing Your Advisor" (from greatresearch.org) | acm sigcomm
    the point below on making meetings count Scheduling meetings sometimes can generate an explosion of email this is a recipe for disaster and ensuring that you never get to meet your advisor see below on email if scheduling is proceeding slowly limit the email thread to 1 2 emails before suggesting a meeting invitation by Google calendar If all else fails send a meeting invitation during an open slot in the worst case your advisor will react by moving it to a time that works it is on the calendar and thus can no longer be deferred indefinitely Try to meet your advisor once a week even if you think you have nothing to talk about Make an effort to schedule a meeting once a week even if the meeting is short in my experience I have found that sometimes even a ten minute meeting with a student can make a huge difference for working around a mental block or changing an approach to a problem Do not assume that a meeting cannot happen simply because your advisor is not in town Short meetings by Google hangout are often very handy In fact throughout the summer of 2013 I was rarely at Georgia Tech many of my students actually found it easier to meet me when I was traveling because I wasn t being constantly bombarded by things related to the daily drumbeat at the university e g committee meetings interruptions from admins teaching etc Consider having a meeting even if you think there s nothing to report You may find you are stuck in a rathole and you may not even realize it You should be particularly worried if you have spent 2 3 weeks debugging or on some implementation without getting any feedback Chances are you are ratholing on something that probably isn t getting you any closer to a publication Seek help immediately Attend every single group meeting Do not miss group meetings These are one of the most important structural elements of your graduate career that actually relates to your research Group meetings are important for several reasons 1 You learn about what others in the group are doing which may be a useful resource or you may find out you can be a resource to someone else This all helps with collaborating across the group 2 You find out what your advisor has been up to and why he or she has not been replying to your emails immediately 3 You can quickly identify if you need to have a longer meeting with your advisor with other students in the group etc This can be a huge timesaver 4 Group meetings mark the passage of time It is useful to hold yourself accountable and make sure that weeks and months don t slip away without progress I have group meetings with my students three times a week initially I thought that this might be excessive but it turns out to work pretty well Three short group meetings can often be a lot better than one extended group meeting I will expand on this more in a later post If you need more of your advisor s time ask for it Students are often confused or concerned that an advisor spends more time with some students than with others and may even wrongly think that the advisor is either less excited about a particular project or worse doesn t like some students as much as others I remember comparing notes with my fellow Ph D students in grad school about how much time our advisor was spending with each of us Yet it is important to remember that good advisors don t play favorites The time that an advisor spends with a student or on a project is typically determined by the advisor s perception of how much time is needed the required time can vary dramatically according to both the stage of the project and the stage of the student s development Students who are early in their careers typically need and should be asking for a lot of guidance and closed loop feedback Students who are close to graduating also tend to need more attention of a different sort help with building their professional network seeking out job prospects practicing job talks and generally landing on their feet Similarly nascent research projects or projects with substantial coordination components e g large systems building efforts often need a lot of advisor attention since they have lots of moving parts and can involve coordination between multiple sub projects and students Do not be overly concerned about strict time accounting If you feel you need more time simply ask for it or better yet just try to take more time walk into your advisor s office approach him or her on IM send regular email updates whatever it takes Advisors tend to spend more time with students who demand more of their time Keep your emails short and to the point Here is a simple rule of thumb If the email is longer than one paragraph it probably won t get read right away particularly if there is no summary at the beginning of it It almost certainly won t get an immediate response Additionally consider whether email is the fastest way to resolve something or whether it s quicker to have a 5 10 minute meeting hangout IM chat phone call or whatever Use the right communication mode for the job Do not assume that if your email doesn t get a reply it hasn t been read I read everything in my inbox almost always on the same day that it arrives Unfortunately I also receive 300 500 emails per day in my inbox not mailing lists many of which are actionable Suppose that half of those emails required action and that each one required one minute to process and respond to that s already six or seven hours a day just to process email

    Original URL path: http://sigcomm.org/content/managing-your-advisor-greatresearchorg (2016-04-25)
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  • User account | acm sigcomm
    Attendees Conference Organizers Tweets by ACMSIGCOMM User account Log in Request new password Username Enter your acm sigcomm username Password Enter the password that accompanies your username Contact us to send feedback about this page Fatal error Call to undefined

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