Essays

Bubbles

2009-02-19T09:59:00.001-05:00

We are living in the worst economic times since the 1930s. The US economy contracted at an annualized rate of 3.8% in the fourth quarter of 2008, the corresponding figure for Japan is 12.7%, and Iceland may become the first post-depression Western economy to suffer from an outright fiscal collapse. Economists tell us that one of the reasons for this worldwide recession is a 'housing bubble' where banks overestimated a borrower's ability to pay back a loan and where house buyers--armed with cheap loans--overestimated the true worth of a house.

The recent Internet bubble is still fresh in some of our minds, where there was a similar overestimation of the true worth of Internet-enabled businesses. That bubble crashed too, with consequences suffered by the entire economy.

Unfortunately, bubbles are not uncommon in networking research. Certain topics appear seemingly from nowhere, become 'hot,' propelled by interest from both leading researchers and funding agencies, and just as mysteriously die off, leaving behind a flood of papers, mostly in second- and third-tier conferences, written by authors only too keen to jump on a trend. Bubbles lead to an overexpenditure of research effort on marginal topics, wasting resources and breeding a certain degree of cynicism amongst our brightest young minds. Moreover, they drain resources from more deserving but less hyped ventures. Can our experience with economic bubbles shed light on research bubbles and teach us how to avoid them?

Both economic and research bubbles share some similarities, such as having unrealistic expectations about what can be achieved by a company, the real-estate market, or a new technology. Bubble participants either naively or cynically invest time and money in solutions and technologies whose success is far from assured and whose widespread adoption would require the complete overthrow of legacy infrastructure. To avoid being caught in a bubble, or to merely avoid being caught in the tail end of one (being at the leading edge of a bubble is both fun and profitable!), ask tough questions about the underlying assumptions. In the midst of the housing bubble, could one point out housing prices could down as easily as they could go up? Could anyone have believed in the '90s that videoconferencing, ATM, RSVP and other 'hot' topics would soon be consigned to the midden heap of history? I think so. It only requires the willingness to question every assumption and draw the inevitable conclusions.

I think that in the end, what really inflates a bubble is money. Cheap money from venture capitalists, banks, and funding agencies makes it profitable to enter a bubble and make it grow. So it is important that the gatekeepers of funding be vigilant. They should be prepared to turn down applications for funding that smack of riding the bubble. Experienced researchers should willingly serve on grant panels, then should be prepared to be critical with even their favourite areas of research if necessary.

Finally, bubbles can be identified and quashed by an active media. The press should have more deeply questioned the Internet and housing bubbles. Research conferences in our field should do the same for research bubbles. Paper reviewers and program committees thus play the same role as investigative journalists.

This is not to say that all speculative ideas should be systematically de-funded and rejected. There should always be room for open-minded, blue-sky research. However, this activity should be limited and clearly identified. Perhaps every conference should have blue-sky sessions where all assumptions are left unchallenged (our community has done this with recent papers on 'clean-slate' designs). The best of these ideas, when proven to be sound, could then be funded and widely adopted.

Of course, I am assuming that that we can get out of bubbles by rational means. Humans are all too fallible, however, and bubble thinking plays on human foibles. Worse, there is an incentive structure that encourages bubble formation: people at the leading edge of a bubble are disproportionately rewarded and people at the tail end can point to large body of literature (emerging from top-ranked places!) to justify their work, which reduces their cognitive effort. So, bubbles may be here to stay.

Nevertheless, given the destructive effects of bubbles over the long term, I suggest that we look out for them, deflating them before they deflate us!

An Occam's Razor for System Design

2008-07-25T13:45:00.000-04:00

Occam's Razor states: "All other things being equal, the simplest solution is the best." Stated differently, it asks us to find the simplest theory that fits the facts. Of course, the metric for simplicity is unstated, but presumably it is apparent to the perceptive mind.

I have been thinking that a variant of Occam's razor ought to be applied to systems design. Any design tries to meet some goals given some assumptions. Setting aside poor designs, which do not bother to articulate either the goals or the assumptions, lets consider those designs which try to achieve the same goals. My reading of Occam's razor then advocates the design that makes the least assumptions. This is related to the network tenet "Be tolerant in what you receive and conservative in what you send." By being tolerant of inputs, the system is less fragile, and therefore less dependent on assumptions about the input.

When comparing two solutions that both achieve the same goals, and make the same assumptions, we should choose the simpler solution. But what does simplicity mean? Is there a metric of complexity?

Now, in the area of algorithm design, the notion of time (or space) complexity is well understood. We consider the asymptotic limit on the execution time as the size of the input grows. This assumes, of course, that all problems can be made as large as necessary.

This notion of asymptotic complexity is not relevant for many system designs. Real systems are bounded. You do not need to show humans videos faster than 30 frames a second, for instance, and you do not need to build a system that deals with more than, say, 12 billion cell phones. So, in this sense, asymptotic limits are meaningless. But then, what is the replacement for time complexity?

I can offer two alternatives.

The first alternative is the implementation and testing time. Given two systems, you should prefer one that can be built faster. If you have a set of building blocks that permit assembly of complex structures rapidly, so much the better. This is the reason why Unix succeeded. Cheap processes, pipes, and scripting allow rapid construction of complex applications. From that perspective, an application constructed from Unix pipes (what you would call a 'mashup' today), is the 'simplest' even if the underlying primitives themselves are complex. In the same way, given the ease of database integration these days, even the use of a complex database like postgres can be thought to be 'simple'.

The second alternative is the amount of shared state. Shared state necessiates communication for maintaining state consistency. Moreover, discrepancies in shared state are at the root of almost all bugs in distributed systems. Therefore, the complexity of a distributed system, which is to say, nearly all systems today, can be measured in terms of the amount of shared state. More precisely, we can multiply the bytes of shared state with the number of nodes that need this state (or perhaps, given n nodes n^2 or n log(n)) and call this the complexity of the system.

Both measures are approximate, and not necessarily always applicable, but represent at least a first step in measuring the complexity of today's distributed systems. Thus, they would allow us to practically implement Occam's razor.

As another first step, it may be a good idea for system designers to justify their work using Occam's razor. They would need to show that their system is the most parsimonious one, using one the two metrics above, or something equivalent. Hopefully, this will automatically rule out overly baroque designs.

Do rural communities need computing and communication?

2006-11-16T20:36:00.000-05:00

It is not obvious at first glance that rural communities need any digital technologies, let alone cutting-edge research in an esoteric area of computer networking. As many people have pointed out, why would a villager suffering from malaria and malnutrition, illiterate, and perhaps jobless, care about sending email from a WiFi-enabled smartphone? Does this make any sense?

Superficially, there is no connection between high technology and rural development. However, if one digs deeper, a surprising connection shows up. This has to do with the reasons why rural communities are poor in the first place. The villager is poor because he or she does not have skills for which the global market is willing to pay for. Without money, food is scarce, and with hunger, opportunistic diseases take their toll. Of course, exploitative social structures and blind tradition have their role to play as well. Nevertheless, it appears that, given the wealth of capital and technologies in the world today, the only reason for poverty is the lack of efficient and affordable information flows.

By information flows, I mean the transfer of knowledge (what something is) and expertise (how to do something) among the communicating parties. Information flows can be in the form of books, radio and TV broadcasts, or email. We can classify these into traditional and digital information flows. Traditional flows are coarse-grain: what is broadcast to a mass audience is not customized to the recipient. Therefore, it is likely to be less effective than customized communication. For instance, a TV program that goes through every possible crop disease doesn't really help a farmer who wants to know about a specific disease. A second problem with traditional technologies is that they are one-way. You can read a book, but you can't reply to the author. Third, traditional technologies are not democratic. Access to the content creation is guarded by many guardians: editors of newspapers, book publishers, and TV station owners. Finally, many traditional technologies are relatively slow. It takes months or years for a book to be produced; TV and radio are much more immediate, of course.

In contrast, modern digital communications, and the information flows then support, are fine-grained, two-way, democratic, and rapid. These attributes allow them to be affordable, robust, and efficient conduits for information flows. We believe that these flows can break the chains of poverty rapidly and discontinuously. Why so?

Access to information is closely tied to productivity, that is, the use of skills to produce goods or services. The greater a worker's productivity, the better he or she is paid. A web-designer sitting in a village can make ten times the income of a daily-wage laborer. A farmer who knows when to water his crop, based on satellite information, is able to better husband his resources, and grow more.

Access to information removes information arbitrage due to traditional asymmetries. A farmer who knows the price of cotton in the futures market in the Chicago stock exchange can make rational economic decisions.

Access to information improves governance. The two biggest problems with governance in the third world are monitoring and enforcement. Government hands out money for 'development', but neither the government nor the taxpayers know where the money went. The billions of dollars that went into food aid programs have most likely ended up in Swiss bank accounts!

Access to information can break the hold of millenia of superstitious thinking.

In short, the provision of appropriate information flows is, to my mind, the basis of a fundamental change in the material and social circumstances of the developing world.

This, then, is the goal of my research: to use the ideas of tetherless communication to provide affordable and effective information flows, and to carry my ideas through to the field.

Against travel

2006-09-11T20:53:00.000-04:00

I have been traveling quite a bit this year, and I am sick of it. So sick, that I want to organize my thoughts on why I am against travel.

Not that all travel is bad, mind you. Some travel is unavoidable, such as for medical treatment, to deliver goods, or to visit close relatives. What I am talking about is discretionary travel, and, in particular, discretionary business travel. This is for meetings, conferences, and retreats, where the purpose is to go somewhere, meet a bunch of people, talk until late at night, sleep little, and then go home tired. This sort of travel is not strictly necessary, and, as I argue below, can actually be bad. There is also the entire category of leisure travel, which I am not discussing at all, though I suspect this category is dying a natural death, with the restrictions on air travel, the high cost of fuel, and the growing trend of cocooning.

Before I launch into my reasons why travel is bad, let me first say why travel is good. Travel, as the cliche goes, expands the mind. It lets people see new ways of doing things, and, the juxtaposition of the new with the old often stimulates thinking. Moreover, there is much to be said for face-to-face contact. Even computer networking researchers, who are more cyber-linked than most, get something out of a face-to-face conversation that email and voice communication do not provide.

Yet, despite these positives, one aspect of the world has changed, which makes the negatives, which I will describe next, outweigh the positives. And this is the rise of the Internet. With the web, videoconferencing, webcams, and collaborative tools like blogs and wikis, communicating with others around the world, and even working with them, has become far simpler. Perhaps this will obviate travel?

But why bother? Whats wrong with travel in the first place?

In short, the main problem with travel is that it disrupts your routine. By removing you from the context in which you're most productive, it diminishes productivity, and, worse, when you return, you have to work extra hard to make up. As a rule of thumb, for every day of travel, you can expect to spend a day-and-a-half to two days making up. So, a week's trip really means that you are not back to your routine for two-and-a-half to three weeks. One trip a month, and you can see that your equilibrium state is indeed disequilibrium!

Don't believe me? Look at the pocketful of business cards you got on your last trip out. Remember all the things you said you were going to follow up on? Chances are pretty good that you never found the time to folow up. Worse, for many of these cards, you aren't quite sure why you have them in the first place.

Once in a while, when I am in a fit of diligence, I go over my cards and contact the people I said I would and follow up. Nineteen times out of twenty, I get no reply. Why? The other person was busy - traveling! This is symptomatic of a disequilibrium equilibrium.

Besides this mental disruption, which is hardly conducive to thought, let alone productivity, a second problem with travel is that it causes real harm to the environment. Airplanes fly on jet fuel, which is just a high-class way of saying kerosene. And that causes a lot of pollution. When the planes were grounded after 9/11, people found that the skies were bluer, and pollution was much reduced! Airplane travel has consequences, and thats a fact.

So, where does this leave me? Should I stay home and not attend any conferences ever? Or plant trees for every trip I take, to balance the carbon load?

I think that the answer is to set the bar on travel very high. There has to be a solid, justifiable reason. And, even with a good reason, one ought not to travel more than, say, five or six times a year. Certainly, I am planning to stick to this. Since I made my resolution in July, I have traveled only twice. I think that this has tremendously improved my groundedness and productivity: I can highly recommend it.

Has anyone else tried this? Do let me know your comments.

Reviewing the reviewers

2006-09-11T20:51:00.000-04:00

A major problem with research conferences is that anonymous review allows reviwers to get away with murder. Anonymity, meant to allow fearlessness in reviewing, has become a way to hide ills such as:

* not spending enough time reading the paper, so that the review is essentially content-free
* writing a biased review of a paper written by a rival or friend
* turning down a paper for repeating past work, but with no reference to the past work
* stating that the paper does not fit into the call for papers, but not justifying this
* using reviews as a way to advance a pet theory or position

The first of these problems is probably the most common. Researchers are keen to be on a program committee, but not that keen to fully discharge the associated duties!

The result of this drop in review quality has led to discouraged authors, widespread assumptions of conference bias (every Sigcomm outrageous opinion session has a predictable riff on the fraction of the program contributed by PC members), and uneven paper quality even in the 'top' conferences. Something has to change.

Michalis Faloutsos and Kevin Almeroth recently proposed total transparency as a solution. I think this is a pipe dream.

Here is a simple alternative: let the authors judge the quality of the reviews they get, say on a scale from 1 to 10. At the end of the review process, every PC member gets to see the mean score of every other PC member. The score, however, is confidential, and not to be discussed beyond the PC. In particular, the score is not known by authors. Also, note that reviewer anonymity is preserved.

Why will this work? The idea is that the peer group of a PC member is the rest of the PC. No one wants to look bad in front of a peer group. So, every PC member gets an incentive to do a good job. Obviously, someone who cannot commit the time to do a review is likely to bow out of the review process (and the PC) altogether. This should eliminate the root cause of most of the shoddy reviews!

Second, if a PC member delegates reviews to grad students or untrained reviewers, they now have an incentive to make sure that the reviews are well-done. It is their reputation at stake.

Third, although reviewer scores are confidential, they are likely to be informally discussed in the PC member community. So, consistently poor reviewers will soon be eliminated from program committees.

Finally, the system sets the right incentive in terms of reviewer area. Currently, a reviewer not in the area of work of the paper does have the option to ask not to review the paper, but this option is rarely exercised. Instead, the reviewer simply marks his or her expertise level as low. In the new scheme, this will almost surely result in a paper with a low reviewee score. So, the reviewer has every incentive to better match papers with his or her expertise.

Of course, this process is not perfect. For instance, a reviewer who gets out the hatchet only some of the time will get away with it. However, this is unavoidable. This scheme is not perfect, but, in my opinion, much better than the current situation.

A more subtle problem is that this may discourage PC participation by senior researchers whose opinion is valuable PC discussions, but who do not have the time to do detailed reviews. One solution would be to have a PC where some PC members are expected not to do any reviews, but to participate fully in PC meetings. Their identities do not need to be known in public.

All in all, I think this solution balances anonymity and transparency. Please feel free to send me any comments.

Acknowledgement: these ideas were refined over lunch at Mobisys 2006. Unwitting guinea pigs for these ideas include Victor Bahl, Dan Siewiorek, Satya, and Nigel Davies.

Recycling a billion cell phones

2006-09-11T20:47:00.000-04:00

Industry pundits predict that a billion cell phones will be sold in 2007. The same pundits also tell us that cell phones are discarded about once every two years. I myself have a cell phone from 2003 that looks increasingly prehistoric by the day, with no camera, no MP3, and no SD card slot. So, the two-year lifetime seems reasonable. The billion dollar question is, what happens to all the cell phones sold in 2007 when 2009 comes around?

One obvious answer could be that the phones would be junked, like most other electronic devices. If each cell phone is 2cm x 4cm x 1cm, or 8cc, a billion cell phones would occupy 8x10^9 cc, or 8,000 cubic meters, which would occupy a trench a meter wide, 8 meters deep, and 1 km long. Not that much, really, especially if you were to dig the trench in an out of the way place.

Another answer is to donate the phones to needy people. This is both a good idea, and something that is already a major trend. But with a billion phones being sold a year, and only 6 billion people on Earth, there will soon be more than enough phones to go around -- which will probably end up in a landfill...

But perhaps we can do better.

After all, a cell phone in 2007 is likely to have about a 200MHz processor, about 64MB RAM, a Bluetooth NIC, and a CDMA/GSM NIC, as well as a nice color screen. In effect, a little computer. Could we convert a billion tiny computers into a big computer?

The technical challenges are quite interesting: dealing with power distribution, communication, failure, and massive coordination. So, it is interesting research anyway. Surprisingly, there may be money in it too.

Suppose manufacturers had to deposit a $5 recycling fee for every cell phone they sold. This isn't that far-fetched: the EU already imposes such a fee on cars. Then, the billion cell phones translate into a %5bn annual revenue stream. So, if one were to take, say, a 10% market in recycling, one would have a $500mn annual revenue stream. Moreover, if the cell phones were incorporated into something useful (like a giant billboard, where every pixel was a cell phone screen), the cost of hardware would be essentially zero, plus there would be additional money to pay for everything else.

What could one do with a set of phones? Here are some random ideas:

* giant billboards
* TV sets with 'glued together' screens
* Massively parallel rendering engines
* Super SETI
* Massively distributed antenna arrays, where each antenna element was associated with one processor
* Bonded cellphone NICs embedded into a single NIC for laptops
* Disco dance floors (a la the MIT LED dance floor)
* Wall-to-wall displays in meeting rooms
* Ceilings covered with LCD displays that show blue skies always
* Intelligent (changeable) signs for supermarkets
* Massive camera arrays for 3D image capture
* Replace RFIDs with cell phones
* Cell phone based terabyte flash file systems
* ...

Maybe this is not that bizarre an idea after all! If you are interested in this, send me mail or add a comment below.

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ReCellular is a bulk consolidator of used cellphones, and provides the back end for Sprint and a number of 'cell phone donation for charity' organizations. I wonder what they are actually doing with the phones...

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From Jon Crowcroft (paraphrased):

''"What if everyone plugged in their old phone into the charger and left it on? You could build a multi-hop mesh network using the Bluetooth and WiFi interfaces..."''

This is brilliant! Maybe this is something that can be done right away!

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Here is another thing to do with old cell phones -- but I like my ideas better!

Visited and entered landscapes

2006-09-11T20:44:00.000-04:00

(I wrote this in July 2005 while visiting Budapest, sitting across from the Opera house)

What does it mean to be in a place rather than to visit it as a tourist? To be part of a landscape instead of viewing it as if, or literally, through a lens?

For instance, the opera house, baroque, festive, flags flying, brightly lit against the blue, cloudless, even brighter sky, is there in front of me, yet strangely removed. Once photographed, it may as well cease to exist! Indeed, it only appeared in my consciousness five minutes ago, so it can cede this temporary lodging, like an unwelcome renter, five minutes hence. A visitor or bored tourist passing by may not even recall anything of it, other than a vague impress of Baroque prolixity, after their trip.

In contrast, to residents, like home owners, the opera house has fixity in the consciousness that is not easily dislodged. Once can imagine an emigrant from Budapest, years hence, still able to vividly recall its every contour. That must be the difference, then. The space occupied by an artefact in one's consciousness is what distinguishes a viewer of a landscape from its true occupant.

But, does an occupant really know more about the landscape than a visitor? Paradoxically, the first time visitor, with a Zen mind, may see more than the resident. The incongruity of a black flag fluttering from the balcony, the coolness of the porch, may be such second nature to the resident that they cease to register. On the other hand, they are quickly grasped by a fresh viewer (though just as quickly forgotten).

To convert from a viewer to an occupant, one has to enlarge the space occupied by an artefact. This either takes time or focus, or both. Would someone with an intense grasp of their surrounding reality, a Zen master, bridge the gap and become a resident of every landscape they visit? Or does it necessarily take time and repeated exposure? Can the neurochemical pathways of memory only be created by repetition, or can they be etched by force of will? Indeed, how can a visitor, any visitor, learn of the history, the associations of triumphs and scandals of a place? Or see it (or just imagine it) in every shade of light and dark? What would it look like under grey, lowering skies and pouring rain? Or in the first red blush of autumn? Perhaps time and repetition are necessary to create such associations.

Entering a landscape, leaping from a visitor to resident, is seductive, but does it come at a cost? Does becoming a resident cause other places, artefacts, landscapes, to fade? Will entering one landscape cause others to vanish without trace? If so, maybe human consciousness can only be a 'resident' in one place, and forced to be a visitor everywhere else.

Perhaps that is not such a bad thing after all. We want to have a 'home' to return to. If everywhere is 'home', then you have none!

The Goal of Systems Research

2006-09-11T20:32:00.000-04:00

What is, or ought to be, the goal of sytems research? The answer to this question differs for academics and researchers in industry. Researchers in the industry usually work either directly or indirectly on a specific commercial project, and are therefore constrained to design and build a system that fits manifest needs. They do not need to worry about a goal beyond this somewhat narrow horizon. For instance, a researcher at Google may be given the task of building an efficient file system: higher level goals beyond this are meaningless to him or her. So, the 'goal' of systems research is more or less trivial in the industrial context.

Many academic researchers in the area, however, are less constrained. Lacking an immediate project to work on, they are often left wondering what set of issues to address.

One solution is to work with industrial partners to find relevant problems. However, although this results in problems that are well-defined, immediately applicable, and even publishable in the best conferences, it is not clear whether this is the true role of academia. Why should industrial research be carried out for free by academics, in effect subsidized by society? I think that academics may be inspired' by industrial problems, but should set their sights higher.

Another easy path is to choose to work in a 'hot' area, as defined by the leaders in the community, or a funding agency (more often than not, these are identical). If DARPA declares technology X or Y to be its latest funding goal, it is not too hard to change ones path to be a researcher of flavour X or Y. This path has the attraction that it guarantees a certain level of funding as well as a community of fellow researchers. However, letting others decide the research program does not sound too appealing. It is not that far from industrial research, except that the person to be satisfied is a program manager or funding agency, instead of your boss.

I think academic researchers ought to seek their own path relatively unfettered by considrations of industrial projects or the whims of funding agencies. This, therefore, immediately brings up the question of what ought to be the goal of their work. Here are my thoughts.

I believe that systems research lies in bridging two 'gaps': the Problem Selection Gap and the Infrastructure-Device Gap. In a nutshell, the goal of systems research is to satisfy application requirements, as defined by the Problem Selection Gap, by putting together infrastructure from underlying devices, by solving the Infrastructure-Device Gap. Let me explain this next.

What is the Infrastructure-device gap? Systems research results in the creation of systems infrastructure. By infrastructure, I mean a system that is widely used and that serves to improve the daily lives of its users in some way. Think of it as the analogues of water and electricity. By that token, Automatic Teller Machines, Internet Search, airline reservation systems, and satellite remote sensing services are all instances of essential technological infrastructure.

Infrastructure is built by putting together devices. By devices, I actually mean sub-systems whose behavior can be well-enough encapsulated to form building blocks for the next level of abstraction and complexity. For instance, from the perspective of a computer network researcher, a host is a single device. Yet, a host is a complex system in itself, with many hundreds of subsystems. So, the definition of device depends on the specific abstraction being considered, and I will take it to be self-evident, for the purpose of this discussion, what a device is.

An essential aspect of the composition of devices into infrastructure is that the infrastructure has properties that individual devices do not. Consider a RAID system, that provides fault tolerance properties far superior to that of an individual disk. The systems research here is to mask the problems of individual devices, that is, to compose the devices into a harmonious whole, whose group properties, such as functionality, reliability, availability, efficiency, scalability, flexibility etc. are superior to that of each device. This then, is at the heart of sytems research: how to take devices, appropriately defined, and compose them to create emergent properties in an infrastructure. We judge the quality of the infrastructure by the level to which it meets its stated goals. Moreover, we can use a standard 'bag of tricks' (explained in the networks context in George Vargheses recent superb book 'Network Algorithmics') to effect this composition.

Although satisfying, this definition of systems research leaves an important problem unresolved: how should one define the set of infrastructure properties in the first place. After all, for each set of desired properties, one can come up with a system design that best matches it. Are we to be resigned to a set of not just incompatible, but incomparable, system designs?

Here is where the Problem selection gap fits in. Systems are not built in a vacuum. They exist in a social context. In other words, systems are built for some purpose. In the context of industrial research, the purpose is the purpose of the corporation, and handed down to the researcher: 'Thou Shalt Build a File System', for instance. And along with this edict comes a statement of the performance, efficiency, and 'ility' goals for the system. In such situations, there is no choice of problem selection.

But what of the academic researcher? What are the characteristics of the infrastructure that the academic should seek to build? I believe that the answer is to look to the social context of academia. Universities are supported by the public at large in order to provide a venue for the solution of problems that afflict society at large. These are problems of health care, education, poverty, global warming, pollution, inner-city crime, and so on. As academics, it behooves us to do our bit to help society solve these problems. Therefore, I claim that as academics, we should choose one or more of these big problems, and then think of what type of system infrastructure can we build to either alleviate or solve it. This will naturally lead to a set of infrastructure requirements. In other words, there is no need to invent artificial problems to work on! There are enough real-world problems already. We only need to open our eyes.