Are Humans Smart and Computers Dumb? Can Computers Become Better at Helping Humans Solve Challenging Problems?

Computers are generally seen as “dumb”, unable to think for themselves and therefore unable to solve certain complex tasks that humans, being “smart”, are able to solve relatively easily. Humans outperform computers at speech recognition, many image processing problems, and at real-time control problems such as walking – bipedal robots cannot manoeuvre as well as humans. Some may argue computers will never be able to prove mathematical theorems or engineer complex systems as well as mathematicians or engineers.

From a pragmatic perspective, “being smart” is ill-defined.  Roughly speaking, a solution is “smart” if a formulaic solution is not known (or if the solution is obtained much more efficiently than via a formulaic but brute force solution, e.g. one could argue humans are still “smarter” at chess than computers, even though computers can now beat humans).

My current viewpoint is that:-

• we are probably not as smart as we may think;
• computers are dumb primarily because we only know how to program them that way;
• regardless, the future vision should be of challenging problems being solved jointly by humans and computers without the current clunky divide between what humans do and what computers do. We should be aiming for semi-automated design, not fully-automated design.

The following three sections elaborate on the above three points in turn. First a summary though.

Summary: We should not dismiss the idea that computers can help us in significantly better ways to solve challenging problems simply because we see a divide: we are smart and computers are not. Ultimately, smartness probably can be recreated algorithmically provided computers (robots?) and humans start to interact extensively. But well prior to this, computers can become better at assisting us solve challenging problems if we start to understand how much ‘intuition’ and ‘problem solving’ boils down to rules and pattern recognition. Certainly not all intuition would be easy to capture, but often challenging problems involve large amounts of fairly routine manipulations interspersed by ingenuity. Semi-automated design aims to have a human and a computer work together, with the computer handling the more routine manipulations and the human providing high-level guidance which is where the ingenuity comes in.

Readers short of time but interested primarily in a suggested research direction can jump immediately to the last section.

As the focus is on solving mathematical and engineering problems, no explicit consideration is given to philosophical or spiritual considerations. Smartness refers merely to the ability to solve challenging (but not completely unconstrained) problems in mathematics and engineering.

How Smart Are Humans?

A definitive answer is hard to come by, but the following considerations are relevant.

Human evolution traces back to prokaryote cells. At what point did we become “smart”? My favoured hypothesis is that as the brain got more complex and we learnt to supplement our abilities with tools (e.g. by writing things down to compensate for fallible memory), exponential improvement resulted in our capabilities. (I vaguely recall that one theory of how our brain got more complex was by learning to use tools that lead to improved diets, e.g. by breaking bones and accessing the marrow.) It seems much less likely we suddenly picked up an “intelligence gene” that no other creature has. Flies, rats, apes and humans are not that different in terms of basic building blocks.

When comparing humans to computers, one should not forget that humans require 21 or so years of boot-up time. And different humans have different strengths; not all are equally good at solving mathematical problems or engineering systems. An unpleasant a thought as it may be, consider an extraterrestrial who has a choice of building and programming computers or breeding and teaching humans. Which would be a better choice for the extraterrestrial wishing for help in solving problems? (Depending on the initial gene pool and initial population size, it might take 100 years before a human is bred that is good at a particular type of problem. Regardless, if starting from scratch, there is an unavoidable 15-20 year delay.)

Then there is the issue of what precisely smartness is. Smartness is defined by a social phenomenon. At a small scale, one just has to look at review committees and promotion panels to realise there is not always agreement on what is smart and what is not. More striking though, smartness is relative – humans compare with each other and with the world around them. There are infinitely more problems we cannot solve than we can solve, yet no one seems to conclude that we are therefore not smart. We look at what we can do and compare that with what others can do. In a similar vein, a computer can effortlessly produce millions and millions of theorems and proofs in that it could systematically piece axioms together to form true sentences, recording each new sentence as a “theorem” and the trail leading to it as a “proof”. Yet this would be dismissed immediately as not useful. So ‘usefulness to humans’ plays a role in defining smartness.

How do humans solve problems? Following again the principle of Occam’s Razor, the simplest hypothesis that comes to my mind involves the following factors. Most of our abilities come from having to compete in the world (think back thousands of years). Image processing is crucial, and as over half the brain is involved to some extent with vision, a large part of how we reason is visual. (Even if we do not explicitly form images in our minds, our subconscious is likely to be using similar circuitry.) We also need to be able to understand cause and effect — if I stand next to that lion, I will get eaten — which leads to the concept of thinking systematically. So my current hypothesis is that systematic thinking (including understanding cause and effect) and pattern recognition are the main players when it comes to reasoning. The mathematics and engineering we have developed, largely fits into this mould. Rigorous systemisation and writing down and sharing of results have lead to ‘amazing’ results that no single human could achieve (insufficient time!) but at each little step, ideas come from experience and nowhere else. Those that can calculate faster, are more perceptive, are more inquisitive, tend to find the “right” types of patterns, have greater focus and stamina, and are more attuned to what others may find interesting, have significant competitive advantages, but to rule a line and say computers can never do mathematics or engineering is unjustified. (The issue of creativity will be discussed in the next section.)

A final point before moving on. Speech recognition is very challenging for computers. Yet are we smart because we can understand speech? Speech was something created over time by humans for humans. Presumably grunts turned into a small vocabulary of words which grew into phrases and more complicated structures. The point though is that at no time could the process evolve to produce something humans couldn’t understand, because by definition, the aim was to communicate, and if communication was not working, another approach would be taken. If we could learn the languages of all extraterrestrials, perhaps we really are smart, but I’m skeptical.

How can Computers be Made Smarter?

The three main characteristics of a computer system (i.e., something built to do speech recognition or solve mathematical problems) are its size (raw processing power), architecture (e.g., what parts can communicate with what other parts) and the software running on it.

Since humans tend to set the benchmark at what humans can do, a minimum amount of raw processing power is required before a computer can even hope to do something “smart”. Yet the architecture is even more important. Engineers currently do not build computers anything like the way nature builds brains. It is very likely that current computational architectures are ineffective for the types of pattern recognition the human brain engages in.

More interestingly, the architecture of the human brain evolves over time. In simple terms, it learns by changing its architecture. There are two obvious components; via DNA, natural selection increases the chances that a human is born with a ‘good’ architecture to start with. Then there is the long process of refining this architecture through everyday experiences and targeted learning (e.g., attending school).

There is nothing stopping us from building reconfigurable computers that are massively interconnected, thereby very crudely approximating the architecture of a brain. (I suspect this may involve a shift away from ‘reliable’ logic gates to logic gates (or equivalent) that work some but not all of the time, for there is a trade-off between density and reliability.)

With remarkable advances in technology, the real challenge looking forwards is the software side. Because we don’t understand precisely the sort of pattern recognition the brain uses to solve problems, and because until recently the technology was not there to build massively interconnected reconfigurable computers, no one has seriously tried to make a computer “smart” in the way I have been referring to in this essay. (This is not overlooking Artificial Intelligence whose approach was partly hampered by the available technology of the day, and which I suspect never delved deeper and deeper into how the brain does pattern recognition — once artificial neural networks came on the scene, there were sufficiently many research questions for AI researchers to chase that they did not continuously return to the biology to understand better and better how the brain does pattern recognition. And in fairness, as they lacked the computational power for hypothesis testing, it would most likely have been a futile endeavour anyway.)

Summarising this section, several points can be made. Current computing systems (which nevertheless serve the majority of their intended purposes extremely well) seem to be a ‘mismatch’ for doing what humans are good at doing, therefore, they come across as “dumb”. There is no evidence yet to suggest there is a barrier to building (this century) a computing system that is “smart” in some respects, but it will require a whole new approach to computing. It is not clear whether imitating the architecture of the human brain is the best thing to do, or if there is an even more efficient approach waiting to be discovered. Nevertheless, if smartness is being measured against what humans can do, a good starting point is starting with similar resources to what a human has.

Bringing in points from the preceding section, one must not forget though that humans have been ‘trained’ over centuries (natural selection), that each individual then takes an additional 21 years of training, during which time they are communicating with and learning from other individuals, and even then, we tend to work on the problems we believe we can solve and ignore the rest. This suggests we have a narrow definition of “smartness” and perhaps the only real way for a computer to be “smart” in our eyes is if it were to ‘grow up’ with humans and ‘learn’ (through daily feedback over 21 years) what humans value.

Indeed, smartness is usually linked with creativity and being able to solve “completely new” problems. (I would argue though that the problems we can solve are, by definition, not as distant from other problems we have solved before as we would like to think. Who knows how much the subconscious remembers that our conscious mind does not.) Creativity, even more than smartness, is linked to how humans perceive themselves relative to others. A random number generator is not creative. An abstract artist is. Some computer generated pictures coming from fractals or other mathematical constructs can be aesthetically pleasing to look at but is creativity involved once one realises a formulaic pattern is being followed? When it comes to problem solving, creativity and smartness come back largely to usefulness, or more generally, to some notion of value. We solve problems by instinctively knowing which of the thousands of possible approaches are most likely not to work, thereby leaving a manageable few options to work our way through. When we “create” a new theorem or engineer a new system, we are credited with creativity if it is both potentially useful (“sensible”?) and different from what has been done before. A random number generator succeeds at being different; the challenge is teaching a computer a sense of value; I suspect this is achievable by having computers interact with humans as described above (it is all just pattern recognition refined by external feedback!), and perhaps humans can even learn to write down systematically not just an algebraic proof of a mathematical result but also the “intuition” behind the proof, thereby enabling computers to learn like humans by studying how others solve problems.

A Future Vision of Semi-automated Design

Although arguing that if we wanted computers to be smart then we are most likely going to be able to achieve that goal eventually, the more important question is whether we should be trying to head directly there. Personally, a more useful and more easily achievable goal is to work towards semi-automation and not full automation. At the moment there is essentially no way to guide a computer towards a goal; we run something, we wait, we get a result. Often we make a modification and try again. But we are not really interacting with the computer, just using it to shorten the time it takes for us to calculate something. By comparison, two people can work together on a design problem or a mathematical proof; there are periods when they work alone, but there are periods when they come together to discuss and get ideas from each other before going off to think on their own again. Semi-automation lies somewhere between these two extremes: the computer need not be “smart” like a human, but it should come across as being more than just a dumb calculator (even if, at the end of the day, all it is doing are calculations!).

Efficient exchange of information is vital. Computers can store more data than a brain can, but we can probe someone else’s brain for information much more efficiently than we can probe a computer’s memory banks. Largely this is because exchange of information is more efficient when there is shared knowledge that need not be explicitly transmitted.

Semi-automated Theorem Proving

There are so many mistakes, both big and small, in the published literature (even the top journals) that it seems not only highly desirable but inevitable we will ultimately have all mathematical works stored on and verified by computers. This is certainly not a new dream, so how far are we from achieving it?

Although proof verification systems exist, otherwise simple proofs become excessively long when translated into a suitable form for the computer to check. Exchange of information is far from efficient! At the other extreme, automated theorem provers exist, but are yet to prove any theorems of substance. I propose the following stages of research.

1) Choose an area (e.g. basic set theory, or basic set theory and finite-dimensional linear algebra). Work towards devising a notation so that humans can enter a theorem and proof using a similar amount of effort to typing up the theorem and proof for a formal set of lecture notes. To improve efficiency, the notation does not need to be unambiguous since the computer can always ask for clarification if it cannot figure out the correct meaning. Similarly, the gaps between each step of the proof may not always be sufficiently small for the computer to be able to fill in, nevertheless, the computer should have a go, and ask for help (e.g., ask for a sub-step to be inserted) if it fails.

2) Enhance stage one above by having the computer give a list of suggestions whenever it gets stuck; it is easier for the user to click on the correct suggestion than to type in the answer, and if none of the suggestions are correct, the user can always fall back to entering the answer. Here, some method of ranking the suggestions is required (for otherwise there might be too many suggestions). Initially, this can be based on the computer determining “what we already know” and “what we want to find out”, then searching through the axioms and existing theorems to find something that relates either to “what we already know” (a possible ‘starting move’) or “what we want to find out” (a possible ending move).

3) Stage two will eventually prove inefficient as the number of theorems grows and the proofs become more complicated. Some sort of ‘learning’ and ‘intuition’ on behalf of the computer is unavoidable if humans and computers are to interact significantly more efficiently. Perhaps ultimately pattern recognition, as discussed in previous sections, becomes unavoidable, but one should not be too hasty in ruling out the possibility that a fair amount of intuition is more formulaic than we think. Stage three then is supplementing theorems and proofs with basic intuition. The first example that comes to mind is working with bounds, e.g., the triangle inequality. A computer can be taught that if it wants to prove x and y are close, then it can do this if it can find a point z that is close to x and also close to y. Or in another form (i.e., ), if the computer wants to show x and y are some distance apart, it can endeavour to do so by comparing the norm of x with the norm of y.

Certainly some proofs require deep intuition and ingenuity, but even then, a large part of the proof is generally fairly routine. Once a human has specified the “stepping stones”, the routine parts can be filled in (semi-)automatically by the computer working its way through its collection of routine moves and supplemented by basic intuition to rank the order in which it should try the moves.

Stages 1 to 3 are within our grasp and would already have a tremendous impact if they work as expected.

4) Stages 1 to 3 were concerned with a user stating a theorem and sketching a proof, with the aim that the computer can fill in the missing steps of the proof and thereby verify the correctness of the theorem, falling back to asking for more information if it gets stuck. Stage 4 is for the computer to work with a user in proving or disproving a theorem. That is, the user states a conjecture, then through a series of interactions with the computer, the user either finds a proof or a counterexample in a shorter time than if the user were to proceed unassisted. Refinement of the “intuition engine” may or may not be necessary. Some way for the user to suggest efficiently (minimum of keystrokes) to the computer what to try next is required. Some way for the computer to make suggestions to the user as to what to (and what not to) try next is required. [I omit my ideas for how to do this because they will most likely be superseded by the insight gained by anyone working through stages 1 to 3.]

5) The fifth stage is for computers to propose theorems of their own. In the first instance, they can look for repeated patterns used in proofs stored in its database. The examples that come to mind immediately are category theory and reproducing kernel Hilbert spaces. In part, these areas came into existence because mathematicians observed the same types of manipulations being carried out in different situations, identified the common threads and packaged them up into their own theory or “toolbox”.

Semi-automated Chip Design

Engineers have long had the dream of being able to specify what they would like a software program or an electronic circuit to do, push a button, and have a computer generate the software or the circuit. Even more significant than saving time, if done properly, this would ensure the software (and possibly the circuit, although this is a bit harder to guarantee in more complicated situations when extra considerations such as EM interactions must be taken into account) is guaranteed to work correctly. There is a staggering amount of buggy software and hardware out there that this dream is becoming more and more desirable to achieve.

Basically, all the ideas discussed earlier are relevant here. Instead of a library of mathematical theorems, proofs and accompanying intuition being built up, a library of software or a library of electronic circuits is built up. Humans will always be part of the design loop, but more and more of the routine work can be carried out by a computer. Brute force algorithms and heuristics must be replaced by a way of encoding “intuition” and “lessons from past experience”, thereby allowing humans and computers to interact much more efficiently.

Optimisation Geometry

In an invited book chapter (downloadable from arXiv), I made a first attempt at understanding how the geometry of a family of cost functions influences the computational complexity of the resulting optimisation problem.  Importantly, real-time optimisation problems were studied rather than classical “once-off” optimisation problems.

Real-time optimisation problems differ from classical optimisation problems in that the class of cost functions is known beforehand and (considerable) time can be expended beforehand studying this class prior to developing a tailor-made algorithm for solving the particular real-time optimisation problem at hand.  Real-time optimisation problems deserve closer attention because there is no reason for classical optimisation methods to perform particularly well for real-time problems.

In addition to demonstrating how an algorithm with guaranteed performance can, in principle, be constructed for any real-time optimisation problem, a geometric framework was given which is hoped will yield, in future work, insight into the computational complexity of real-time optimisation problems.

An embryonic concept is that overall complexity divides into intrinsic complexity and extrinsic complexity.  The intrinsic complexity is the unavoidable complexity of the real-time optimisation problem, the best that can be done with infinite resources allocated to simplifying the problem beforehand.  The extrinsic complexity is the additional complexity coming from how the optimisation problem is posed; for example, if a quadratic cost function is composed with a complicated diffeomorphism then the resulting optimisation problem is “difficult” whereas the underlying optimisation problem, that of minimising a quadratic function, is “easy”.  (This distinction makes less sense for “once-off” optimisation because there is no opportunity to determine beforehand, “free of charge”, whether or not the original problem can be simplified by a suitable change of coordinates.) The coordinate-independent nature of geometry suggests differential topology/geometry is an appropriate tool to be using in this investigation.

Optimisation on Manifolds — Lifting Iterative Algorithms from Euclidean Space to Manifolds

A natural question to ask in the theory of Optimisation on Manifolds is how the Newton method can be generalised to an iterative method on a manifold. Traditionally, the standard way was formulaic: because the Newton method involves a gradient, a Hessian, and vector space addition, generalise these concepts first then apply Newton’s formula.  This led to the Riemannian Newton method. Gradients, Hessians and vector addition are not intrinsic though; they are just one realisation of an iterative method that uses the first and second order derivatives to converge locally quadratically to a (non-degenerate) critical point.  The standard Newton formula in Euclidean space is designed to be optimal for quadratic cost functions, but a simple change of coordinates will change it to being optimal for another class of cost functions instead.

It turns out that changes of coordinates play a fundamental role in understanding how the Newton method, or any (memoryless) iterative method for that matter, can be lifted to manifolds. In A Framework for Generalising the Newton Method and Other Iterative Methods from Euclidean Space to Manifolds, it was essentially demonstrated that all generalised Newton methods can be understood as applying a different change of coordinates at each iteration, and local quadratic convergence can be assured if and only if the Newton method in Euclidean space is “robust” to these changes, meaning its radius of convergence can be uniformly bounded under all coordinate changes of interest.  The Newton method is indeed very robust, leading to a tremendous variety of possibilities for lifting it to manifolds which go well beyond the traditional class of Riemannian Newton methods.

It was also pointed out there is generally no reason to insist that the lift is uniquely defined globally.  It suffices to lift locally in response to where the iteration is currently at. Visually, one way to think of this is to re-centre at each step of the iteration: rather than move a point around a sphere searching for a critical point, keep applying rotations to the sphere endeavouring to bring a critical point to the North pole.  More generally, arbitrary transformations of the manifold, or of the ambient space containing the manifold, can be used for re-centring at a distinguished point, and the Newton method need only be lifted to a region containing the distinguished point.  (A special case is “rolling without slipping”, but there a Riemannian metric is present, which results in the local lifts fitting together globally. This need not be the case for more general re-centring techniques, and may possibly lead to more efficient algorithms that use simpler lifts.)

Many competing factors come into play when designing a Newton method for a particular problem. Hopefully the framework will prove useful, but it is far from being a panacea.  It raises more questions than it answers.

The Role of Estimates, Estimation Theory and Statistical Inference – Is it what we think it is?

The tenet of this article is that estimation theory is a means to an end and therefore cannot be sensibly considered in isolation. Realising this has pragmatic consequences:

• Pedagogical. When faced with solving a statistical problem, it becomes clearer how to proceed.
• Philosophical. A number of controversies and debates in the literature can be resolved (or become null and void).
• Interpretive. A clearer understanding is gained of how to interpret and use estimates made by others.

Forming estimates is ingrained in us; I estimate the tree is 5 metres high, there are 53 jelly beans in the jar and it will be 25 degrees tomorrow. This can draw us strongly to the belief that forming an estimate is something intrinsic, something that can be done in isolation. It suggests there should be a right way and a wrong way of estimating a quantity; perhaps even an optimal way. Succumbing to this belief though is counterproductive.

Once you have an estimate, what will you use it for? Putting aside the amusement or curiousity value some may attach to forming estimates, for all intents and purposes, an estimate is merely an intermediate step used to provide (extra) information in a decision making process. I estimated the height of the tree in order to know how much rope to buy, I estimated the number of jelly beans in the jar to try to win the prize by being the closest guess, and I estimated the temperature tomorrow to decide what clothes to pack. In all cases, the estimate was nothing more than a stepping stone used to guide a subsequent action.

In general, it is meaningless to speak of a good or a bad estimator because, without knowing what the estimate will be used for, there is no consistent way of ascribing the attribute “good” or “bad” to the estimator. The exception is if the estimator is a sufficient statistic, and indeed, it might be more intuitive if “estimators” were sometimes thought of as “approximate sufficient statistics”.  All this will be explained presently.

The James-Stein Estimator exemplifies the assertion that it is generally not possible to declare one estimator better than another. Which is better is application dependent. Less striking examples come from situations where the penalties (in terms of making a bad decision) resulting from different types of estimation errors (such as under-estimation or over-estimation) can vary considerably from application to application.

Usually, estimates serve to compress information. Their job is to extract from a large set of data the pertinent pieces of information required to make a good decision. For example, the receiving circuitry of a radar gathers a very large amount of information about what objects are around it, but in a form which is too difficult for humans to process manually. The familiar graphical display produced by a radar results from processing the received signal and extracting out the features we are interested in. Even in estimating the height of a tree, this is true. The full information is the complete sequence of images our eyes see as we look up at the tree; we compress this information into a single number (we hope is) related to the height of the tree.

Initially then, there is no role for estimation theory. We have data (also commonly referred to as observations) and we wish to make an informed decision. A standard and widely applicable framework for making decisions is to determine first how to measure the goodness of a decision and then endeavour to construct a decision rule (which takes as input the available data and outputs the recommended decision to make) which can be shown, in a probabilistic framework, to make good decisions the majority of the time. A key point is that theoretically, we should use all the data available to us if we wish to make the best decision possible.  (Old habits die hard.  It is tempting to reason thus: If I knew what the temperature will be tomorrow then I know what clothes to pack, therefore, I will base my decision on my “best guess” of tomorrow’s temperature. This is not only sub-optimal, it is also ill-posed because the only way to define what a “best guess” is, is by starting with the decision problem and working backwards.)

There are two pertinent questions, one a special case of the other, caused by the undesirability of returning to the full set of data each time we wish to make another decision. (Imagine having to download the global weather observations and process them using a super-computer to decide what clothes to wear tomorrow, only to repeat this with a different decision-making algorithm to decide whether or not to water the garden.)

1. Is there a satisfactory (but perhaps sub-optimal) method for processing the data into a compact and more convenient form allowing for many different decisions to be made more easily by virtue of being based only on this compact summary of the original data?
2. Are there any conditions under which the data can be processed into a more compact form without inducing a loss of optimality in any subsequent decision rule?

In fact, the mathematics used in estimation theory is precisely the mathematics required to answer the above two questions.  The mathematics is the same, the results are the same, but the interpretation is different. The true role of estimation theory is to provide answers to these questions. There are many situations where it seems that this has been forgotten or is not known though.

The answer to the second question can be found in statistical textbooks under the heading of sufficient statistics. The rest of statistics, by and large, represents our endeavours to answer the first question. Indeed, we routinely go from data to an “estimator” to making a decision. When the Bureau of Meteorology forecasts tomorrow’s weather, they are doing precisely what is described in the first question.

In virtue of the above discussion, I advocate thinking of “estimators” as “approximate sufficient statistics”.  They serve to answer the first question above when a sufficiently convenient sufficient statistic (the answer to the second question) cannot be found or does not exist.

By shifting from thinking in terms of “estimators” to “approximate sufficient statistics”, I hope to show in subsequent articles that this leads to clarity of thought.

Are your research aims the right aims?

Defining the aims of a research project, whether it be for a Masters or PhD thesis, or even a major grant application, requires considerable thought. It is more difficult than it looks for several distinct reasons.

First, one must define a general research area in which to work.  The hardest part about research is finding the right problem to work on.  The problem needs to be hard enough and interesting enough for others to recognise the value of your contributions.  Yet if it is too hard, it would not be possible to make a sufficiently worthwhile contribution in a reasonable amount of time. Several common strategies are:

• The entrepreneurial approach. Identify a problem that has not been considered yet by your peers but which you believe will attract attention once people become aware of it. Looking backwards, it is easy to identify areas of work which were (or are) a hot topic and for which the barrier to entry was not great; it was the right problem at the right time to consider.
• The arbitrage approach. Different disciplines can have different approaches for tackling similar problems; it is not uncommon for one discipline to be completely unaware of related advances in another discipline. Look for how your expertise can be applied outside your discipline in a novel way.  (Breakthroughs in an area often come about by the introduction of ideas originally foreign to that area.)
• The team approach. Find a world-class team of experts working on a grand challenge problem and join them.  This has many benefits.  It will serve as a constant supply of interesting research problems to work on and your research will have greater impact because the team as a whole will work towards consolidating contributions into even bigger ones.
• The tour de force approach. Keeping in mind that even great research is the result of 1% inspiration and 99% perspiration, if you have the determination and single-mindedness to spend many months chipping away at a difficult problem, chances are that you will be rewarded.

Next, it must be appreciated that identifying an area in which to work is just the first step in defining your research aims.  Wanting to develop a better algorithm for a certain signal processing problem is not a tangible goal that you can work towards unless you have defined what you mean by better.  It is not uncommon for this step to be omitted, with the hope that a new idea will lead to a new algorithm which will be found serendipitously to have some advantage over previous approaches. Yet there is little to recommend this rush-in approach since invariably the small amount of time saved at the beginning is more than lost by the lack of focus and direction during the remainder of the project. Furthermore, few funding agencies would be willing to fund such a cavalier approach, just as few investors would be prepared to invest in a start-up without a business case. It might succeed, but experience suggests it would be a bigger success if time is invested up front to think carefully about what it is you really want to solve.  Measure nine times, cut once.

Research aims should be:

• Tangible and measurable. An independent person should be able to come along and judge whether or not you have made significant progress.
• Outcome focused, not output focused. Writing reports and journal papers are outputs, but if no one uses or builds on your work, you have not achieved an outcome.
• Achievable. You must be able to give a credible argument as to why you will be able to achieve your aims in the allocated time frame.
• Hierarchical. A hierarchical structure allows for ambitious aims at the top level with shorter-term goals leading up to them. This is generally seen to be:
  • focused and efficient – your work builds on itself and grows into something substantial rather than remaining a diverse collection of less substantial contributions;
  • mitigating risk – by having lower level aims which are perceived as achievable then there is less concern that you may not achieve all of your more ambitious aims;
  • outcome orientated – focused work on ambitious  (and appropriately chosen) aims is perhaps the best way of maximising the potential outcomes and impact of your work.

Supporting the research aims should be statements on the significance and innovation of the proposed research and an explanation of the approach and methodology which will be adopted.  All this should be described in the context of previous and current international work in the relevant areas.