SHARING AMERICA'S TECH NEWS FROM THE VALLEY TO THE ALLEY
by Chris Lee (courtesy arstechnica)
One of the great untold stories in science is the process of science itself. I don’t mean stories about what scientists have discovered and what those discoveries tell us; we (and many others) cover those every day. I also don’t mean stories about the pure joy of discovery and the excitement of finding out that everything you thought you understood was total nonsense. We cover that here at Ars occasionally, and there are plenty of books on the subject if you’re hungry for more.
What’s missing is the background for these stories of discovery. How do you take an idea from its beginning as a casual musing all the way through an actual research program? What’s involved in that process? How do you sort out the good ideas from the bad and choose what to pursue and what to abandon? That’s the story I want to tell.
Since this is the story of science-as-a-process rather than science-as-a-result, I will be using myself as an example. I am, as some of you may know, a tenure track faculty member at a research institute in the Netherlands. Being a researcher in the Netherlands is not that different from being a researcher anywhere else, so much of what I discuss will be familiar to scientists everywhere. Since I recently hopped on the tenure track, I have the next few years to prove that I am able to not only carry out research, but to start and manage entire research programs. As of yet, I have no research program to manage.
I am aiming to give you a flavor of what goes through researchers’ minds when we come up with an idea, and what happens afterward. It’s not enough to just have an idea—it has to meet all sorts of criteria, only some of which have anything to do with science. As such, we have to refine and structure an idea into something that could become a coherent body of research. We then have to convince other people that it’s a good idea. What you will read here are my ideas of the sort of research I want to do and the beginning of my attempt to get a research program off the ground.
Before we get to the science, we need some background. What does it mean to be a physics researcher in the Netherlands? What conditions do I have to meet? What sort of time-scale are we talking about in terms of viable ideas?
To understand how I choose between good ideas and bad ideas, we need to step back from actual physics and science and take a look at the structure of the research community that I work in. Research takes resources. I don’t mean money—all right, I do mean money—but it also requires time, people, lab space, and support. There is a human and physical infrastructure that I have to make use of. I may be part of a research organization, but I have no automatic right of access to any of this infrastructure.
In the Netherlands, doctoral candidates are not students (nor are they, as many think of students, free labor). Instead, they are full-time staff with four-year contracts. What does this mean? First, it’s very difficult to organically grow an idea from small scale research projects into something larger that has a doctoral student attached to it. The timing just doesn’t work out with that four-year limit. It’s difficult to begin a project with a master’s or undergraduate student who will “just take a look” and then hand it over seamlessly to a PhD student should it appear promising.
This has implications for scale. A PhD student has the right to expect a project to generate a decent body of work within those four years. A project that is going to take eight years of construction work before it produces any scientific result cannot and should not be built by a PhD student. On the other hand, a project that dries up in two years is equally bad. In other words, no matter what idea I come up with, I need to be able to say that all the candidates I hire should find enough material to write a thesis and graduate—no matter what the experimental outcome.
This means that any big idea I come up with also needs to be partitioned into chunks of the right size. If it can’t, then it doesn’t work in an academic institution.
Since all experimental results need to be thesis-worthy, the questions I want to answer should be open enough to accommodate failure. For instance, my ideas are often based on a single experiment: if we conduct experiment “a,” we could measure property “b,” and that would be so cool! But, what if “a” doesn’t work? Does the student go home?
The core idea needs to be structured in a way that, should certain experiments not work, the idea still builds something that can lead to successful experiments. Or, if the cool new instrument we want to build can’t measure exactly what I wanted, it can still measure other things. One of those other measurements must be fairly certain of success.
To put it bluntly: all paths must lead to results in some form.
I owe it to my students to come up with research ideas that will generate some success in the right time frame. But there’s another human side—mine. As a tenure tracker, time is a big boundary condition. If I choose to forego PhD students, I could come up with an idea that involves eight years of construction before the first results might be expected (and the first students are hired). That would be acceptable in terms of meeting their requirements.
Unfortunately, my time would be up by then. Partway through the eight years, the director of the institute would look at my performance and promptly tell me to seek work elsewhere. The tenure track is there to give researchers a limited time to prove that they can do everything a tenured researcher should be able to. I must succeed with medium scale projects or many small scale projects rather than a big, long-term project.
That doesn’t mean, however, that these projects can’t be pieces of some longer-term big project. I simply have to ensure that the project delivers results at all time-scales. In my case, the projects should be in the one-to-six PhD student range and should not require more than a year of instrumentation building (unless building the instrument can be counted as doing science). It should, from today, deliver many results within a four-year period, or I’ll be looking for another job.
Finally, there are institutional goals and resources. At the moment, I am in an institute that is going through a major restructuring and relocation. The institute will split up, with pieces moving to three different universities. Each piece will have a very different focus: energy research at Eindhoven, soft X-Ray optics at the University of Twente, and a free electron laser facility at the University of Nijmegen. At the moment, I’m part of the soft X-Ray optics group, so my research should fit within that theme. On the other hand, as a tenure track researcher, I need to demonstrate some independence. My research still needs to be distinct from what the group already does.
These considerations, which are largely political in nature, are surprisingly important. They make the difference between enthusiastic institutional support (above and beyond what you are entitled to) and grudging assistance (limited to exactly what you are entitled to, delivered on someone else’s schedule). In other words, the enthusiasm with which an institute supports a research program may very well be the difference between success and failure.
The job, then, is to take what I’m interested in and beat it into a shape that also looks interesting to the research institute and the people who decide to provide money for research.
I really love quantum physics, but not necessarily the entanglement and computation that I write about here at Ars. Think of my interests like this: how do two molecules come into proximity and react to form products? Usually there are many different possible reactions, so why do we end up with the products that we observe?
For many molecules and potential reaction products, the energy released or absorbed during the reaction is enough to tell you what you’re going to end up with. But there are many, many cases where the energy differences between different products are small enough that more than one product is produced. Or sometimes a catalyst can intervene to allow reactions that, from an energetic perspective, should be very rare.
In any case, I’m not really interested in the bulk reactions and average products. I’m interested in the details: how do the starting quantum states and coherences between these states influence the final reaction product?
Expanding and generalizing on that: since the quantum states of molecules determine their properties, how much control can we exert over those characteristics through quantum manipulations?
I think there are very few physicists and chemists who would argue that these are uninteresting questions. The physicists, however, might say, “This has all been done before.” After all, electromagnetically induced transparency, self-induced transparency, frozen light experiments, and Bose Einstein condensation are all examples of manipulating quantum states to set the properties of a material. The chemists would point to molecular beam experiments on cold molecules as evidence that we are already studying how the initial quantum state of a molecule influences subsequent reactions.
These things are already being done, and I probably can’t add much to the conversation. But I don’t want to add to those examples; I don’t want to work on those sorts of materials. I have no interest in making cold dilute gasses of metallic atoms or molecules or working with crystalline solids dropped to the temperature of liquid helium. And there is no way that I would willingly enter the seventh circle of the hell that is molecular beams.
No, I want to work with liquids and thin frozen layers—and layers that are not necessarily ordered crystals. (At this point, all the physicists and chemists reading this will be laughing, because liquids are absolutely the worst choice to work with.)
Liquids are interesting, though. They lack the order that makes the behavior of a crystal relatively clean, yet they still retain near-solid densities, meaning that individual molecules interact with each other constantly. In a very real sense, liquids represent the messy middle ground between low-density cold gases and crystalline solids.
On Earth, liquids are where all the most interesting stuff occurs. All the chemical reactions that occur in a cell? That’s a liquid environment. Almost all pharmaceutical products are produced in wet-chemical reactions. In fact, many industrial processes are condensed phase reactions. If we can get control of and directly play with the states and coherences of molecules in a liquid phase, then we will have an important new tool. This wouldn’t just be useful for studying why things are the way they are, but it would also provide us with new knobs to control the properties of materials. I think that is exciting and worthwhile stuff.
We know this is important—experimental results tell us that coherence is a vital aspect of photosynthesis. But there is a rumbling controversy over speculation that enzymes make use of coherence to help catalyze reactions.
On the applications side, we know that coherence between vibrational states—these are the quantum states that describe the spring-like vibrations of atoms within a molecule—is the source of a lot of interesting optical phenomena and that controlling their coherence would allow for new imaging techniques. All of this paints a picture of something that is of broad interest. Yet no one has been able to put together the important experiments to do any of it. That is what I want to do.
As nice as this idea is, it doesn’t matter at all unless I can come up with a reasonable scheme to make the measurements involved. Sometimes experiments are blindingly obvious, but on other occasions no one knows how to do them.
I often daydream about what atoms and molecules get up to when no one is looking. Lately I have been getting flashes of images of the coherence involved as molecules approach each other: I dream of sitting on an atom in a molecule and seeing the electron clouds moving around in response to an approaching molecule. At some point, I snap out of it (the hot water has run out, most likely), thinking, “I would love to see that for real.”
These sorts of dreams seem to prime my brain. I’ll more likely end up dreaming about the same molecule and the same coherence, but this time there will be a laser, or an electrode, or something else involved that interferes with what’s going on. I even dream about what that instrument could record. I’ll have the same dream with variations to the external interference over and over again. At some point, the dreams converge into one “ideal” experiment.
The kernel for this particular idea came from a dream about how coherence can appear to have vanished yet may, in fact, still be around. Imagine, as I’ve attempted to illustrate in the picture below, a liquid with a single molecule that is different from the rest. We hit that molecule with a laser pulse designed to excite a specific vibrational mode—for example, a pulse that sets two carbon atoms in motion so that the bond between them stretches and compresses. Now, because the molecule is in a liquid, it is continuously brushing up against other molecules. Every time it does, that vibrational mode is disturbed: its phase might change, or it might give up some energy to another molecule. This process occurs on time scales that are typically faster than a couple of picoseconds (it depends on a lot of factors).
But there’s another process going on. The very motion of those two carbon atoms will set other atoms within the same molecule into motion. So exciting one vibrational mode leads to other vibrational modes being excited in a kind of cascade. This process, called delocalization, is a bit like one oscillator (think a ball on a spring) driving another spring linked to it. All kinds of crazy things can eventually happen, but at least initially, the two oscillators are in phase and coherent with each other.
In my dream, I see this molecule’s atoms sequentially begin to vibrate until the vibrations get smaller and finally stop. In the absence of collisions, the phase relationship between these different vibrational modes is not simple, or even predictable. It is deterministic, however. Now, if I were to shine another laser pulse on it, it could take away some vibrational energy from the molecule in a process called Raman scattering. This slows the vibrations but also extracts information about how the original vibrational wave packet spread out through the molecule—information that can be gathered by measuring the frequency, phase, and amplitude of the scattered light.
Imagine that I can do these measurements. What do I learn? Some very specific information about that particular molecule and its environment. For example, I learn:
Those are interesting things to know. But we’re already aware of a fair bit about this, especially for electronically excited atoms and molecules. What does this “ideal” experiment add, and how does it become a research program?
The first step is to realize that the questions this one experiment can answer change based on the context—the molecules and conditions involved. This is actually a very useful thing: the same basic experiment, conducted under different conditions, will tell us very different things, with different implications and relevance. We can take advantage of this to create a research program that easily generates tasty, PhD-sized chunks of science without needing much in the way of new equipment and development time—they are all based on similar measurements from a similar apparatus. Once you have those measurements working, the projects flow.
This is actually the secret to a lot of research labs: a technique is mastered, and then you make hay for as long as you possibly can with it.
It’s time to get specific. This is the part that I admittedly have difficulty with: turning ideas and desires into concrete plans. Or at least making them into plans that are acceptable to people who provide money.
Let’s take the general ideas above and break them up into individual, graduate-student-sized projects. In one sense, this is easy—just come up with three sets of experiments. Unfortunately, the experiments need to tie together intellectually. It isn’t necessary that the students work together on everything, but, thematically, they should be sufficiently related. That way, the students can assist each other when problems arise.
Getting specific means thinking about who I’m going to ask for money and how much I’m going to ask for. The European Research Council is offering up to €2 million (about $2.59 million) over five years to a few clever and competent researchers fitting a certain profile. I need to be relatively young—you must have held your PhD for less than 12 years—and you should be looking to strengthen an existing research group. There are other criteria, but those are the two that give you the essence of what the council is looking for: new researchers, trying to get more independence. As for the money, it sounds like a lot, but for what I want to do, it will provide for three PhD students over the entire period.
On the upside, the fact that I can only run three PhD research projects offers an unexpected benefit: I need to think carefully about what I really want to do.
I want to understand the vibrational motions of molecules at their most intimate level. To do this, I envision taking a molecule that has one unique bond—say a single oxygen atom stuck on a ring of carbon atoms. We use a laser to pump the hell out of the stretch vibrational mode of the bond between the ring and the oxygen. Because it’s the only bond of that type and all the other vibrational modes have quite different vibrational frequencies, I have a unique starting point in my experiment. I know exactly which vibration is oscillating.
Now, as the oxygen molecule bounces around, it will start transferring energy to other atoms in the carbon ring. When it collides with other molecules, it will transfer energy. So, after a certain amount of time passes, I take a snapshot of the excited vibrational modes. And I do it in such a way that I can see not only which vibrational modes are excited, but also whether they are oscillating in a fixed phase-relationship with the original excitation pulse.
All of this will depend strongly on the environment. There are a huge number of experiments to do, each of which could tell us a little more about what the molecule is doing.
These same experiments, but with different model compounds, can be used to tell us what is going on when a molecule attaches to a surface. For instance, if an alcohol molecule attaches to the surface of certain metals, it will break up. We can use this experimental scheme to understand that breakup in more detail, by exciting vibrational modes and looking at how they shift and vanish as the alcohol breaks up into new compounds. In a sense, we use the excitation of vibrational motion as a tag to track when and how the breakup occurs. And that holds a great deal of importance in understanding how metal catalysts work.
It may be sad to think that the life of a grad student can be summed up in four paragraphs. But I am pretty confident that what I have described is actually more like eight years of work instead of four. I’m not too concerned about that; with a good start, new students can follow the project as long as it remains interesting.
Shoveling molecules around and making them do cartwheels
If the first project is about understanding, the second is about control. We want to use the vibrational motion of the molecules to our advantage. To do that, we need to be able to set a certain fraction of the population vibrating in a particular way. In fact, we want to be able to drive what are called “coherent population oscillations.” This basically means that for a laser pulse of a given intensity, I can be certain that every molecule within the focus is vibrating at a certain vibrational frequency, and all the vibrations are in phase with each other.
What makes this important is that population statistics underlie optical properties. For instance, if I can make a population that’s evenly divided between two vibrational states, then I prevent the molecules from emitting certain colors of light. This is an important step for improving some imaging techniques. We can image using the vibrational frequencies that we excite with a laser as labels for particular chemicals. This provides high contrast images without introducing artificial contrast enhancers. If we can prevent the molecules from emitting certain colors of light, then we can improve the image contrast.
Better yet, we can use this process to see smaller features. I can choose my laser beam shape so that it will create equalized populations in some places but not in others. As I increase the laser power, the size of the area where the populations are equal increases. If I set things up right, then the image is generated from the shrinking areas where the populations aren’t equal. Essentially, as I turn the laser power up, I can see smaller and smaller features in an image. That will be one of the main goals of this project: imaging at high-resolution.
This isn’t the only way of controlling population dynamics, either. It’s possible to crank the laser intensity up so high that it keeps the molecules vibrating in phase. Once we get to that stage, the entire molecular population will cycle rhythmically between the two states. These coherent population oscillations, otherwise known as Rabi flops, are used throughout atomic physics, but doing Rabi flops with molecules is so much harder that it has never been popular.
The nice thing is that Rabi flops can also be used as a probe for molecular behavior: where is this molecule within the light field? Does its proximity to a surface shift its vibrational resonances, and how far? All of this will show up in the spectrum of the Rabi flops.
You might expect that these Rabi flops will be very short-lived. But in atomic physics and nuclear magnetic resonance spectroscopy (think MRI), a number of techniques have been developed to preserve the conditions required for Rabi flops. One aspect of this project will be trying to apply variations of these techniques to our molecular systems to preserve those conditions and increase the precision with which we can perform spectroscopy. That will be… challenging. (“Challenging” is a forbidden word in grants, because it is viewed as being synonymous with “impossible.”)
In the last project, I want to get into some basic chemistry. When it comes to physics, I am pretty confident. I know where the difficulties are and I know where I am pushing boundaries. But I am entirely ignorant of chemistry. And I want to do some chemistry.
Previously, I described how we were going to excite the vibrational mode of an oxygen atom attached to a benzene ring and then see what would happen. Well, one might wonder: does the excitation of a particular vibrational mode help determine the outcome of a chemical reaction?
To explore this has been a bit difficult. The natural energy of that vibrational mode is such that we would not expect a single excited molecule in a beaker full of compound. In fact, if we were to heat the beaker, the compound would boil away before that mode would be excited in a single molecule—temperatures of about 3000K are required to get a small population with that mode excited. Usually no one really knows if the excitation of vibrational modes can affect the outcome of a chemical reaction.
But lasers give us a tool to create molecular populations in a highly excited vibrational state, and we can take snapshots of molecular states at a later time. So we can really get right into the dynamics of the reaction itself. This is separate from determining the statistics of a reaction like its rate or the energy released—those are a compilation of many factors. Here, we would just be looking at the reaction itself. We can tag a molecule by putting it in a vibrational state and then look for reaction products in the vibrational spectrum. We can track both the appearance of new products and where the vibrational energy goes as the products are produced. I think this would be very informative.
The difficulty is picking model reactions to study. Again, I’m no chemist and I’m not sure that my choices are good. I’ve decided, rather arbitrarily, to divide the world up a bit. There are reactions that normally just go in a single direction: two reactants form a single or pair of products. Then there are reactions that go forward and backward: the reactants form products that then recombine to form the reactants. There are reactions where the outcome is a pair of products, with the balance between the two determined by something like the temperature.
The job is to choose some good examples in the classes that I have created and study them. It should be possible to use vibrational modes to enhance, or suppress, the direction a reaction wants to go. In the first case, the reaction might be severely hindered by certain excitations and sped up by others. In the second case, the right excitation might prevent the back-reaction from occurring. In the last, we might be able to selectively choose which product dominates.
In the end, though, I want to apply this to something more relevant, like catalysis. The end-point would be studies on catalytic activity when the reactants and/or products are vibrationally excited. Obvious examples include the reduction of carbon dioxide and water splitting. Although they appear simple, these are not easy reactions to understand. As I am rapidly learning, the catalysis community speaks an entirely different language, so even when we do the work, it will be difficult to communicate the results in a way that shows their relevance to the community that should be most interested in them.
In short, I need to be very circumspect in describing this project and what I want to do with it.
So that’s the three-course meal of science that I have in mind. I must admit that the last project worries me. The ideas are clearly expressed in the application, but I’m concerned that I am simply going to walk into the trap of not knowing enough chemistry to make this one work. Luckily, I was able to convince a very good chemist to collaborate in this part of the project, so that will help. I intend to keep the chemistry as simple as possible, mostly sticking to reactions that are well-known and easy to run. Even so, a chemist might well balk at giving me money to do this.
Those are the ideas and the specific projects. Now it’s time to see how they fit with the institutional goals and how they and the funding agencies will perceive the risks and rewards.
I think I’ve got a good balanced program in the works. On the other hand, the laser system that enables it all seems… complicated. Certainly, the early work will involve a lot of set up time. That should worry me, the funding agency, and the institution. I’m not going into this blind, however. I can’t walk into a showroom and order a laser system, like you might a car. “Hi, I’d like the red M3 with the boy-racer body kit, low profile tires, mags, and red brakes. Oh, and because this is on the government ticket, please make it a diesel.”
On the other hand, the components are all available, and most of what I want can be obtained from a single commercial supplier. What I’m looking for is a combination of two laser systems, both of which are known to work—the question is really in the details of implementation. I have asked a pair of companies that sell the systems if they can do it and how much space it will take up.
Even so, I think it will take something like a year to get the full laser system up and running, though I should hasten to add that we can start doing experiments with a partial laser system. However, these details are very dependent on the degree of support I get from my host institute.
I have two options as far as hosts go. I am currently at the Dutch Institute for Fundamental Energy Research (DIFFER), where I work in a group that plays with X-ray optics. The X-ray optics group, though, is moving to the University of Twente (UT). I have a choice: moving to the UT with my current group or staying with DIFFER. If I move to the UT, I will be expected to continue studying the physics and chemistry of X-ray optical elements. That research is a story of highly accurate deposition processes, diffusion, material mixing and reactions, and understanding surface chemistry.
These are challenging and interesting problems. The money for this type of research comes partly from government and partly from industry, which means that we end up working on an interesting mix of practical problems and physics. As you may have guessed, though, the work is a bit removed from what I would be planning to do, since none of the lasers I plan on using are in the X-ray region of the spectrum.
But chemistry is chemistry, and physics is physics. Put another way, if I choose a good set of experiments, the results and conclusions will apply more widely. The surface phenomena that I currently study on the surface of an X-ray optic are the same as those going on in the liquids that I hope to be studying. The techniques I plan on using can be applied to understanding surface reactions. Furthermore, they provide a wonderful new tool for studying the layered structure that goes into making an X-ray optic. In other words, although the experiments I want to do in the project are not X-ray optics related, they are relevant to the work going on at UT.
That said, all this means there is a promise to deliver. At some point, my fancy new laser system has to be turned on an X-ray optic and, when it is, it had better find something interesting. My arguments about relevance only buy so much time before I have to deliver something that is actually relevant, and I had better be truly committed to doing so. It would seem, then, that the UT would be a bad choice.
The one appeal of UT, though, is that its research program is bigger than the X-ray optics group—there are three other research groups that are deeply interested in the research I want to do. They don’t have research programs that directly overlap, but they would certainly like to be engaged with the results and in related projects.
The result of all of this is that my direct support from the X-ray group would be minimal and depend on work that is not directly included in the proposal. But, indirectly, there would be a great deal of support, and that could be crucial. Since I will need experienced technicians to help build the equipment, support from outside the immediate research group will be vital; my success will depend upon good relationships with neighboring research groups. A strong collaboration will be key to getting the experiment off the ground.
The alternative, DIFFER, is an energy research institute: fusion physics and artificial photosynthesis (referred to as solar fuels) are its specialties. There is an immediate connection here: I would be studying, at a very low level, the very basis of the physics and chemistry that underly artificial photosynthesis. Clearly, my direct connection here is better, and my research plan reflects that.
But DIFFER is also a very practical institute. Although I think they will enthusiastically support my ideas, in the end, they will want a payoff in terms of the ideas contributing in a very visible way to some part of the solar fuels effort. In that sense, they will see a risk in supporting me, even though they will see a good chance of quality fundamental research coming out. The looming question will always be “What if none of these studies show a way to make solar fuel production more efficient?” That question is unanswerable at present, but it’s something that both I and DIFFER will bear in mind as my research progresses. The downside is that DIFFER has very little in-house expertise with this sort of experiment. At the UT, I might be able to purchase technician time from experienced people who could set up the basic laser system. At DIFFER I would have technician time, but the technicians would require a lot more supervision and may have less experience than I do in setting up such a laser system. That means that, at DIFFER, the first PhD student would have a heavier burden to bear than if I were at the UT.
In the end, though, if I didn’t think I was competent enough to do these experiments myself, I wouldn’t be suggesting them—I could even build the laser system from components by myself if I had to. It’s therefore better to ensure that I have good direct support and continue to generate external collaborations to make my research stronger. Since I can make that case easier at DIFFER, that is the place to be.
What are the chances that I’ll get the money? From a straight odds perspective, they’re low. But the straight odds never represent the true chances, so let’s examine things more carefully. The European Research Council will be looking for innovative and interesting research. I think that I fit this criterium.
The other hurdle is assessing my quality as a researcher: does my history suggest I am worthwhile investment? Do I have the skills to carry out this research? This is where I am going to run into trouble. One of the reasons I can propose this research is that I have worked on a range of different physics experiments. I have papers on laser engineering, fundamental nonlinear optics, classical optics, theoretical atomic physics… the list goes on.
That’s both good and bad. From one perspective, there is no true focus to my research. You can’t pick up my publication record and immediately point to some area of physics and say, “that’s his field.” The European Research Council may not see the specialization that would make it feel certain that I will deliver, but this project makes use of that. It crosses discipline boundaries, and I know enough about every aspect of the research to make it work.
This adds up to me being a risk. It’s easy to make the case that I don’t have the skills to carry out the research. Because I haven’t specialized, it’s questionable that I will ever have the impact on a single field that other applicants may have. I’m missing the research background that says “these are experiments I know like the back of my hand.”
(Of course, I haven’t seen any experiments quite like this before, so maybe no one can say that.)
I have to counter the perception of risk by arguing that my lack of specialization is actually good for this particular project: I know a fair amount about a lot of relevant topics, so I can reach a bit further. For the grant, I have to make the reviewers believe that no one else could carry out what I propose to do as effectively as I could. Specifically, to do this work, you need a background in lasers, optics, nonlinear optics, quantum physics, and chemistry. I have a relevant background in all of these, with the exception of chemistry. And my practical lab experience is directly relevant to the technical aspects of the project.
The other risk, one that I can’t address, is that this all may be a bit too soon. I will be one of the youngest applicants. I was too young to be eligible last year. No matter what I would like to think, experience counts, and I don’t have it.
I haven’t really discussed the role of reviewers so far. I had intended to save that for later, but a few words are necessary. Since the funding agency really has the goal of funding good science rather than good science with a goal, the proposals are really judged on just two factors: is the science good, and is the researcher good. I have already discussed how I might be perceived by reviewers.
How the reviewers will receive the science is actually very unpredictable. I’ve seen proposals with clear fundamental flaws in the physics get great reviews, and funded. I’ve even seen proposals get trashed for no reason other than the fact that the reviewer didn’t like the ideas. In the former case, the funded proposal (and others like it) never achieve their stated goal, but the science that comes out is still pretty good. In the latter case, you get to watch as others publish the results from the very experiments you intended to perform.
The point is not that peer review of proposals is useless—it isn’t. It’s just not as useful as we might want it to be. It is also completely and utterly random.
You may be asking yourself why I’m bothering at all if my chances seem so slim. The plain fact is that it takes most researchers more than one attempt to get this sort of research program off the ground. I will apply now in the full expectation of failing from the perspective of coming away with funding.
However, it’s possible to make this application successful in other ways. In writing down my ideas, I was forced to clarify exactly what I wanted to do, how I would do it, and why I thought it was worth doing. These ideas have been seen by numerous friends and colleagues, who each offered feedback. Provided I make it past the first selection round, I will get even more feedback, this time from the anonymous reviewers of my grant. Even though their comments may kill my application this time around, I can learn from them and craft a better proposal for the next opportunity. In the meantime, I can scramble around for the resources to begin a reduced-scale version of my grander goals. Every bit of research I turn out in the intervening time will strengthen my case in the next application.
By the time you read this, the paperwork will be at the European Research Council. Since it always takes time for grants to be evaluated and decisions to be made, this series will take a break. The long-term plan is that I will continue to provide updates as the grant proceeds through the review process. In the event that I am kicked out in the first round (which means no review and no feedback), the series may continue through progress on a different grant application.
In any case, for now, all I can offer is a meaningless corporate slogan: “Forward to the future.”
Thank you. TiA.