Occasionally, you have an idea, and you can do the required research within a couple of weeks. But this is the rare exception. Most research requires months, and often years, to complete. In particle physics, with its huge experiments running for decades, this is probably even more aware to people than in many other cases. This requires plans. A very recent example of such a plan is the European Strategy on Particle Physics (Update), in which all of Europe came together to make a plan. I have contributed to this as coordinating the theory input for the national Austrian roadmap. It is a huge effort to get everyone agreeing on what to do next - and what to do in the next half-a-century. Because this is how long you have to plan in advance for the big experiments.
Aside from these big plans, there are also smaller ones. Even for me as a theoretician. Occasionally, I have to sit down, and formulate a research plan for a couple of years into the future. The reason is often that I write a so-called grant proposal to get a considerable amount of money to hire postdocs and PhD students. Such a large proposal requires you to formulate what you want to do with all these people, usually for about five years. Last year, we got one already, for dark matter.
This year, I write another one. Why again, if we just got one? Well, on the one hand each would roughly take up half my time. So, I can manage both, and thereby do more. But putting this up front is cheating. The main reason is that it is unlikely I will get it in the first attempt. As there are currently many more people wanting to do particle physics than resources are allocated for this purpose at the national and international level, these resources need to be distributed. Thus, you write a proposal to get some of these. Then some panel judges the submitted proposals, and decides, who will get resources. And thus where efforts in particle physics will be concentrated. Usually, the are many more proposals the panel would like to fund than there are resources available, and so small points tip the scale to one or the other proposals, and the others are rejected. One can then try again. On average, less than one in five proposals is successful. Thus, you often need to try again, with an optimized proposal. And thus, I already submit another one.
Coming back to the original topic: For such a proposal I need to make a five-years plan. Of course, its research. Nobody can guarantee me that I (or, more likely, someone else) will not discover something which requires a fundamental change of plans. This is always allowed. But you are still required to make a plan what you want to do, if nothing unexpected happens. Usually, in my personal experience, about half what is planned will be done, and the rest of the resources is spent on unexpected stuff. Which is as well.
Still, you need to make a plan, if everything happens as you would expect it now. And that is what I did.
The first thing you need to decide is to what part of your research you would like to base it on. If you read my blog since a while, you may have seen that I actually do quite a lot of different topics, ranging from neutron stars to quantum gravity. But not all of this research is something I would like to extend at this level. The neutron star physics is something I currently do not work too much on. It is very interesting. But I would need to focus much more efforts on it, and needed to mainly concentrate on technical details. That is not what I currently want. The quantum gravity part is very exciting, and we develop quickly new ideas. There is much more to come. But currently it is too much at an exploratory stage as I would be able to formulate a large-scale five-years program. This will have to cook for a little time longer before it warrants this kind of attention.
So, I am down to my Higgs physics and beyond-the-standard-model research. For the latter, we are currently having enough people to work on. Also, it is a bit more speculative, as we did not yet see anything new in experiments. It is thus somewhat less easy to identify where to concentrates ones efforts on. The combination of our current research and what the next few years of experiments, especially LHC Run 3, will bring, will make this clearer.
So I concentrate this time on our attempts to find some new, subtle effects from theory in experiments: That there is an additional Higgs contribution inside the proton.
Right now, what we did was making a good guess, and looked, whether experiment told us we are right. Iterating this would be a time-honed approach to identifying a new effect. But for this plan, I wanted to be more ambitious. I wanted to have some prediction that rather just guess and iterate. This is very demanding. As a suitable tool, I choose simulations. While I will not be able to really simulate an actual proton and its Higgs content, the effort made possible by such a big grant should be enough to get a decent proxy for it. Something, which is close enough to the real thing that from a guess I can move to something which only requires a few more numbers, which I can get from experiments. That would be a huge success. We then use slightly different methods to fix the numbers.
But this is not easy. Based on what we learned so far, this is a big endeavour. At least for a theoretician. I estimated that I will need about four people with PhD, plus myself, and five more doing a PhD to get there. Not to mention that many master students and bachelor students will be able to work on this as well. This also means that especially several of the PhD students will work on this project, but will complete their PhD only on a part of it, and be done before the whole project is done. This required me to break the project down into smaller workpackages, 17 in total. Each of them is a milestone in itself, and provides intermediate (and eventually final) results. Each requires several of the people, and each at least half a year of time, and some even a year. I needed to make a plan, how each of them intersect with the other, and how they depend on each other. If you are interested in how such a thing looks in the end (it has a lot of tech babble in it), contact me. But it is actually not that different from any other large scale project, even in industry, like building a house. Thus, you also need some project management skills to do research. Even as a theoretician.
I am quite pleased with how it turned out in the end. It really has a good flow, and a succession of reasonable and manageable steps. In the end, it holds the promise of a guaranteed discovery - i.e. we will see a new physics effect, as long as we just keep on with the experiments, it will happen. Likely by the end of the runtime of the LHC in about 15 years. Or with the next generation of machines latest, which are part of the Strategy mentioned in the beginning. By this, I come full circle: My small research project ties in into the big ones. And together, we push the boundaries of human knowledge just a bit further.
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