Students start to do research by learning the background knowledge and then asking supervisors for projects. After those steps are well done, the students should try to be more creative, generate ideas and find research project themselves. This is a hard but crucial step on the trajectory toward an independent researcher.

I am definitely not creative enough to talk about creativity. Nevertheless, share my two cents with the students who have just started to do research.

For those who have just started research, it is important to practice your creativity. As exercises, one may start with the simplest types of creativities. The ideas that you got may not be important enough to work out and write a paper. Nevertheless, don’t stop practicing to generate ideas and you will catch something big. Once you have an idea, talk to your supervisor for comments.

I am not saying that the ideas of this kind has to be small. Lots and lots of great ideas are of those simplest types.

## The discussion section of a paper

People often mention some future directions in the discussion section of their paper. One may pick up a direction to follow if they did not show intention to do it in the future. This is not really creativity, but still following what other people have said. Nevertheless, this helps to find projects. And it is a good practice to build more explicit and practical ideas based on their arguments.

But be reminded why they did not work it out in the present paper. They may either be technically much more difficult or an order lower in terms of importance.

## Q&A section after a talk

This is a brainstom version of the previous point. The questions raised can be very inspiring.

But be careful to respect other people’s original ideas. If the question and/or answer clearly (the threshold is different for different people though) shows the idea and you are interested after heard it, show your interested to who asked/answered the question and try to collaborate. Never steal other people’s idea.

## Generalizations

When you read a paper, think about how more universal results may be obtained. A good example is the trajectory of generalizing the scalar field dynamics:

slow roll → K-inflation → Galileons → Horndeski → Beyond Horndeski

And if somebody had something for slow roll inflation, there are automatically 4 additional projects as above to generalize its dynamics. For sure, most projects of this kind are not worth to work out. But sometimes generalized scenarios can solve some serious problems of the original model. Then it can become interesting.

## Interdisciplinary thinking

Once you know two research directions, try to marry them in a natural way.

My second research paper, which is the first paper coming from my own idea, is of this kind. I worked on inflationary perturbations as my first research project. I also learned that holographic dark energy can become important again during inflation. So why not study the inflationary perturbations with the presence of holographic dark energy?

Fortunately my supervisors did not laugh at how naïve I was. But rather they helped me to make the idea more interesting and encouraged me to work it out. That is a great practice for me in every sense.

## Reconstruct other people’s key idea

When reading a paper, what’s the key idea from the author? This is typically not obviously written but try to reconstruct that by inverse engineering. Further, how they are able to have the idea, especially if the idea is non-trivial? It’s helpful to go through other people’s path towards creativity, because you are likely to be in a similar situation in the future, and you can use the same creativity pattern.

## Practice creativity in daily life

The more you use creativity, the greater creativity you have. Practice creativity in your daily life helps indirectly for your research ideas. Try improving the things that you are routinely doing in your life. Try different ways and find your optimized way to do it. You have a better life and also likely better papers.

# Get prepared for a nontrivial idea

Now we talk about nontrivial ideas. The generation of such ideas is like quantum mechanical tunneling (or is it closer to the relation between P and NP?). There is no classical solution and you don’t know when it happens. But you can do something to lower your barrier for the tunneling to occur in your brain. Don’t rely on pure luck and wait. You know the tunneling rate is exponentially small if you don’t do anything.

## Taste

Direct your ideas towards important problems.

You may be doing research for fun, not for its importance. Nevertheless, mysteriously, important problems are typically fun. Also, proposing and solving important problems make sure that you can make a living by fun.

What’s good taste for research? Good taste is subjective and objective. It is subjective at the frontier of research and objective after decades when the people with good taste are recorded in history and the people without are forgotten.

Talking to great people helps a lot. In addition, think about the past and the future.

Think about the past. How people make crucial choices in the past among possible theories, with incomplete knowledge about them? Is there any logic beyond pure luck for their choice?

Think about the future, if your work turns in to a paper:

• Will your work be noticed once it appears on arxiv?
• Is it a shame for the researchers in this field for not having read your paper?
• Will it be mentioned in review papers?
• Will it be written in textbooks?
• Will it be remembered after a year, after 10 years, after 100 years?

Do not think about the standard for being published. That is either too low or too random. Do not think about Nobel Prize. That is not instructive. (But the list of past Nobel laureates is a good collection of people that you can analyze how they are successful.)

## Be a modular learner

In the real world, things are always related. But try to modularize your knowledge. It is similar to why programmers has to program in a modular way:

• Things can change. The more advanced topics you learn, the more adaptive you have to be towards new knowledge. Be modular then you are open to changes and know the minimal and enough amount of knowledge that you need to update for the new development.

• The capability of our brain is limited. We can only think about a simple thing at a time. Thus once your knowledge is in small trunks, you can make use of it with less efforts.

How to modularize knowledge? Refactor what you have learned as how programmers refactor their code. Use standard technique, easier mechanism and less dependence to organize what you have learned. The process is also similar to how mathematicians diagonize matrices into a block-diagonal form, or how physicists divide a system into free and interaction parts.

## Be a deep thinker

For some students, when they start to do research, the workflow may be as follows:

for project from ideas_of_supervisor:
project.learn_calculation_technique()
while project.not_completed:
while project.know_how_to_calculate:
project.calculate()
project.poke_supervisor()
project.write_paper()


This is an efficient way to generate initial papers. However, it is not a healthy or sustainable way to do research. It is not the fun way to do research. Also the loop breaks sooner or later, e.g. when you get your PhD.

Jump out of the loop and think deep. First ask “why” before asking “how”. If you only know “how”, you are doing applied math and solving problems, and only after you know “why”, you are doing theoretical physics, including finding and solving problems.

Also, only if you are deep, when something looks wrong, you can find out the underlying reason why it is wrong. The knowledge of “how” without understanding does not help.

## Know and try open questions

There are lots of open questions around. There are different dimensions to classify the problems. Get to know them and deal with them accordingly.

• Impact of the problem.

– Big problems, for example, nature of dark energy, cosmic singularity, the true theory of quantum gravity. It is very easy to get a list of big problems (just Google) and they stay unchanged for years unless something ground-breaking happen. It is extremely hard to perfectly solve them. But keep them in mind! You may be the one, and more practically, defective (but not wrong) solutions may also be considered interesting for such big puzzles.

– Intermediate problems, for example, trans-Planckian problem, CMB anomalies and whether graviton can have a mass. It is not easy to Google a list. But if you check arxiv, go to talks and discuss with people, you have in mind a number of them. A possible candidate solution makes an okay paper; a natural solution makes a good paper and the complete solution can find a position for you.

– Small problems. There are too many. Be cautious to the importance of them. But it may be nice to solve them perfectly, or solve a few small problems altogether. More importantly, some small problems are clues of discovering or solving greater problems.

• Aspects which limits the solution of the problem, experiment or theory.

– Experimentally limited problem, for example, dark matter. As a theorist, wait for the chance (warm up before the chance and be quick afterwards) if you want to attack those problems, like Liang Zhu-Ge prepared for Mont-Qi.

– Theoretically limited problem, for example, dark energy. Know the literature and wait for your ideas.

Try to solve the problems in your own ways. Even if you cannot solve it, try to. That makes sure that the problem does not only stay in your notebook, but also deeply live in your mind. If the problem does not live in your mind, don’t expect you can have a solution.

## Discover open questions

Think about the logical connection of every pieces of a theory, without taking anything for granted. A good situation to do so is when you are writing a study report, thesis, the introduction of a paper, or at best totally a review paper.

I call this type of thinking analytic – your understanding of the whole theory should be like an analytic function – you can think about every problem in every possible directions, and they all converge at a consistent result. Otherwise, the non-smooth stuff should draw your attention.

If you find anything unnatural, dig until you reach the deepest origin. Then typically you end up with understanding the theory better. But sometimes you found the true obstruction. Then you discovered an open question.

# Welcome the idea to arrive

## Keep the problems deep in mind

Again, plant the problems as deep in mind as possible. That makes sure that you shall not miss a solution when you come across it.

Also, if you merely remember the problem, then you are not working on the problem when you are not thinking explicitly. While your subconscious keeps working on the problem once it is deep in your mind (you can recall the whole thing without any efforts). The subconscious plays a crucial role in creativity.

## Put together knowns and unknowns

The situation here is surprisingly similar to a quantum mechanical effect: the resonant tunneling. Generate an idea – either create a new direction of research or solve a problem in a nontrivially clever way – is exponentially difficult like a tunneling event. You have to overcome a barrier, sometimes multiple barriers, by almost random fluctuations in your brain.

However, by putting the correct things into your working memory (roughly speaking like the processor register in a CPU), the “tunneling” process is greatly assisted.

The thing you put in may be another problem, but usually, it is a piece of your knowledge. This is why you need to make your knowledge modular. Then each small piece can be put into your working memory easily. The surprising similarity with resonant tunneling comes here. Your piece of knowledge is really like a bound state, which is well bounded not only in the sense of knowledge, but also (in my naïve feeling) well bounded in how the neurons in your brain is connected.

 Once the bound state is right, everything become clear suddenly. A analogue is the this type of games -- once you put the right things together, reaction emerges. But the non-trivial thing is that what the right things are.

## Discussion

Discuss the problem. Even if you do not have anything particularly smart to say about the problems, you can still discuss it in informal situations. For example,

• Explain the problems to whom interested. It seems a service. But talking put your brain in a special mode and inspires you to think. Some ideas may appear in an intangible way. Try to catch them and think deeper right after the discussion. Be quick. The intangible feelings are hard to remember for long.

• Ask other physicists’ opinion about the problem. Their opinions may not converge at all, otherwise it is not an open question. Those different opinions are likely to be reasonable in one way or another. Put together their most reasonable points and see what you get, and search for logical possibilities to reconcile the contradictions.

## Be yourself at creative moments

From your experience, know which is your most creative moment in a day. Find a quiet place and reserve some free time at that moment, say, 15 minutes to half an hour, and just relax. You may take a coffee or tea, but do not use your cellphone or check emails. Be yourself at that moment. Restrict your mind to the interesting questions a little bit. Say, initially think about some interesting papers or big questions. Then let your mind free.

It is not a waste of time from my experience. Even you get one idea in a year, it is worth to do. Also, I often recall that I almost forgot to do some important things in this situation.

Do not let cellphone (emails, Facebook, WeChat moments, …) fill your free time (and also the “register” of your mind). Remember that free time is creative and filling free time hurts creativity.

Interestingly, sitting in a seminar with related but unfamiliar topic can be moments of creativity. Students often skip such seminars, or start to focus on cellphones/computers when they get lost. This can be a waste of opportunities.

# After the Eureka moment

## Well-define the idea

Formulate your idea into a precisely math problem. Figure out what technique to use and what to calculate. Note them down explicitly.

It is very likely that your plan gets modified significantly during the actual research. But then you need a plan anyway and the modification gives you experience about planning.

## Make sure your idea is new

Take a look at arxiv everyday. Then you are likely to know what ideas are not new in your research field.

Figure out the several most important papers in this direction. Take a look at the papers which cite the important papers. That typically helps to make sure your idea is new.

Ask the experts in this direction who you trust. There is also a chance that he/she would like to collaborate with you. That’s typically great for your professional development.

## Work it out

You have the experience to do research. So it is a piece (may be a big piece though) of cake!

## With extra care, but do not be afraid

Things can easily go wrong when you are exploring a new direction. All relevant factors have to be considered and it is difficult not to miss any single one. This is another level of difficulty compared to double check the calculation to avoid algebraic mistake. Think over and over again from all directions.

Do take the challenge. This is the important step towards being great!