Learn to Enjoy Frustration!

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At the 2010 annual meeting of the Institute of Neuroscience, Chinese Academy of Sciences, Director Mu-ming Poo said, “It won’t take too long; after this presentation today, I have to catch a plane... First, I’d like to talk about this year’s annual meeting—it was a very unusual one. This year, we had the highest number of external organizations participating. In previous years, we invited at most one organization; this year, we invited three. As a result, each group had fewer opportunities to speak. However, the topics discussed were more diverse, and there were more chances for exchange.” I believe everyone has some thoughts after listening to the three days of talks. Three days ago, I hadn’t decided what to talk about; however, after listening to them, I feel it’s necessary to bring this issue up once again. Innovation, innovative people, innovative research – we talk about innovation these days; the whole country is talking about it, and newspapers report on innovation every day. I think my views on innovation – there are some things I’ve said many times over the years, and some people who have been at the institute for a long time might consider me tedious for saying them, but now I have the right to be tedious, as I’m an elder... Innovation. What is innovation? Let’s first think about what true innovative research entails. There are many types of innovative research. There is theoretical research, in which one develops a new perspective on natural phenomena and proposes new concepts or theories – this is the kind of innovation seen in theoretical scientists ； In our field of biology, most research involves experimental science. There are many types of innovations in experiments. For instance, one type is observing new phenomena—phenomena that others have not noticed. You design a very clever experiment that allows you to observe natural phenomena which can only be seen under your experimental conditions, but not by others. Examples include sub-molecular and sub-atomic phenomena; these are phenomena that became observable only after various new technologies in physics, such as accelerators, were developed. What was previously impossible to see in biology can now be seen more clearly with two-photon microscopy, as well as with new microscopy methods. These are all innovations – technological innovations, as well as innovations that arise from the observation of new phenomena. Another form of innovation is when, rather than discovering a new phenomenon, one manages to clarify the causal relationship between two phenomena that others have observed, thereby establishing a new connection and advancing our understanding of the natural world. Others observe this phenomenon and then that one, but they don’t understand the relationship between these two phenomena. By clarifying that relationship, that too is innovation. Also, even if you don’t have this, and you use phenomena that others have observed, but you have a new analytical method that allows you to explain those phenomena better, that is also considered innovation. Right now, we often talk about innovation. But for many people who have just started doing research, they wonder how they can be innovative. At present, I can only use the techniques I’ve learned—all of which belong to others; I can only observe phenomena that others have discovered. How can you have opportunities for innovation even when you are just starting out? I think the simplest example is this: you have some data at hand. Generally, when you want to analyze the data—whether it’s microscopy data or biochemistry data—what methods do you use for analysis? Most of the time, people simply follow what others have published before; they do exactly as others do. This is the most common scenario. Well, in fact, as a graduate student engaged in original research, you should consider whether you can develop better analyses based on others’ methods – more quantitative ones, or even using new types of graphs; if no one has drawn such graphs before, then your creation of those graphs represents something new. Often, graduate students bring me data and say that I don’t know how to analyze it. Ah, this is the best-case scenario! Since you don’t know how to analyze it, it means that no one has worked with this data before; you have no examples to follow, and you can’t use the analysis methods used by others. This is the best time for innovation, the best opportunity ； You need to come up with a way to conduct the analysis; that is innovation in methodology. The same goes for drawing; when you look at the papers, the most boring ones are those that simply describe methods that have already been used by others—there’s no further advancement ； Although it’s similar data, presenting it using a new method makes it seem fresh and novel; this is innovation. There are innovations at various levels. We are all engaged in research; for example, when analyzing dendrite branches, I see that people follow the traditional analysis methods, but many details are not taken into account. When looking at dendrite length and branch points, many other parameters are ignored, and numerous details go unnoticed – such as counting the number of spines. In the past, spine intensity was not considered, but from a quantification perspective, spine intensity is actually also valuable information. Therefore, I’m glad to see that the students in Yu Xiang’s group realized that the differences in spine intensity also contain useful information when conducting their reports. This is great; most people working on spine analysis fail to take this into account. Any further step in the analysis can be tried by those present, including those who have just started. Also, when you apply methods from other fields to your research—methods that haven’t been used in experiments within your own field—that too is innovation. Also, everyone says that innovation means finding new things, observing new phenomena, and acquiring new knowledge. This is an innovation, but there is another kind of innovation that I think is even more important, yet it is rarely implemented. These days, everyone is engaged in research. From what I’ve seen at this annual conference, the work you’re doing isn’t that much different from that done by other laboratories around the world, in Europe and the Americas. It’s competitive with their work, but it’s not certain that you can compete with them, because those top laboratories abroad have excellent resources, great equipment, talented students, and a favorable working environment. If you’re just starting out in this field, then you’re at a disadvantage. So I say that there are two types of innovation in research: one type of innovation is truly early-stage – it involves figuring out what those who came before did and what the next step should be; you need to discover new knowledge and new methods, and that is innovation ； There is another approach as well; actually, it can’t be called an innovation. I call it “retrospective research.” It involves using current methods to examine old problems. You don’t necessarily need to develop new theories or new phenomena – you can simply re-examine the phenomena that have already been observed, using new methods to do so. For example, resolving the issue at hand now is also a form of innovation ； Although it’s not the question you asked or the phenomenon you observed, you used new analytical methods and new experiments. Even the contents in textbooks—those concepts and theories are conclusions drawn from experiments conducted 30 or 40 years ago, using very old technologies and superficial data. Yet they’ve made it into textbooks because they’re considered important; no one bothers to re-examine these issues anymore. You use modern, new methods to design experiments in order to revisit old problems and old hypotheses, to test whether they are correct. Basically repeat the experiment, but be sure to use a new method. I believe that 50% of the experimental results confirm the original findings, while 50% of the original experimental results are not conclusive. As we all know, on average 50% of the content in textbooks is incorrect and needs to be revised; however, we don’t know which 50% it is, so you can carry out this task. It’s a win-win situation: everyone likes learning new things, and no one repeats experiments, as there are no credits for repeating them. After all, people say that masters did such things 20 or 30 years ago; so what’s the point of doing it now? Isn’t it just causing trouble? However, it’s very likely that you will reopen this issue; in fact, this kind of retrospective research constitutes an innovative form of work, and its results are just as important as those from earlier studies. After all, scientific progress involves constantly revising our current knowledge, and during this process, the accumulation of new knowledge and phenomena may force us to change our existing views – and that’s generally how things work these days. When new knowledge begins to accumulate, any inconsistencies are masked. But once there are enough inconsistencies with the hypothesis, one is forced to modify the hypothesis—to change the current theory ； This is what we call a paradigm shift, Thomas Kuhn’s paradigm shift. A paradigm shift becomes necessary once new knowledge emerges. But this kind of retrospective research approach I’m talking about directly attacks and checks the foundations of current opinions, right? You simply look at where there is a crack, and then you either consolidate that foundation or knock it down. If you have a 50% chance of winning ； For the other 50%, you’re not a loser either, because you used a new method to confirm an existing phenomenon; you can also publish a paper, and it will be an important paper, as your results represent an important confirmation. I have been advocating for at least a decade to go back to the old hypothesis, to conduct experiments and repeat them. I can say that several of the successful results achieved in my own laboratory were achieved by revisiting that hypothesis. This is the advantage of revisiting old hypotheses; it allows one to open up new areas, especially for young researchers. So there are many forms of innovation; it’s not necessarily something new. But we say that when everyone conducts original research, it is, in principle, something new; the experiments that we see at today’s annual conference are all ones that haven’t been done before. But are they truly very innovative research? Most of them are not; they all follow current trends. Everyone’s hypotheses are just for verification, with little addition of original ideas, and there’s no real potential for true innovation. Why? Because the problems you are solving are not hard questions; they are all details. The issues related to the overall framework are the most important ones. It’s not the case that new work is automatically innovative; innovative work must have an element of surprise, something that catches people’s attention and makes them think, \"How did I not think of that?\" There should be a element of surprise in the results, some hint – only then can it be considered innovative research. Why is it like this? Why do people pay attention and become surprised? Because I don’t think it is that way at all; it’s not something that falls short of my expectations. In other words, true innovative work must be linked to importance; innovative sciences must deal with important, unsolved problems. What is an important unsolved problem? There are two unsolved problems. One type of unsolved problem is one that we know can be solved someday – a problem that is known to be solvable. For example, sequencing the human genome was considered an important problem in the 1990s; it was something that everyone was aware of. It’s definitely solvable; you just need to carry out the sequence, it’s just a matter of time, as machines weren’t that good back then. But you know, if you have the resources and manpower, you can tackle the problem. Nowadays, in neuroscience, the important problem that can be solved is the connectome. In principle, we can map every connection in the brain; what’s needed is hundreds of people to carry out this task. With current technology, it would take hundreds of laboratories working for hundreds of years to map every branch and every connection. The technology exists; what’s needed is a way to analyze it and to understand its meaning. Currently, there are many centers abroad working on this; for instance, there’s the Centre of Neural Connectome, which aims to map the connections in the cortex. That said, it’s not impossible for China to do this as well, as long as it makes the effort. But I don’t think this is the best way to solve the problem. The genome has been sequenced, but it hasn’t solved any disease-related problems; we still need to understand the functions of genes. It’s important, but it isn’t the best problem for you to devote your life to. Regarding the human genome, back in the 1990s there were no sequencing machines; now, sequencing can be done in just one month. In the past, it took ten years to complete this task. Therefore, those people who spent ten years on it during the 1990s probably regret it. They could have used that time to work on more important problems. The second type of problem involves people having little or no idea as to how it can be solved. There are many problems that remain unsolved yet – why is that? Because we don’t know what the best way to start is. There are some clues we can start with: language, perception, and even more complex aspects like consciousness – all of these are very important issues. The most important question in neuroscience is to understand the human brain, and the most crucial aspect of the human brain are its human-specific properties. Yet we have little idea as to how to approach this task. This is where it becomes critical; these important questions can be solved, and it is here that one can apply their intelligence. Next, it will be discussed how to choose questions. Peter Madewar once said something that I think everyone has heard; I’ll say it again. Peter Madewar is an immunologist and Nobel Prize winner; in my opinion, he was the wisest man in biology in the 20th century. He wrote many books, and they are very interesting to read if you go to our reading room. He said that science is the art of solvability. By this, he does not mean that science is simply about finding solutions to problems. What he really means is to find a problem that is \"solvable\" by you at this time. What you need to choose are the important problems that are within your control and can be solved at this moment. How to choose? This art cannot be explained in just a few sentences; it is something that one must learn throughout their life. Everyone learns in different ways, comes to different conclusions, and chooses different issues; everyone has their own style. The difference lies in the fact that when choosing a problem, you always have some clues, but it depends on how willing you are to take risks based on those clues – whether you prefer to conduct more conservative research or riskier research. Everyone has a different style, a different approach; everyone has their own way of doing science. I think this is the most important thing: how to make a choice. Even now, when you face a difficult problem, it’s important to consider whether you have the ability to solve it. If you feel confident enough to overcome the situation deficiency, you can take the risk and make that choice. This is a major issue, so when it comes to Hu Shi’s words, he said one should \"formulate hypotheses boldly and verify them carefully\"; of course, he was referring to the process of verification. The same is true in science: one needs to pursue innovative science, to do things that no one else has done before, to discover something new. It’s like exploration – one has to find new paths. In the process of exploration, you must take risks; otherwise it’s not exploration ； If you don’t take risks, you won’t reap any benefits; you won’t find treasures or new paths. This reminds me of the saying, “Where it’s easy to reach, many visitors gather.” ； If the distance is great, few will reach it. And the wondrous, magnificent, and extraordinary sights in the world are often found in remote and dangerous places, areas that few people venture to visit; therefore, only those with determination can reach them. So one must be bold in making assumptions – propose hypotheses and set goals. I recall this quote: In biology, any mechanism you can imagine, as long as it is useful to the organism and does not violate physical and chemical principles, is likely to be utilized by the organism. (Poo’s Dictum) It is your imagination that allows you to conceive such hypotheses. Such hypotheses should not violate any principles, just like your motives shouldn’t either. As long as a hypothesis is reasonable, you can pursue it – and that is what it means to be bold in making assumptions. I’ve said this sentence many times; I think I’ve heard it from someone else or read it in some book, so I try to find that sentence, but I can never locate it. Since I can’t find it, I claim it as my own… You can’t say where an idea comes from; that’s a very important thing. Everyone wants to claim intellectual property for themselves. But it’s difficult – was it told to you by someone else, or did they tell you half of it and you had to figure out the rest? It’s hard to say. So I believe that in science, not in technology, intellectual property is nonsense. If everyone tried to claim intellectual property rights, the world would be in chaos; there would be no communication within the scientific community, and no real progress would be possible. The scientific progress of the past 20th century has entered the 21st century; if it remains the same, it will start to decline. Scientific progress in the 21st century relies on communication. It wasn’t until the 1980s and 1990s that molecular biology was used to commercialize science, which has led to a chaotic situation today. How to innovate? I’ve talked about this in class; some students might have forgotten, so I need to explain it again. 1. Knowing how the facts are obtained is more important than knowing the facts themselves. How he did it, and why he thought of doing this work—he won’t mention any of that in his paper. The most important findings are unexpected; they are not what was originally intended to be discovered. The true purpose will not be told to you, nor will it be stated in the paper – this is part of the style of writing papers, a result of the rigid conventions of science. But we know that there are often first-class scientists around, so I ask the students to ask questions. Next time, if you can’t think of a question and stay silent, then raise your hand and ask a standard question, such as “Why do you conduct that experiment?” ”I tell you you’ll get the best answer; he’ll say, Ah, that’s interesting! We were working on this thing, and then we found it and finally succeeded. ^^So in the process of innovation, you have to search for it. I ask why we should have lunch with these visitors – it’s so we can ask them questions. Here, there are 5 Ws: What, Who, When, Where, and Why. The last four Ws constitute history—the foundation of innovative work. Knowing how each innovative endeavor came about has a subtle yet significant effect. I’ve already told you a lot about this book; today’s first prize is this book. I have the original edition from 1979 of this book; it has been kept for 30 years, and it won first prize this year. 2. Knowing how to find the facts is more important than knowing the facts themselves. There is too much information, and having access to it can be detrimental; we are facing an information overload problem nowadays, as too much information can restrict one’s imagination. Because every piece of information seems to be a fact, claiming with certainty that I have discovered this or that; as a result, after reading countless papers, you can’t do anything, you don’t dare to do anything, because your way of thinking is restricted. So don’t simply download and read all the papers. Students in lower grades should pay extra attention to this; before entering a lab, it’s most important to read a few review papers. There’s no need to read all of them – read them only when you need to do a particular task. Don’t spend your whole day downloading papers, as this is just as harmful to you as smoking. Excessive reading is detrimental to your health. “The path of learning is endless; it’s never too late to turn back.” 3. Knowing how to present the facts is more important than merely knowing the facts themselves. Human thinking is quite peculiar; you must train yourself to articulate your thoughts. The process of speaking itself constitutes integration. All presentation is a process of logical integration. Present your ideas in a linear manner, establishing a clear sequence: determine what should be said first, what afterward. General discussions are very important; I think the presentations at the annual meeting have seen great improvement, and everyone was very serious. Science is a social phenomenon; lock me on an island, give me unlimited resources, prevent me from talking to others, and let me do research – would I want to do that? I’m not going to do any research; I’d rather spend my days in the sun… I think no one appreciates what I do. Only when people understand what you do can you feel that you’re creating something useful. So you must engage in social communication; you need to interact with others. It’s not possible to work in isolation, without talking to anyone, and just focus on conducting experiments. Moreover, part of the fun in science is communication. We know that in the past, in molecular biology, a group of 40 people was responsible for advancing the field. They had their own RNA Tie Club; each member of this club wore a tie that represented an amino acid. They were all interested in figuring out how coding works—how nucleic acids are encoded. Yet none of them published any papers ； The function of this Tie Club is to host unpublished communications, letters, and short notes; that’s where its appeal lies. Many of Francis Crick’s important papers were not published and instead appeared in the communications of the RNA Club. 4. What’s unknown is more important than what has been known. You need to know what an unsolved problem is, as well as what a solvable problem is. All current knowledge is incomplete, flawed, and unreliable. Either fix the questionable issues, or acquire unknown knowledge. What’s important here is to read review papers ； I just said that reading review papers is important, because you don’t need to read too many papers. When reading review papers, you need to decide which review journal is the best; you should check whether the person who writes the review has an overall understanding of the topic and whether they have extensive experience in this field. There are many review papers that have hundreds of references. The more references a review paper has, the worse it is; this is because the author doesn’t know how to make a selection. They mix together both reliable and unreliable sources, as they don’t want to offend anyone. A truly good review points out what’s important. It clearly summarizes what is known and what isn’t. There are many things that seem to be known, but the reviewer says they’re unknown; he states “we don’t know,” and this is debatable. You need to distinguish between what is unknown and what is known. Don’t simply choose the paper with the most references, as doing so could have the opposite effect. 5. Educating yourself is more important than finding someone to educate you. We often complain about our environment – without a Cavendish Lab where a mentor can guide you, you only have a 50% chance of winning a Nobel Prize. But times have progressed; we no longer need these masters around us. Why? There are now many firsthand accounts available; every famous scientist has written about how to conduct innovative research, and their writings explain things more clearly than if they were speaking in person, as what they write is the result of their careful reflection, and it contains only the most essential ideas. You can go read in our reading room; if you need a master’s guidance, go study there. There are also many autobiographies that describe how they made their discoveries. And if you don’t want to read books and just want to go online, then visit this website: http://webofstories.com. Some students have visited this site – do they like it? As long as you like science, you’ll be stuck in it – there are hours of interviews involved, during which he talks about his background, why he was able to conduct that experiment, and what his experience is. We have limited time; there are still a dozen minutes left. I’ll just mention a few notes. I talked about making bold assumptions earlier, but I haven’t mentioned the need to verify them carefully yet. Cautionary notes for innovative research: Be rigorous in every step of your work; Be receptive to criticism; Learn to deal with frustration. To take bold assumptions means ensuring that your risks yield results – choose a path that no one else has taken, select the right path for you, and be rigorous at every step. If your preliminary findings do not support the conclusions you draw, it means you have missed a step, which could lead you down the wrong path. If you want to achieve a goal, you must stay true to your outcome. In this process, one also has to accept criticism. What is criticism? Once the paper is submitted, you must accept the criticisms given by the reviewers. Many people say that reviewers act as adversaries who try to undermine you; perhaps there are indeed some unfair reviewers, but most of them, especially those from high-quality journals, provide fair reviews. He dare not be unfair; if he were, the next time the Journal editor wouldn’t let him review articles. Most people would consider their own careers first. Moreover, most reviewers are useful; I think the greatest achievement of our Institute of Neuroscience over the first decade was an increase in publications, as early PIs respected the opinions of reviewers ； Whatever criticism they give you, you go and fix that issue first, then send it back. So be receptive to criticism, even sometimes it is negative. And most people give up at that point. The third is to learn to deal with frustration; innovation is not an easy task. If it were easy, everyone else would have done it already; why would they need you to do it? Therefore, when dealing with important issues, one is bound to encounter many setbacks, it will take a long time, and the reward may come slowly; but to achieve one’s goals, one must endure these difficulties. There have been many setbacks, such as the frustration of not being able to obtain funding, and the frustration of not being able to conduct experiments. Many people ask me what makes a good scientist, a successful scientist. I say that learning how to deal with frustration is the guarantee of success. This is extremely important. I say that adversity breeds creativity; in other words, without frustration, you can’t create anything good. A smooth-sailing environment often fails to inspire you to produce your best work. We say that the best works of painters and writers come about during their most difficult times; once they earn a lot of money, their works become of poor quality. Xu Beihong studied painting in Paris; he didn’t even have money to buy bread when he was hungry ； During the War of Resistance, those historical and portrait paintings created in the rear area, such as those depicting 500 brave warriors, were all created in times of great hardship. Why were the paintings he created at that time the best? I think there’s a logic to it: when faced with difficulties, somehow, I don’t know why, it stimulates your creativity even more – you’re driven to overcome those challenges, and through creation, a solution can be found. The story of Xu Beihong is also very interesting; he insisted on creating many paintings because he had to pay for them. If you want to know the story... His ex-wife insisted on getting his paintings – hundreds of them – before he could get a divorce ； So, in order to get a divorce, he had to paint; under extreme hardship and frustration, he created many excellent paintings. So, to put it another way: if you currently feel that life is comfortable, that you have more money than you can spend, and that you can easily publish papers of average to good quality, then this means you need to put yourself in difficult situations. You must find harder problems to solve in order to break out of this comfort zone. Some very famous scientists switch fields every decade; our board member Charles Stevens is one such person. He feels that he’s done enough in his current field—there are no more challenges left. New problems, on the other hand, represent challenges. A challenge is essentially a difficult situation; by overcoming it, one can reach a higher level. This explains why not everyone can achieve accomplishments like those of Mr. Pu. OK. Thank you! Happy New Year! Finally, Mr. Pu’s advice to graduate students is: Learn to enjoy frustration!