牛人就是牛人!一年4篇Cell!拉斯克奖得主Ronald分享科研经验

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牛人就是牛人!一年4篇Cell!Ron Vale 1959 年出生在了加州好莱坞。21 岁从加州大学圣塔芭芭拉分校毕业,主修生物和化学。其后到斯坦福大学念双博士(哲学博士-医学博士),26 岁获神经生物学哲学博士。因为他的研究生记录太好,他就只要哲学博士,不要医学博士。他 27 岁做助理教授,35 岁做正教授,42 岁当选美国科学院院士。

他 20 岁时开始发表论文,是两篇论文的非主要作者。1985 年,他 26 岁,发表 5 篇『Cell』论文,其中 4 篇是第一作者。加上这 4 篇,他在研究生期间共发表 12 篇第一作者的实验论文。这一记录,大概是现代生命科学研究生的上限。他的论文解决了一个重要问题,将研究推到了新层次。

到此你以为NB结束了,没!牛人NB之处正如绝世高手,随手任何一样东西都可以成为最厉害的武器。这位牛人他在获得拉克斯奖后,把获奖感言发表在了『Nature Medicine』(IF=22.864)上! 像这种杂志,很多人一辈子想都不敢想的,人家随便发点感想就上了。除了NB之外,我真是无语了。来膜拜一下这篇奇文「How lucky can one be? A perspective from a young scientist at the right place at the right time」

牛人就是牛人!一年4篇Cell!拉斯克奖得主Ronald分享科研经验

穿着印有驱动蛋白(Kinesin)T恤的 Ronald Vale

你能想象当我和我的朋友也是同事James Spudich和Michael Sheetz在一起时,我接到电话说我荣获了基础医学研究 Lasker Award奖时的兴奋么?Lasker Award所奖励研究的重要部分从我研究生时就开始了。当我第一次遇见Jim Spudich时,我只有21岁,那时,我正在申请MD-PhD。当Mike Sheetz,Tom Reese, Bruce Schnapp和我开始对轴突输送进行研究时,我23岁;当我们的有关微管运输和驱动蛋白的论文发表时我25岁;当我在旧金山加州大学(UCSF)开始我的第一份工作时,我27岁。对我而言,那是一段极其不平凡的时光。我深感自己在恰好的时间处于恰当的位置,同时我也享受生命中科学带来的愉悦。撰写该文,目的是对那些年轻的刚刚开启学术旅程的科学家说一些有感而发的话。我将从我自身在校学习及对驱动蛋白的发现的经历出发,写一些观点及10条经验之谈。

读书到研究所及驱动蛋白历史的简短回顾

1980年,Jim Spudich在斯坦福大学对我进行了MD-PhD项目的面试。我们交谈非常愉快,他的建议对我的录用非常重要。彼时彼刻,谁曾想我们将来某一天会共享Lasker Award 的荣誉?我的论文导师Eric Shooter是一位杰出的生物化学家和神经系统科学家。跟随他后,我开始学习配体结合和神经生长因子(NGF)受体的生物化学特性。

同时,由神经生长因子与其受体结合发出的信号如何回溯至细胞核的问题深深吸引了我,带着这个问题,我开始翻阅大量有关轴突运输的文献。1982年,我学习并深入了解了Jim和Mike Sheetz正在做的完美实验,即重建肌球蛋白包衣珠随着肌动蛋白缆的运动。我不知道是否可以用相似的肌动球蛋白机制来解释膜囊泡的轴突运输?Mike和我决定通过乌贼巨轴突来验证这个想法。至于为何要选择乌贼,是因为Robert Allen,Scott Brady,Ray Lasek以及他们的共同作者写的一篇里程碑式的论文。在这篇论文中,这些研究者通过使用Allen新发明的视频增强显微技术来对巨轴突中的轴突运输进行成像。在此之前,人们从来没有如此清晰的看到过一个活细胞内部的精美细节。目前,通过显微镜而不是那时仅有的费时费力的放射影像实验,人们可以在10分钟的实验中对轴突运输进行研究。

十诫

以下是我从自身经验中总结的十条经验之谈。我全神贯注于科学中,时而犯些小错误,并从错误中学习,对于科学将把我带向何方,最终我将有何成就我几乎从来没有想过。

1. 寻觅良师,学习他然后发展自己的风格

从你周围的事物中学习。科学与哲学相似,都是来处理问题,在试验进程中,需有个人风格及与其他人的合作。作为一名年轻的科学家,你需要接触不同的科学研究方法,从比你资深的科学家哪里汲取思想及治学态度。这种吸取的混合营养最终会沉淀成为最适合你的一种风格,也将让你身上拥有你所钦佩的人的气质特征。既不极度崇拜谁,也不轻视谁。我深感幸运,因为在我成长过程中遇见了许多不同寻常的导师,他们是由Bruce Schnapp, Tom Reese, Mike Sheetz和Jim Spudich组成的核心团体。从他们各自独一无二的个性及科学方法上我所获甚多。但是,他们拥有一个共同点:都非常友善,且支持我成为一个年轻的科学家。在我研究生期间,我也遇见了对我影响深远的英雄人物。第一位是我的导师Eric Shooter。试问,能有几位论文导师任他的研究生漫步于他的课题之外,或做一些与实验室工作无关之事?且任其对学分不上心?那时,我还不完全明白与其他许多科学家相比,Eric对他的实验室「家庭」是多么的无私。在MBL,我也遇见了活跃的老科学家Shinya Inoue和Andrew Szent-Gyorgyi。他们拥有虽小但非常专注的实验室(不像斯坦福的大多数大实验室),他们热爱生活,热爱科学,并不会对任何一方做出很大的让步。

2. 选择一个重要的问题

每个人都是这样,情愿去解决一个有趣的问题,而不愿意触及一个无聊的问题。然而,确定一个既重要又刚好时机成熟到需要解决的选题并非易事。此外,几乎大部分人都会按部就班的生活,在规定的时间内获得学历、找工作或者获得资助。这致使我们中的大部分人在大多数时间里,精力并不是专注于生物学中的大问题上。然而,如果你想不一样,在一些重要问题上,你必须保持警惕,还要比别人多思考一些,从而能寻得一些针对解决这些重要问题契机或入口,即使这些问题并不是你所研究的领域或你的专长。如果机遇来临,要学会抓住它(见下一建议)。大多数时候,如果你在最开始的时候不能提出一个重要的问题,你是不能做出重要发现的。

3. 领先并抓住机会

在Eric Shooter实验室的前两到三年,我发表了几篇内容翔实但并不是非常杰出的论文,但是我心里清楚,这几篇论文足够获得博士学位。有了这个安全保障,我就有闲心去寻找并开始重要但是也有风险的项目了。机会伴随着对Sheetz/Spudich试验的接触而来到我身边。整个轴突运输项目都是一个冒险,它从最后一刻决定去Woods Hole而开始的。将科学当做一个大冒险使得整个事变的有趣,也使得许多无论在科学结果方面还是自己个人职业生涯中未预料到的事情发生。

4. 阅读文献但是不要被文献所困

刚进入一个新的领域,由于它的漫长历史和大量文献,难免会有些底气不足。这时你需要了解前人所做的工作,但是最好避免陷于各种各样先前试验中,同时也要避免一直沿着现存模式的思考路线来思考。用新鲜的视角来看待历史资料是个好事情。我刚接触这个领域时,快速轴突运输已有很长历史,也有大量的相关文献,但是我发现,描述其发生机制的资料很少。然而,由于Allen,Brady和Lasek视频显微镜研究对运动的小囊泡成像提供了新方法,使得这成了关键的转折点。继续向前,通过生物化学和不再对药理学的坚持来简历方法就行得通了。而之前,对药理学的坚持主导了整个工作。

5. 做好实验不必一定要有顶级实验室

我的实验室在斯坦福大学的一个相对较新的大楼中,它有些陈旧却井然有序。而位于海洋生物实验室中的Tom Reese的研究室则相对较乱,在Loeb大楼的地下室的一个小房间中,只有一台化学试剂单放机和一些铺满设备间的小设备。我们在被海水熏的潮湿的地下室房间中解剖乌贼巨轴突。我们戏称这个小房间为「海王星的洞穴」。但是这一切都没有产生负面影响,相反,与那些在现代大楼中流行的井然有序却单调的实验室相比,这个实验室让人耳目一新。Tom的实验室有符合目前水平满足基本工作需要的设备-视频灯和电子显微镜。但是在对驱动蛋白提纯的初始阶段,我们楼里没有离心机,所以我们不得不到马路对面的楼中去进行这一步,那时也没有色谱分析设备。但是,一个人可以适应任何环境然后使其正常运转。这也是科学探险一部分。

6. 努力学,努力玩,并要挤时间洗衣服

科学不是朝九晚五的工作。在Wood Hole时,我工作异常努力。1984年的整个冬季,我几乎都在工作。特别的时刻需要特别的努力,我很高兴,在关键时刻我花了尽可能多的时间在实验室,见证了科学奇迹的发生。但是,在接下来的春天,我需要离开一段时间来调整状态,所以我骑车游行了欧洲。在到UCSF工作前,我又花了四个月时间在尼泊尔和日本游玩。在关键时刻对项目进行特别努力十分重要,就如打仗时攻克关键要塞一样。但与此同时,你也需要平衡你的生活。

7.持之以恒比才华更重要

如果你并非天生聪颖(比如我),在科学实验中,你也可以做的很好,当然,前提是你得有恒心。诀窍就是更努力!举例来说,1984年那一年的大部分夏天,因为一系列的实验错误,我无法完成体外轴突运输。夏天快要过完了,我也将马上离开开始我的医学实习生涯。在这个关键点上,我没有成功,或许在这时,我应该去海边放松一下。但我并没有选择这条路。

在我回到斯坦福之前,我近乎执拗的对这个实验试了又试。在度过了神奇的一周后,一个神奇的晚上来临了。于是。我取消了我的回程航班。

8. 失败乃成功之母

正如1983至1985年间的那段成功一样,所有的科学完美或许并不如它所表现出来的那样。我们曾犯过几次概念性的错误,也犯过技术性错误。幸运的是,这些错误并不致命,他们并没有让我们偏离正确的轨道太远以致脱轨。这或许对那些课题不是一直顺利向前行进的同学有所安慰;困惑和疑惑的时光对任何项目都是不可或缺的。同时,你也可能或错失很多良机。那时,我们指出「溶液中的微管之间也相互作用从而形成简约聚合的微管」这个论点,但是我们并没有一直对此研究下去。通过马达蛋白驱动的微管自组织随后就成为研究的重要领域。在美国国立研究院对我的第一次资助中,我也想过「存储」行轴突运输的净化(更像名为HMW的ATP酶),最后证明这并不是一个明智的决定。任何一个职业都是不良的决策与好的决策混合出现;你只要保持后者多余前者即可。

9. 莫对改变人生计划感到惶恐

我二十岁和三十多岁早期时的人生是被规划好的。MD-PhD项目后,最大可能是去医院实习,然后跟大部分人一样做一名住院医师,然后再回到科学领域。然而,Woods Hole的出现改变了我的人生规划。回到医学院?从我现在的观点来看,答案当然是否定的。但是那时,其他人会怎么说呢?我的导师鼓励我继续坚持自己的课题并延迟医学实习;很显然,我的心思一直在科学上,科学生涯将使我感到快乐。许多年后,单核马达对医学产生了影响使我感到极其满意,同时,针对这种蛋白的药物也正在研发中也是我倍感欣慰。

10. 科学在极速发展:做时代的弄潮儿

作为研究发现的亲历者是非常棒的感觉。但更大的乐趣是,你正在科学的大舞台上,亲眼目睹着科学作为一个整体所取得的惊人进步。科学家是非常幸运的,因为我们能站在世界的前沿,是巨大进步的见证者。科学冒险有许多形式,在实验室的任何一天都有可能「拥抱」微小却美妙的发现。在未来的某一天,某个巨大的惊喜最终到来。永远相信美好的事情即将发生。

下面是英文全文

How lucky can one be? A perspective from a young scientist at the right place at the right time

How amazing to receive a call that I, along with my friends and colleagues James Spudich and Michael Sheetz, won the Lasker Award for Basic Medical Research. An important part of the research cited for the Lasker Award stems from a time when I was a graduate student. I was 21 years old when I first met Jim Spudich while applying to MD-PhD programs, 23 when Mike Sheetz, Tom Reese, Bruce Schnapp and I began work on axonal transport, 25 when our papers on microtubule-based transport and kinesin were published and 27 when I started my first job at UCSF. It was an extraordinary period of time. I was at the right place at the right time, hanging on tight, and enjoying the scientific ride of my life. This essay is aimed at young scientists who are starting their own journeys. I will provide a perspective and ten lessons learned from my own experiences in graduate school and travels to the discovery of kinesin.

An abbreviated history of my journey to Woods Hole and kinesin

In 1980, I interviewed with Jim Spudich for the MD-PhD program at Stanford University. We had a great discussion, and his recommendation was crucial for my admission. Who would have thought at that time that we would enjoy sharing the Lasker Award together? With my thesis advisor Eric Shooter, an eminent biochemist and neuroscientist, I began studying the ligand binding and biochemical properties of the nerve growth factor (NGF) receptor. I was also intrigued by the problem of how a signal initiated by NGF binding to its receptor at the nerve terminal might travel back to the nucleus, a question that brought me in touch with the literature of axonal transport. In 1982, I learned about the beautiful experiments that Jim and Mike Sheetz were doing on reconstituting the motion of myosin-coated beads along actin cables1. I wondered, might a similar actomyosin mechanism account for axonal transport of membrane vesicles? Mike and I decided to test this idea using the squid giant axon. The attraction of the squid was a consequence of a landmark paper by Robert Allen, Scott Brady, Ray Lasek and their co-workers where they used Allen's recently developed video-enhanced microscopy technique to image axonal transport in the giant axon23. Never before had the fine details of the interior of a living cell been visualized so clearly. Axonal transport could now be studied in a ten-minute experiment under a microscope rather than in a laborious week-long experiment with radioactivity, the traditional measurement at the time.

A meteorological disturbance then changed the course of the project and my life. We arranged to get squid from the Hopkins Marine Station, a satellite of Stanford in Monterey, California. But no squid were caught that year. It was 1983, the year that an El Niño warmed the ocean waters and chased the squid away from the Monterey coast4. What to do? If the squid would not come to us, we had to go to the squid. Mike and I decided at the last minute to go to the Marine Biology Laboratory (MBL) in Woods Hole. Within three weeks, airplane tickets were bought, an MBL lab was rented, an old, rusty Volkswagen Beetle was purchased, the essential supplies from Mike's University of Connecticut lab were packed in the car, and off we went on a scientific camping trip to Woods Hole. Mike and I teamed up with Bruce Schnapp and Tom Reese from the US National Institutes of Health (NIH), outstanding microscopists who had a year-round laboratory at the MBL. It was a perfect team (Fig. 1), as we all brought different skills and thinking and enjoyed the camaraderie of working together on the problem.

牛人就是牛人!一年4篇Cell!拉斯克奖得主Ronald分享科研经验

Figure 1: Mike Sheetz, Tom Reese, Bruce Schnapp and Ron Vale (left to right) at the Marine Biological Laboratories in Woods Hole circa 1984.

The goal of the project was focused on identifying the machinery powering axonal transport. Bruce and Tom performed a tour de force experiment combining light and electron microscopy to show that single microtubules served as tracks for long-distance axonal transport56. Our initial ideas of axonal transport being primarily driven by actomyosin were not right. Next, we sought to reconstitute transport from isolated components, a strategy that worked well for many biological processes including DNA replication, transcription, vesicle transport, ubiquitination and others. In the summer of 1984, reconstitution of vesicle transport worked, but unexpected results led to even simpler and more powerful assays. Molecular motors, without membrane vesicles, could be attached to glass cover slips and could translocate microtubules across the surface; motors also could be attached to beads and propel them along stationary microtubules7. I asked Stanford whether I could postpone my medical clerkships, which were coming up in a few weeks. That winter, the biochemical hunt for the molecular motor was on; with these powerful assays in hand, the dominant motor was not hard to find. It was a previously uncharacterized protein, which we called kinesin8. That same winter we also found evidence for another motor that moved in the opposite direction to kinesin9, which was later found by Richard Vallee's group to be a cytoplasmic dynein10. The work was published in five papers in 1985, and I was lucky enough to get a job offer at UCSF in 1986. I am still on leave of absence from completing my MD degree.

Ten lessons

Here is my top-ten list of what I learned from this experience, most which only became obvious in retrospect. I was immersed in the science, making and sometimes learning from mistakes and having very little idea of where it would all lead and how or where I would emerge at the end.

1. Find good mentors, learn from them and then develop your own style.

Soak up your surroundings. Science is as much about philosophies of approaching problems, personal styles of research and working with others as the process of experimentation itself. As a young scientist, you need to be exposed to different ways of doing science, absorbing the ideas and attitudes of more senior scientists. The net result is a maturation of a hybrid style that best suits you and is a composite of the characteristics that you admire in different individuals. Neither idolize nor ignore anyone. I was fortunate to have many great mentors, which included the core group of Bruce Schnapp, Tom Reese, Mike Sheetz and Jim Spudich. I gained tremendously from their unique personalities and scientific approaches. But they all shared one thing in common—they were incredibly kind and supportive of me as a young scientist. I had additional heroes in graduate school. First was my wonderful advisor, Eric Shooter. How many thesis advisors would let their graduate student wander off quite a distance to work on a project unrelated to his or her own lab's work and without any thought of gaining credit for something that might emerge? I did not completely appreciate at the time how different Eric's unselfish attitude about his lab 'family' is from that of many scientists. I also met lively older scientists at the MBL—Shinya Inoue and Andrew Szent-Gyorgyi who 'adopted' this kid from the West Coast during the Woods Hole winter. They had small and focused labs (unlike the generally larger labs at Stanford) and merged a love of life and a love of science without compromising either.

2. Pick an important problem.

Everyone would rather solve a fascinating problem than a boring one. However, it is not easy to identify a project that is both important and ripe for solving. Furthermore, pragmatics dictate getting results in a defined time period in order to obtain a degree, job or grant. As a result, most of us are not always working on grand issues in biology all of the time. However, you should be vigilant and thoughtful, looking for a wedge or an opening to tackle an important problem, even if it is not in your area of research or expertise. If the opportunity comes along (see next point), seize it. In most cases, you cannot make an important discovery if you are not asking an important question from the start.

3. Get ahead but then take a chance: seek adventure.

In my first two to three years in Eric Shooter's lab, I published a couple of papers that were solid but not outstanding, but I knew that they were sufficient to get a PhD. With that safety net, I had the freedom to look for and take on an important but risky project. That opportunity came along with the chance to build upon the Sheetz/Spudich experiment. The whole axonal transport project was an adventure, beginning with a relatively last-minute decision to go to Woods Hole. Thinking of science as a grand adventure makes it fun and allows unexpected things to happen, in terms of both scientific outcomes and your personal career.

4. Read the literature but don't be crippled by it.

It can be daunting to enter a new field because of its considerable history and literature. You have to be knowledgeable about prior work, but it is also good to avoid getting caught in the trap of doing variations of prior experiments and thinking along the lines of existing models. Fresh eyes and some naïveté can be a good thing. Fast axonal transport at the time had a long literature but relatively little clarity on the mechanism. The Allen, Brady and Lasek video microscopy studies, however, were a turning point because they provided a new way to image small moving vesicles23. Going forward, it made sense to build upon that method by doing biochemistry and not sticking to pharmacology, which had dominated work in the past.

5. You don't need a fancy lab to do good science.

I came from a pristine, well-organized laboratory in a relatively new building at Stanford. Tom Reese's lab at the Marine Biology Laboratory, in contrast, was a chaotic rabbit warren of small rooms in the basement of the Loeb building, with a monolayer of chemical reagents and small equipment covering most of the available bench space. We dissected squid giant axons in a wet and dank seawater room in the basement, which we called 'Neptune's cave'. But none of this mattered, and it was a refreshing change from the well-organized rows of monotonous lab benches that populate most modern research buildings. Tom's lab had state-of-the-art equipment that proved essential for the work—video light and electron microscopy. But at the start of the kinesin purification, there was no centrifuge in the building (we had to go to a building across the street) and no chromatography equipment (we initially used syringes with glass wool). One can adapt to any surroundings and make things work. This also adds to the scientific adventure.

6. Work hard, play hard and squeeze in time to do your laundry.

Science is not a 9-to-5 job. I worked very hard on the projects at Woods Hole; during the winter of 1984, I pretty much only worked (there was not a lot to do during the winter at Woods Hole, so I was not missing much). Special times require special effort, and I was incredibly happy spending as much time as I could in the lab and seeing the science come together. But later in the following spring, I needed time off and went on a long bike trip in Europe. I also spent four months in Nepal and Japan before starting my job at UCSF. It is crucial to push a project hard at some points, but you also must make time to balance your life.

7. Persistence is more important than brilliance.

If you are not naturally brilliant (my case), you can still do well in experimental science if you are persistent. The converse is harder. As an example, for much of the summer of 1984, I failed to reconstitute axonal transport in vitro, mostly owing to a series of experimental mistakes. The summer was drawing to a close and I was soon off to start my medical clerkships. With no success up until that point, it might have been a juncture at which to relax and spend time at the beach. Perhaps the only point to my credit in the kinesin story is that I did not take this path. I was dogmatic about giving this experiment my best shot before returning to Stanford. Then, one magical night followed by one magical week, everything came together. I cancelled my return flight.

8. No project or career is immune from mistakes.

As successful as the 1983–1985 period was, it was not as scientifically perfect as it may appear. We took some conceptual wrong turns and made technical mistakes. We were fortunate that they did not derail us too far off the track. Perhaps this will be comforting to students whose projects may not be going forward in a straight line; moments of confusion and doubt are typical for any project. There were also plenty of missed opportunities. We noted that 「microtubules in solution also moved relative to one another to form a contracted aggregate of microtubule」8 (in modern terms, an 'aster') but did not pursue it. Self-organization of microtubules by motor proteins later became an important area of research. I also thought to 'save' the purification of the retrograde axonal motor (most likely the ATPase called HMW1)89 for an aim in my first NIH grant, which turned out not to be a sensible decision, as I was scooped before I had the chance to do it. Every career is marked by poor and by good decisions; you just have to try to keep the scorecard favoring the latter category.

9. Don't be afraid to change your life plans.

My twenties and early thirties could have been on autopilot—an MD-PhD program most likely followed by an internship and residency and a later return to science. However, the in vitro motility assays from Woods Hole threw a wrench into that plan. Return to medical school? Certainly not now from my point of view, but what would others say? My mentors encouraged me to stick with the project and defer my clerkships; Stanford Medical School was incredibly supportive, as well. I never returned to medicine; it became abundantly apparent that my heart was in science and that a scientific career would keep me happy. Many years later, it is gratifying to me that molecular motors are having an impact on medicine and that drugs are being developed that target these proteins.

10. Science is moving fast: hold on and enjoy the ride.

It is nice to make your own discovery. But there is also great pleasure in having a seat in the big scientific arena and watching the amazing progress that is taking place overall. As an illustration, I was captivated by watching kinesin move vesicles or plastic beads, but it seemed hard to imagine in 1984 how one would be able to understand the detailed inner workings of a motor so small. At that time, I could not envision the many new tools that would come along (single-molecule techniques, better structural methods, genomic studies of a multitude of kinesins) and the ideas contributed by the many people who would enter the field. In the subsequent two decades, we know of many kinesins and the many roles they play and have reasonable ideas of how they produce motion. This incredible progress is being played out in all areas of the life sciences, and we scientists are fortunate to have a front-row seat and witness the tremendous advances that are taking place.

Perspective

I began this essay by saying how lucky I was—lucky to be a young person in the right place at the right time. Now that a few decades have gone by, I have come to appreciate that my job as a senior scientist is to offer students the taste of independence and discovery that I had when I was young. And for the young scientists reading this essay, you don't need to discover kinesin to be excited about science. Discoveries come in all flavors and sizes. Scientific adventures come in many forms. Embrace the wonderful small discoveries and adventures that can happen any day in the lab, and then a big one may eventually come along.

原文地址:http://www.nature.com/nm/journal/v18/n10/full/nm.2925.html
本文部分内容源于http://www.bio360.net/news/show/8362.html

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    • avatar 我是来感悟的 9

      赞~

      • avatar 我是来惊讶的 9

        我太阳的,变态啊!学习!