Venki Ramakrishnan, Thomas A. Steitz and Ada E. Yonath, Nobel Prize in Chemistry 2009: Interview

ade yonat thank you ramakrishna thomas steins welcome to stockholm u3 are united by your studies of the ribosome and so this is the molecular machine which lies at the end of what crick called the central dogma of molecular biology dna makes rna makes protein and the ribosome is what translates rna's code into protein and deciphering its structure and workings is a lifetime's work so i wanted to start just by asking each of you what it is that appeals about taking on a task which is so enormous that it it it you really do have to spend a lifetime sorting this puzzle out so if i could start with you well i started about 30 years ago to get the structural basis of quick central dogma dna makes rna mix protein as you just said and we started with dna polymerases and then looked at rna polymerases and some of the proteins that are involved in for example putting amino acids on trnas and then finally in the mid-90s we got to the point where the ribosome was the the really important target and arione had already shown that in fact crystals could be grown and she had some crystals that diffracted pretty well so it seemed like that was the next mountain we wanted to climb and indeed it was a very exciting adventure it's it's an adventure which is but it is sort of absorbing all of one's time and passion does it not sometimes seem like an adventure that's too large to undertake it didn't seem too large although it wasn't uh so clear how long when we were going to get there it was clearly a challenge but um and indeed in fact it was took less time than many of the problems in the lab not that we expected that to be the case so i got into ribosomes almost by accident i was switching from physics to biology and i had written to a number of universities asking whether i could join the graduate program to do a second phd in biology and at the time tom won't remember this but two people from yale wrote to me the chairman of yale wrote to me and said we won't take you as a graduate student but i've circulated your letter to faculty members and some of them may want to take you on as a postdoc and two people wrote to me don engelmann and tom here asking if i would be interested in doing a postdoc and i wasn't ready for it because i felt i needed a broader background in biology so i went to the university of california in san diego to study biology and then after a couple of years i realized i didn't actually need a second phd and i then wrote to don again and at the time don engelman was collaborating with peter moore on the effort to locate all the individual proteins in the small ribosomal subunit and so peter moore met me at some meeting and then kindly accepted me in his lab and so that's how i got into ribosomes and that was in 1978. and then i you know when i had my own lab we started working on pieces of the ribosome and then in about the mid 90s i had some ideas of both how to try to get better crystals of the small ribosomal subunit for which there weren't very good crystals at the time as well as perhaps what to do if i actually got crystals and so with these sort of ideas in mind we started tackling this problem of the whole ribosomal subunit which i thought of as a sort of stepping stone towards looking at the entire but again this this idea of having to take stepping stones to get to the eventual goal it does from the outside look it's almost impossibly daunting that one begins so small not if you look at it one step at a time i think um you know we were looking at individual ribosomal proteins then we did a protein rna complex in the ribosome then we did some an initiation factor so so it's sort of each time i think the complexity uh increased a little bit but then i think i agree it was a big jump to uh try to sort of work on the uh whole rhyme solomon subunit which of course people like ida had been doing for quite some time by then so so you you sort of began the the herculean task by attempting to get a crystal of the ribosome from which you could derive a structure when people really were saying this couldn't be done what turned you to the subject in the first place so it started with i think that people began before me there were some that tried to produce crystals of the ribosome in order to determine the structure so i knew about some attempts some even serious attempts around the world but what my my way in getting into it was very similar to what tom told anything that has to shed some light on protein biosynthesis was of interest for me because the process attract my curiosity so so strongly that i was ready to do almost everything so i started with the initiation factors and when i needed some more material i don't want to go into all the detail i got into the idea that maybe ribosomes can be crystallized by reading not direct directly related to the journals i see from your lecture title that that story is going to come up in your novel actually i think so but in the beginning i thought as i said earlier in any any progress in this very complicated and very challenging process would be of interest the translation of the genetic code and i thought that even if i step just one little step forward with not so good crystals with better crystals with this type of crystal so this object can be only viewed by electron microscopy whatever can be done that will will uh increase our knowledge in our understanding of it would be for me a satisfactory almost completely but not fully so curiosity is what drove me and we had to to to go through obstacle after obstacle which took about 15 years until we showed the feasibility as tom showed said earlier and and also banking and eventually we got there but i think yours my driving force was curiosity the wish to understand this process and i didn't think about this is too big too large or whatever i was ready to to go more or less step by step did other people around you believe in you do you think they believed there was a very few but the few that believed were very good and quite supportive very few the person i collaborated with was the director of the max planck in berlin that they heinz dental whitman who prepared the materials and prepared the ribosomes and had the the manpower to produce what i needed to to try so john kendra who was the head of amble at that time and embell was made it possible for me to go to synchrotrons and try to measure although the synchrotron radiation people not always wanted me there they said oh you don't have any result you go but he said a project like this shouldn't be stopped luckily he was also on the scientific advisory committee of the weizmann institute when where i worked and once he said this sentence the wise men supported me for a long time going on erwin klogg from mlc whom i visited by accident because i came to see somebody else and asked me what i'm doing there and looked at my initial results fought and fought and fought and said you know leave it here maybe we can help you so i knew that i have something that some and this was back in the beginning of the 80s and ken holmes who said even if there are no ways to to continue after crystals they will be found just go on and then they on the way there was a lot of upside up and downs and ups and downs but they did you welcome the um advent of other people in the field because as as success began to come more people joined the field was that something that you saw as a positive thing or was it worrying that suddenly an area that you'd have to yourself okay so i have two answers first first a general answer i think that for science it's best that more and more people are interested interested in basic problems because they have different views they may have different techniques they may look at things in different with different attitudes so at the end this is very good for me it was wonderful the first time i held it tom has crystals this was the first time in my life ribosome life that people don't told me don't didn't tell me oh you're dreaming or you don't really have what you have or whatever all the all the attitude i had earlier so this was and tom told me it was easy to repeat so it was good i think it's true that all uh science all scientists stand on the shoulders of those who went before and so we and it doesn't have to be very far before and that is we help each other i mean obviously we benefited from otter's early work i think we did some things that might have might or might not have helped some of the others in in their approaches or at least seen that it can be done so i think this is a very helpful thing you don't want to do science in a closet it's a very uh first of all it's not any fun uh and and second of all it's not as as as productive and as exciting i also want to say that in the mid 90s when both tom and i entered the field it was still far from clear that those there was a solution in sight okay and in fact both of us had to do sort of had our own approaches of how to get the job done and in fact we've you know used some of tom's ideas for getting low resolution phases so i think um it isn't quite right to sort of say well you know all of the groundwork was laid and then the uh you know others sort of joined in i think it was far from a foregone conclusion and uh so much so that i actually had i i felt that i i needed to leave my professorship in the u.s to seek the rather stable funding environment of the lmb in cambridge because i had no idea whether it would take five years or ten years or or longer so so if i can still hate because i didn't i didn't finish that your earlier question there were two more people that did believe and did help and i would like to to mention them it's hack on hope from davis who was with whom we found a way to eliminate or at least minimize crystal damage at the x-rays a method that became routine right away afterwards cryo-cryobio-crystallography and he came he came in a very critical mement when i thought 76 77 when i saw 86 87 when i thought that the whole thing is gone and michael pope from georgetown who provided us with the clusters with the polytungsten clusters that were used for phasing by us by tom and by uh venky at least at low resolution in our case even at high resolution so i think one once i saw i talked about those people i would like to mention them and michael seller who was the president of the weizmann institute and made clear that i can continue i might return to the topic of competition again in a little while but the but you mentioned you mentioned the the lnb and um so you still work at the mrc laboratory molecular biology in cambridge and you were a postdoc i think that and i did a sabbatical there as well okay for half a year so it's one of those famous places that people talk about and has generated for instance a large number of nobel laureates um what would you say was its defining characteristic that makes it successful i think there are several of those one is that it has core funding from the medical research council and the mrc has always understood that the lmb would be tackling hard fundamental problems and not ones where you have a quick payoff and lots of papers and so on so that's one thing the other other thing is that all facilities at the lmb are shared and so there's a great spirit of collegiality there anyone from a senior scientist to an incoming phd student has exactly the same rights to use x-ray equipment or any central facility so that kind of interactive environment also fosters exchange of ideas and so on and then it has a tradition of being self-critical people are always asking each other you know why are you doing this and that's a very powerful question you know if the answer is oh because i want to get my next paper published you know it looks a bit lame and you have to really think about you know why is this thing that i'm struggling with important and what you know even if i succeeded would it actually tell me anything so i think that's an attitude uh that it tries to cultivate so there are several aspects there's a sort of self-policing going on that everybody else everybody's asking not policing it's the wrong word but everybody's asking each other what is your bold question yeah no there's a there's a real culture of of uh not spending your time on what might be called sort of mundane or or trivial problems i think that's that's true and uh i think that's also made possible by the way the lmb is funded and by the sort of organization of the army so the three aspects actually are all interlinked i felt i found as a postdoc it was the most impressive environment because of the way people interacted with each other i always had lunch uh coffee in the morning lunch at noon uh or actually one o'clock uh and then tea uh in the afternoon there's so much so that i always wonder well how does anybody get anything done but it's exactly what vinky just said people would only talk about science not what they saw on tv last night or the movie they saw and they would always bring up this what they were doing and why they were doing it and you might happen to be sitting next to francis crick and he might say well i wonder why you're doing that or had you thought of the following way of solving this problem and there was a and within just a few months we knew everybody in the whole laboratory it's a fabulous environment for learning and for doing creative thinking and i think that i all these other points like the funding and that very important but to me as a postdoc the most exciting thing was the culture of how you do science and how you think about science and how you interact with other scientists do the senior society still go to tea at the lmb oh yeah no that's a very important part of the culture and i remember i went there on sabbatical in 1991 and i arrived the first day and john finch who works closely with aaron klug was my official host and i came into the lab at 8 30 and about 10 o'clock and he came and said um would you like to go for coffee and i thought no i've only been here you know an hour and a half and you know so i said well not really and someone looked at me and and looked at john and said he's he hasn't learned our ways yet and uh you know then i realized that actually this you know the these periodic interruptions in your day they're actually you don't you tend to get less tired as well because you know you're doing something and the mind i think can only focus for a couple of hours at a time uh before some sort of mental fatigue sets and so it's a natural way of breaking it up and then you talk to other people and it's it's certainly a very important point [Music] we shouldn't really leave out the vitamin i suppose when we're talking about this the vitamin is a very successful institute as well do they do they try and foster similar cultures there um i think the right development is larger than lmb so this type of interaction everybody sees everybody all the time or almost all the time or three times a day is just impossible there are hundreds of people working there but the weizmann does try to single out people and projects that have very high importance very significant and let them work even if success is not shown just across the border not always the funding is not so simple although there are some some ways to make it better like a creating centers i was very lucky to have a center like this of a structural biology fostered by helen kimmel from new york but they they do try no matter how the funding comes to let people uh go above and beyond the the what is called average or trivial or sure or no risk they do try to to let things like this happening if they have a feeling that it's important and there is a chance that it will also mature some chance i should point out also that i've been supported for the last uh 25 years or so by howard hughes medical institute and it's in some ways it's like the lmb in that it's a more stable funding organization um than the nih which every five years you have to renew and i think they've been very helpful and there was a structural biology consortium at yale of many about a half dozen or so investigators and we we tried to emulate the lmb environment and having lunch and interacting so i think they're money money and culture i mean people constantly talk about the fact that the availability of long-term money with few strings attached is becoming scarcer scarcer and a project such as this which has obviously taken such an investment in basic research where one doesn't really know when one's going to get to the end is a great example of why it's needed do you fear for the future of this sort of bold approach outside of places like the lmd well i think even in britain there are movements to um you know constantly sort of evaluate uh work based on its impact etc and so there is a there is a danger but i think i think good uh science administrators understand the value of basic science i mean that's true uh in the u.s and it's true in england as well i i don't know about israel but but there is a danger that because a lot of science gets funded by taxpayer money that you know the taxpayer needs to know you know why why should a truck driver's taxes go to support you know particular kind of research i think scientists need to be able to explain and make the case for basic research it's not a very difficult case to make because you know so many great inventions and discoveries that have benefited humanity have come out of basic research and if you actually put a value on the investment and the return you'll find that basic research is actually very good value for money and so the good administrators are aware of it the problem is sometimes you get people with more short-term visions controlling things and then that it's not so bad so if i may aid please part of a large part of my work on the ribosome was also i made in parallel to the weissman by the max planck a society in germany that even set up a unit for me near the singleton in hamburg in daisy the in the past max planck was like a paradise from point of view of funding there was hardly any any problem once there was a decision this is a project or this is even more like this a person that can run a a department called of thailand recently even there i think as far as i felt and as far as i know i think that it's it's becoming more and more like what venki just described taxpayers want to know there is constant evaluation some people understand the importance of basic science and some don't know do not and even even in places like this like central europe and where it was known that money is given almost with no strings it's not so anymore so i benefited from it for some time but they i also saw how it changes so the the structures all came together in a rather sort of marvelous way in in 2000 and suddenly there was a high resolution structure available of the large subunit of the small subunit and indeed of the whole ribosome and that's been constantly improving since um at that stage just getting back to the competition idea at that stage when things were really coming together was it was that an anxious time to see whether who whether one could get into press first with one's findings oh i i have to say i think it was a very anxious time and we were all very tense and there was a period i particularly remember because we got to five and a half angstroms without any problems and that was published in 99 but to go from five and a half to three angstroms which is what we needed to get the high resolution structure for us was rather difficult because we ran into a number of technical problems which had to do with the behavior of the crystals and i would keep getting reports you know that the yale group was steadily sort of advancing and uh you know and that so it was quite a depressing time uh actually around december of uh 99 and uh luckily in the end you know we were able to sort of uh pull it off but i i i think to be perfectly honest it was a very very tense time and we thought venky would be much faster because it's such a small subunit that he [Music] i once joked to tom it isn't fair that you guys you know got in a bit ahead of us because it would be like hemoglobin being solved before myoglobin well but you see what what what held us up is we had more atoms to fit in because we had a high resolution map in in december i think it was about december early january of 2000 december of 99 or january 2000 but there were 100 000 atoms that had to be fitted into the map and this this takes a while you probably only have 50 000 to fit in so that's about right half half as long so yeah but crystals which were much worse but but i you know i i guess i don't worry i should worry about these things more but i don't um and so we were just worried about just getting there and and uh i knew there were other folks out there but we thought we could do all right we just pressed on there was also another element which is you know i deliberately chose the 30s because the at the time i started there were good crystals of the 50s but there weren't any good crystals of the 30s and so i thought when tom started working on the 50s that he and ara would be competing and i would be quietly having a good time with the 30s and then i found out you know barely a year after i started that ara had her own good crystals of the 30s and so instead of tom and ada sort of duking it out it was you know a head-to-head race between uh me and anna which uh was not the position i wanted to be in so so if i may i add something first of all it's very good question because the first time i heard that frankie was under pressure i thought that frankie is was quiet and went step by step he was so quiet that we didn't even know that he works on it for i think two years more or less and we had we had the two subunits at that time like the one the same one that frankie had but we got it differently and a different one that tom had but a few bacteria so we had to go both ways and somehow i felt that in my group the the feeling of race was not the most important thing it was not so important to be a week earlier a week later as it was important to see the structure i felt so maybe i'm too easy on my people but this this we were also geographically a bit further away but it's very good that you asked him but i think i think all scientists are fundamentally uh curious and are driven primarily by you know wanting to see the result but but we're also human and we'd like to see it before and you don't want to see it in the next one is nature exactly well you're still interpreting your map yeah so i think i think it's i think it's honest to say that most scientists like to see the result but they'd rather see it first you know before maybe it's like for most so if if one tries to describe how the ribosome works with our current picture of it if you sort of i don't know whether one wants to use one's hands or whatever but how would you describe this molecular machine as you see it when you when you picture it working um i mean broadly the large subunit is building proteins and the small subunit is checking their integrity i gather no it's it actually it has to check the whether the right amino acid has been brought in before the amino acid gets added on because otherwise it's too late so we call the small subunit the clever one because it has to it has to find the right piece of of the messenger rna to be translated and bind to it or bind it to whatever you want to call it and then it has to select for the right amino acids that's what bank is did now and say it now and also prove it in the beginning before the larger building all what it does is they put them together it's not as clever as the fourth small one but then we found out that also putting together is not as simple not as simple as it is to say it but at what what sort of speed is this molecular machine working and how i mean how do how does should one think of it as a machine or oh definitely yeah it's a machine it uses energy and it moves so it has all the properties it treats instructions it gets instructions it comes out with a product so it's a machine it's like translating these these punch tapes that use that nobody knows that anymore but we used to have paper tapes that we would use for running our x-ray machines and and you would punch the tape and then you could read that out to get the intensities well that's what the ribosome was doing it's reading out this this paper tape the messenger rna to say which trna containing which amino acid should be delivered and that's what the small subunit is doing is making sure the the right trna is delivered to the right message and then the large subunit once the amino acid has been delivered is attaching it to the growing peptide and that's that's the function of the large subunit it does more than this after after it it touches it also protects it because this this little protein starts from little little until it goes up it protects it so it the first one is selecting the second one is protecting that's the sort of pouch it has a tunnel to do that so one thing is that you asked you know how fast is it and um it it synthesizes 20 to 30 uh residues per second with an error rate of less than one in ten thousand now one reason to mention it is every time you know the nobel committee gives a chemistry award to something that's in molecular biology let's say there's always a human cry from hardcore chemists saying you know well these people aren't real chemists you know and they've gotten our prize again and the fact is there is no peptide synthesizer today that can come even close to making 20 to 30 residues per second with that kind of accuracy and so well i may not personally be a chemist but the ribosome does some amazing chemistry to get it done and you're trying to understand the chemistry and that's and our view is in order to understand the chemistry that the ribosome is doing one must as one piece of information have the structural us of every state in the process and that's that's what we're doing so so venky studied physics in biology i studied chemistry so and i was a good student i was consider this one that can do synthesis i can't do 15 or even 20 even or 10 in a minute a second i can't do it in a week so so no question the ribosome is a good chemist as well it can do this but the the do we do we on this question of whether this is a chemistry prize or another price do we understand the ribosome at a chemical level do we do we understand the way it does this chemistry much more so after these structures certainly well i think it works no i i think the mechanism uh by which the ribosome is a ribozyme is now understood it was it was proposed by francis crick in 1968 that the ribosome was probably going to be must have been a ribozyme because how could you have a protein synthesize the first protein before you can't have a protein machine synthesized protein the chicken in the egg problem so it had to be an rna uh and and so what the structure showed both for the small subunit and for the large subunit is indeed it is arrivedesign that is the critical functions are executed by rna but then the chemical question is how can rna be a catalyst it's actually not most chemist's choice for a general assert general base to use bases and sugars to do this and so how does that happen and i think the combination of the structural studies that we've done plus some mutational and kinetic studies that others have done have now led to an understanding what is the mechanism whereby the ribosome catalyzes peptide bond formation lowering activation barriers chemists language increasing rate of catalysis uh lowering the entropy of substrate orientation all chemistry phases so i think i think we're doing chemistry myself so these are this is actually almost fully clear what tom just said now but how the whole thing goes on and how it starts and how it finishes and how how the cell and the ribosome interacts this is still not fully understood and there are questions to ask and i think the structures directed new type of questions that hopefully will answer all what i meant and probably much more than that so one consequence of the structures was that um it gave an insight into how one might design new antibiotics that antibiotics i gather about 50 of antibiotics target ribosomes so having a structure of the ribosome should allow you to design new antibiotics and you indeed have started a company ribex which tries to do exactly that is it the case that we now have new antibiotics in clinical testing which have come directly from a knowledge of the structure yes yes yes so in 2001 peter moore and myself bill jorgensen started the company ribex because we realized that the structures of the antibiotic complex with a large ribosomal subunit could be a useful start for designing new antibiotics and they've been working on it now over the subsequent years and um they have one compound that has successfully completed phase two clinical trials that's effective against all methicillin resistant staph aureus and they have several others in the pipeline and their whole strategy is to take a portion of one compound that's bound and tie it to a portion of another compound that's bound nearby so it turns out that the ribosome has many different families of antibiotics that bind nearby in the peptidyl transferase region center region and so by taking different components and making a hybrid molecule you can now make compounds that are very effective against resistance strains and so i'm extraordinarily optimistic that it's not only going to lead to one compound it's going to lead to many compounds in fact they are now using the ribosome structure to design de novo compounds that are now showing activity against gram-negative bacteria like e coli and there are very very few compounds out there that active against gram-negative bacteria that's a major problem and they have several families that they are now developing that are lined up to go into phase one clinical trials so i really think this is going to be another machine generating not just one antibiotic but many and many people ask me they say well is it possible to design an antibiotic that will now always be useful and won't generate any resistance and i always say that evolution trumps intelligent design so however intelligently you design your antibiotic evolution will catch up and so what you have to do is continue to evolve your design and i think now this is a machine that allows the evolution of the design and it's a desperate need as well isn't it a desperate need and in fact we we've just now we haven't published it yet but we've we've made a complex between the 70s ribosome and capriomycin and viomycin and these are capri mice is one of the major antibiotics that targets tuberculosis and there's some strains emerging particularly in south africa that are called xdr and they are these strains are resistant to all of the antibiotics that target tb no matter what their the target molecule is and so the and it's they're very very dangerous and exploding and what we find is that this binding site for capriomycin on the ribosome is right next to two binding sites for antibiotics that venky saw but for um varroa mycin and hygromycin and so i hope i got the names right and and and it looks again like here here's a com here's another opportunity to make a combo for for new antibiotics now the problem with this is of course of the people who get tb these days are very poor and so drug companies are a little reluctant to get into this but i think this could be a problem that will spread worldwide if we're not careful so i'm hoping that this this potential solution to these problems that can be generated by use of the ribosome structure um will um be very helpful i should say one thing about the last comment tom made which is so i should say that i'm a consultant for tom's the company tom founded i'm also on their advisory board but um so i've seen it firsthand how expensive it is to actually get something through to market it's it's tremendously expensive and so it is reasonable for pharmaceutical companies to want a return on their investment but at the same time if large populations in the third world are deprived of these medicines it's a serious problem and i think you know things like the orphan drug program are absolutely essential and perhaps multiple pricing in different markets is another way because you know a western pharmaceutical company is not going to get much money from poor countries in africa or asia anyway and so they as well license it at very low prices there provided of course as stringent controls against you know smuggling but that'll that'll be a problem whether you license it or not and so i think it's this is something that people do need to think about so you know there are new models are needed in order to get drugs yeah so if i'm allowed to to add something from the basic science from the basic research point of view less from the company's point of view there are ways to improve and to understand better antibiotics and consequently on also a resistance for instance we found in the literature recently two compounds that can be synergetic they are not strong and we think now that we can make them strong whereas very very similar one is competing and on this hardly seen differences we are now building or can be can build a strategy of making antibiotics that are powerful and probably less prone to resistance or resistance resistance will happen but probably slower and in not so aggressively if we play on this little difference that can change between synergism and competition and make it most energetic and it's we we found it in natural products that are not in use so there are things like what tom and wenge described making new ones and there are some that are using what the nature gives with improvements need improvements chemical improvement but are possible to be made not that we have a company for it but we have an idea but there are various strands to explore um yes it's nice because it was a basic science story which now has a very very much needed application but i suppose it's worth stating that it all came from basic research without a thought and what's more i i i think it's true with venky it's certainly true in my case i never started working on the ribosome because i thought of its practical consequence in fact i i should have known that the ribosome was a major target of antibiotics but i didn't really it was only after we started that then i realized this when we started working on it and i i must say one of my concerns about what i see with funding agencies increasingly is this desire to have translational research translational research as applied to the ribosome was fine but but i thought but i think translational research in the sense that you want to target your research on doing something practical i think it's the wrong way around i think you want to understand the world and then use that information to solve the problems that it enables it's just in universities and research institutes maybe companies have to think differently but oh yeah that seems like basically basic science was my motivation and i think also bank is in terms understanding the ribosome or understanding translation of the genetic code not translation i think funding translational research as such is okay but what's happening is there's an increasing trend to ask basic research proposals to justify you know themselves on the basis of potential implications and i think it's very very hard to predict uh you know what sort of implication your basic problem will have you know 10 20 years down the line so as yogi berra said nothing's harder to predict in the future and so who knows on that that seems like a good point to stop with although it's quite easy to predict what the next five or six days holds for use i hope you have a very enjoyable week here in stockholm thank you very much

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Published: Fri Jul 29 2022