Lessons from the Discovery of the Ubiquitin System
Hershko, Avram
I shall briefly describe how the ubiquitin system was discovered and then will discuss what general lessons can be learned from this story. One is the importance of having excellent mentors at an early stage of the scientific career, whose influence may greatly affect much of subsequent work. Another is choosing a research subject that is important, but not yet in the mainstream of scientific research. The importance of recognizing accidental observations that lead to novel discoveries and of staying away from “fashionable” technologies (unless absolutely necessary) will also be discussed.
 Thank you very much for your kind introduction. I would like to tell you about, or maybe to tell in a short way, the story of the discovery of the ubiquitin system for protein degradation. I'll do that later to look at it and to find what are the lessons that can be drawn for this story, mainly lessons for the younger people, for the young investigators, for the students in this audience. So I am interested for a long time in the problem of how proteins are degrading cells, as you just heard. And that was a subject that did not interest too many people at that time. Following the great discoveries of the structure of the DNA, the double helix, in the 1950s, and cracking of the genetic code in the 1960s, there was a huge and justified interest in molecular genetics. So it was known that the gene is a stretch of DNA that is the blueprint for the formation of a protein via an intermediary blueprint, the RNA. And then proteins are synthesized for amino acids in the process of protein synthesis, in which the amino acids are assembled in a sequence that is determined by the sequence of the bases in the DNA. So as I said, there was a huge and justified interest in this process of how proteins are synthesized, how the synthesis of proteins is turned on and off. And because of that, there was a very little interest in the opposite process of protein degradation, in which proteins are disassembled back to amino acids. And however, it was already clear at that time, around 1970, that protein degradation carries out important functions. And one important function is to eliminate abnormal proteins. So our proteins are very sensitive structures. They are very easily damaged, for example, by oxygen radicals, by hydro-damages, and then they lose their normal conformations. And the abnormal proteins can get in the way of the action of the normal proteins, and they can actually kill the cells in which they are. So they have to be eliminated. The protein degradation system recognizes these abnormal proteins and eliminates them in a very efficient way. However, it was already clear at that time that protein degradation is not simply just garbage disposal system to remove abnormal proteins, because some normal proteins, completely normal proteins, are also degraded in a selective rate. Usually proteins that have some regulatory functions have rapid turnovers, and they are degraded rapidly, whereas housekeeping proteins are more stable and can stay on for a long time. So protein degradation of normal proteins is a selective process, it happens. And it was clear at that time that the levels, because of that, the levels of specific proteins in animal cells can be regulated not only by changes in rates of synthesis, but also by changes in rates of degradation. That was recognized by Shemke at around the 1970s. So to me it was clear that protein degradation is important process because of these observations, but it was not known how proteins are degraded in such a highly selective and regulated mode. So this was the information when I got to the lab of Gordon Tomkins in the University of California in San Francisco as a young postdoctoral fellow, and Gordon at that time was interested in how a certain protein in liver cells, certain enzyme liver cells is induced by steroid hormones, how hormones can cause the induction, the rapid synthesis of these proteins. So when I got there, I saw that it was a large lab, there were about 25 different postdoctoral fellows, they were all working on different aspects of the induction of the synthesis of these proteins by steroid hormones. I saw that this was a bit too congested and I didn't want to work on what everybody else was working, so I asked Gordon, can I have another subject? And he said, yeah, why don't you work on the degradation of the same enzyme, tyrosine amino transphalase, because it may also regulate the level of the enzyme. So this is how I got on the problem of protein degradation, on which I'm working ever since. And here in this slide you see one of the first experiments that I did in the Tomkins lab, and I found then quite by chance that the degradation of this protein is completely arrested by adding an inhibitor of cellular energy production, such as potassium fluoride. So that is the rapid degradation of this enzyme in the control tube. And when I added potassium fluoride, there was complete stopping of the degradation, which surprised me greatly because I actually saw that maybe it will be degraded even faster when the cells don't have energy. So it was a surprising observation, but I was very much impressed by it, because why would energy be needed for the degradation of a protein? The degradation of exocellular proteins that were known at that time, such as proteins digested in our digestive tract by trypsin, chymotrypsin, did not need any energy. Actually, it released some energy. So why would energy be needed for protein degradation? I thought maybe it is needed for the selectivity. So maybe we have here a completely novel system that uses energy to achieve the high selectivity of intercellular protein degradation. So following my return to Israel, I continued because of that to work on the mechanisms of intercellular protein degradation because of these reasons. So as I said, it was known to be important for the control of levels of cellular proteins. It was an important process, but the pathways were not known. And the energy dependence of protein degradation that I just described now suggested that it may be some kind of a novel previously unknown biochemical mechanism that carried out intercellular protein degradation. And another reason for working on it, important reason was that not many were interested, so I did not have to worry about competition. So I returned to Israel from my postdoctoral fellowship, and then I thought, how should I approach this problem? And I thought the way to approach it, apparently a complex system, and the way to approach it is by the biochemical approach, which is first to make an extract. We have to open the cell to find out what happens inside. So one has to open up the cell, but in a way that facefully reproduces the process in the test tube. So it's very easy to open cells to make extracts, but it's not so easy to make extracts so that they will facefully reproduce the process in the test tube. In my case, I looked for an energy-dependent protein degradation in the test tube, in these extracts. Once one has extracts, one usually fractionates the extract because it has many components, several enzyme components. We have to find out what are the different enzymes. So we fractionate the extract, which has thousands of different enzymes, to find out what are the important enzymes for us, and then purify each enzyme component, characterize the action of mode of action of each purified component. And the last and most important step in the analysis is to reconstitute the activity of the complete system by the addition of all isolated and purified components. So I can try to find out how a watch works, a mechanical watch. We have to open it up carefully, gently. Take out the different components, such as springs and wheels, whatever it is. Look at them and try to figure out how they work. And then to put them back again to the watch, if the watch again works, then we really understood how the watch works. So that's what we tried to do. And our first step in this direction was published in 1978 by BBRC, which is a very small, not very prestigious journal. But I still like this paper because it was the first step in the right direction. And the experiment was made, was done by Aaron Chachanover, who was my graduate student, and then shared the Nobel Prize with me, as you heard, for his part in this story. So what was done is we found that in a lysate from reticulocytes, which are immature red blood cells, we looked at the degradation of a certain protein, globin, and we looked at the degradation with or without ATP. ATP, as you may know, is the source of energy in cells. It is how energy is transduced in cells. So as you can see in the lysate, without ATP, there was very little degradation. But there was much more degradation in the presence of ATP, of energy source. So this told us that we indeed have here the cell-free system that facefully reproduces energy-dependent protein degradation in the test tube. And then he did a fractionation, simple fractionation of reticulocyte lysate to two fractions on a certain ion exchange resin. And fraction one, which is all the proteins that do not bind to the resin, there was no degradation in the absence of presence of ATP. Fraction two, where all the other proteins were, had some activity, some degradation, but most of the ATP-dependent activity was lost. So we thought maybe there is something in fraction one that is missing in fraction two. We combined back fraction one and fraction two, and indeed we could get back the complete activity, ATP-dependent protein degradation. So this very simple experiment told us that the system that degrades a protein's independence of energy is composed of at least two components. Now we know there is much more than two. But then we knew that there are at least two. So we tried to find out what are these two. And I first decided first to, we have to purify, and decided first to purify the active component from fraction one. And that was a good decision because the purification of the active component from fraction one was the key to the understanding of the mode of the action of this system. So we purified this component. It found to be a small protein. Here a protein is separated on a gel. And if you get only one band, then the protein is quite pure. Here we had an increasing amount of the protein, and we could see that the active component was a pure protein. It was a small protein. We called it that time factor one of the system. But later it was found that it is similar to ubiquitin, ubiquitously occurring small protein that previously unknown function. So we tried to find out what is the function of this small protein, ubiquitin. And here we had a great prize. We found that ubiquitin is covalently linked to the substrates which have to be degraded by this system. And here the original experiment is shown in which we took our pure protein, ubiquitin, labeled it by iodine, mixed it with completely crude fraction two, incubated it without or with ATP, and then separated all the products of the reaction on the other gel, on the SDS gel, without, under denaturing conditions. So in this gel, usually small proteins run ahead and they separate by size. So the small proteins run ahead and the larger proteins migrate slower and run below. So following incubation without ATP, ubiquitin remained free and it ran ahead in the gel. But following incubation of ubiquitin with fraction two with ATP, ubiquitin was bound to a huge number of high molecular weight proteins. And then we saw this. We suddenly understood or we had a hypothesis. Until now we did not have a hypothesis. We had a hypothesis that maybe ubiquitin binds to the substrates of the system because fraction two contains not only enzymes but also proteins, substrates that have to be degraded by this system. Maybe it binds covalently and maybe with this binding it targets them for degradation. And to examine this hypothesis, we added the substrate, lysosyme, which was not a natural substrate, but a good substrate, and as you can see there were several higher molecular weight bands that contained both lysosyme and ubiquitin. And we measured the ratios of the radioactivity between lysosyme is labelled or if ubiquitin is labelled. And we found that these bands are increasing numbers of ubiquitin molecules bound to one molecule of the protein of substrates. So based on that we proposed in 1980 that the covalent ligation of ubiquitin to proteins is the targeting, is the labelling or marking which marks these proteins for degradation. And by we, I mean my collaborators, Irwin Rose, whom you mentioned from Fox Chase Cancer Center, and Aaron Chahanowale, who was my graduate student at that time. So here is the original proposal in the upper part of this slide. So we proposed that the ubiquitin or APF1 is linked to the protein that has been degraded and the several molecules of ubiquitin are bound to the protein. And the hypothesis was that following these marking there is some kind of an enzyme that recognises proteins which are bound covalently to ubiquitin, degrades them, and then ubiquitin is being released for another use. So this hypothesis explains the energy dependence of protein degradation because the energy is needed for the marking process. You need energy to make an amide bond. In this case there is an amide bond between ubiquitin and the lysine groups of proteins to which it is linked. And it also explained the selectivity, as I say later on, because the marking is selective and ubiquitin is linked only to those proteins that have to be degraded. And in the following 10 years or so we found that this hypothesis was essentially correct, we found much more detail and the binding of ubiquitin to protein is actually not done by one enzyme but by three enzymes, enzyme one, two, and three, that work one after the other. Enzyme one is the enzyme that activates ubiquitin, so this is the energy dependence step, and then ubiquitin is transferred to another enzyme, so it is transferred to enzyme three or ubiquitin ligase, which ligates ubiquitin to the protein that has to be degraded. So ubiquitin ligases recognize proteins that have to be degraded and transfer ubiquitin to the lysine groups of these proteins. And now we know that there are around 600 different E3 enzymes in the ubiquitin protein ligases in the human genome, and we need this large number of ubiquitin ligases in order to recognize different proteins, because each ubiquitin ligase recognizes a certain motif or certain characteristic in the protein substrate that has to be degraded. Following the ligation of ubiquitin to a protein, usually a ubiquitin chain is made in which each ubiquitin is bound to the previous ubiquitin, and then proteins thus ligated to ubiquitin chains are degraded by a large complex, the proteosome complex that degrades only proteins that have been marked with ubiquitin. And subsequently, ubiquitin is indeed released, free ubiquitin is released, so that it can be used again for degrading another protein. So this is the biochemistry, the basic biochemistry of ubiquitin mediator protein degradation that we found out, and later on I got interested in the roles of this system in cell division cycle, but I won't go into it. And I just mentioned that work by many other groups showed that ubiquitin mediator protein degradation is involved in almost every basic cellular process, such as cell division, signal transduction, embryonic development, and so on. And in all these cases, ubiquitin mediator protein degradation is by degrading regulators. So either a regulator has to be active for a certain amount of time, and then have to be removed, or an inhibitor, a negative regulator is being removed, and then the process can start. And of course, ubiquitin mediator protein degradation also has an important protein quality control to remove abnormal proteins, as I have described. So the ubiquitin system is also involved in diseases such as in cancer, in neurodegenerative diseases in which abnormal proteins accumulate in certain cells of the brain, such as Parkinson's, Alzheimer's disease, certain types of mental retardation, and muscle wasting. And the ubiquitin system is involved in cancer. I skip over there because I want to get to the lessons part. And the ubiquitin system is already being used as a target for new types of drugs, against certain types of cancer, but I didn't have time to tell you about that. But because I want to get to the lessons part, because I think this is important for a young audience such as you. So what did I learn from my life in science thus far? I'm not finished as you heard, but that's why what did I learn? I learned, first of all, I learned how important it is to have good mentors in your beginning, in your first steps in science. So you cannot learn how to do science, good science just from reading the literature. You should read the literature, you should read all the literature, but you learn how to do science by watching a person, a mentor. How does he approach a problem? What does it tell you, what is important to approach a problem? So you need this human touch and you get the human touch from mentors. So I was very fortunate to have very good mentors in my early time in life in science. My first mentor was Jacob Mager, with whom I did my PhD at the Hebrew University in Jerusalem. He was a biochemist of unbelievable knowledge in all various fields of biomedical sciences. He really knew everything. He was also a very, very rigorous experimenterist. Each experiment had to do with all the controls, all the positive controls, all the negative controls. Each experiment had to be repeated in different ways to ensure that your result is indeed correct before going on further and relying on these results. So I learned a lot from Jacob Mager. I had a very good basis of good biochemistry, good strong stringent biochemistry in my early life in science. And then I went on to do my postdoctoral fellowship with Gordon Tomkins at the University of California in San Francisco. And Gordon was very different from Mager. He did not care too much about controls. And because of that he got into trouble several times. But he had a lot of imagination, a lot of inspiration. He was a source of inspiration to many, many people at his times. He was really a genius, I think, in inspiration. So I learned from Gordon how to do, how that inspiration is important. You have to get out of the box to think about ways, about things in a new way. But in science it's very important after you have an idea, after you have a fresh, a new idea, to examine it very carefully, very self-critically, whether your idea is indeed correct, to do the controls. But don't do other controls after a couple of years, do the controls right after your experiment. So I think that this combination of having these two mentors, Mager, the control, critical biochemist, and Tomkins is the inspiration, taught me to have inspiration together with controls, I think. That shows you how important are good mentors in science. Now after you are learning to do some science with mentors, and after you become an independent investigator, you have to find a subject on what to work in research. And I think the lesson is to find an important subject that is not yet interesting to others. Otherwise the big guys will get there before you, do not go with the mainstream. There is in every period there is mainstream science. There is the science that is right now, which seems to be the most important that is going on in science. Don't join them, don't do that. Because if you go with the mainstream, it will become kind of a competition. Who gets there first? And you can be sure that the other guy will get there before you, because he has a bigger lab, and he has many good people who work with him, so don't do that. Don't go with the mainstream. Try to find a research object that you believe it is important. If it is not important, there is no reason to work on it, but it has to be important. You have to believe it is important, and not to be mainstream. As you heard, I was again lucky here, I started to work on protein degradation at the time when most big laboratories were interested in protein synthesis. So I did that, I guess it can be done. It's not easy to find some subjects, but it's possible. Now, my next lesson was that accidental observations may be the most important ones. And to grab your luck when you get it. So I'm sure all of you that do experimental science know that we have many accidental observations. We have almost every day accidental observations, which we did not expect. Sometimes you get the opposite of what you expected. Sometimes you see something else. Now, shall I follow it up, or shall I not follow it up? That's always a big question. If you follow up every accidental observation, then you lose your direction. So you have to think about accidental observations, which may be important to your direction. You have to have a goal, so don't lose your goal. But you can approach this goal in different ways. And in my case, it was the finding that protein degradation requires energy, which was accidental, which I didn't expect it, but I thought it was important and followed it up. And I think it was, again, a good and lucky step in my work. Now, another lesson that I learned is to use whatever experimental approach is needed to reach your objective. It may not necessarily be the most fashionable or state-of-the-art technology. Again, there are fashions in science, in everything else. You have the most up-to-date technologies, and they are very powerful, but are they good for your research objective? You have to find them. Now, for example, we have all the omics, which are very powerful. But are they good for what you really want? You should think about it. If they are good, of course you should use it, because these are very, very powerful technologies. But use new and state-of-the-art technologies only if they are in your objective. If not, they don't use them. Use whatever is needed. For example, in my case, in the early 1980s, the powerful methodologies of molecular biology, molecular genetics came into general use. And as most many biochemists at that time became molecular biologists, but in my case, I saw that the only way to find out how proteins are degraded, how the ubiquitin system works, is by biochemistry, by finding the different enzymes that are involved, the different steps that are involved. Of course, later, all these work could be the basis for molecular genetics, for using genes or genetic manipulations in these enzymes to find out what are the functions of the ubiquitin system. So use whatever is good for your objective, but not necessarily the most state-of-the-art objective. Now, one more lesson was that science should not be always a curiosity-driven adventure. You should have a lot of excitement and fun in science. You have a lot of excitement in discovery. That's great. But science is not always fun. Many times, people are working in science in order to get data. They work to get data in order to publish a paper. They publish a paper in order to get an appointment or to get a grant, or to do the necessary things of publish or perish. So I don't say that you do not do that, but I say that should not be your most important thing in science. You should do that, but not as the main goal. Your main goal should be excitement, fun. You should follow up your curiosity. You're curious about something. You do an experiment in order to find out what's happening. And that way, you will make discoveries. So remember, science is fun. And do whatever has to be done, but don't do only whatever has to be done. And my last lesson, which may not be correct for everybody else, is never to leave Benchwork, and you should continue to have a lot of excitement and fun. As you heard, I am still doing Benchwork, and I love it, and I think it's great. And I do it because it's very exciting. When I do it myself, there is a lot of excitement until I know what are the results. And also, sometimes I make good progress in this way. So my advice is after you are getting senior, don't leave the bench and try to continue to benchwork. Thank you very much for your time. One more slide. Sorry. One more slide. You cannot do everything by yourself in the bench, so you need people. And I wanted to thank the people. One more. And I have many people in my lab, in the Technium, who helped me for many years, including my wife. And I wanted to thank them. I had many graduate students, including Aaron Chahanover, but many, many more, who helped me a lot in collaboration. It's also important to have good collaborators, and I got a lot of help from these people. Thank you very much. Thank you.
 Thank you very much for your kind introduction.  I would like to tell you about, or maybe to tell in a short way, the story of the discovery of the ubiquitin system for protein degradation.  I'll do that later to look at it and to find what are the lessons that can be drawn for this story,  mainly lessons for the younger people, for the young investigators, for the students in this audience.  So I am interested for a long time in the problem of how proteins are degrading cells, as you just heard.  And that was a subject that did not interest too many people at that time.  Following the great discoveries of the structure of the DNA, the double helix, in the 1950s,  and cracking of the genetic code in the 1960s, there was a huge and justified interest in molecular genetics.  So it was known that the gene is a stretch of DNA that is the blueprint for the formation of a protein  via an intermediary blueprint, the RNA.  And then proteins are synthesized for amino acids in the process of protein synthesis,  in which the amino acids are assembled in a sequence that is determined by the sequence of the bases in the DNA.  So as I said, there was a huge and justified interest in this process of how proteins are synthesized,  how the synthesis of proteins is turned on and off.  And because of that, there was a very little interest in the opposite process of protein degradation,  in which proteins are disassembled back to amino acids.  And however, it was already clear at that time, around 1970, that protein degradation carries out important functions.  And one important function is to eliminate abnormal proteins.  So our proteins are very sensitive structures.  They are very easily damaged, for example, by oxygen radicals, by hydro-damages,  and then they lose their normal conformations.  And the abnormal proteins can get in the way of the action of the normal proteins,  and they can actually kill the cells in which they are.  So they have to be eliminated.  The protein degradation system recognizes these abnormal proteins and eliminates them in a very efficient way.  However, it was already clear at that time that protein degradation is not simply just garbage disposal system  to remove abnormal proteins, because some normal proteins, completely normal proteins,  are also degraded in a selective rate.  Usually proteins that have some regulatory functions have rapid turnovers, and they are degraded rapidly,  whereas housekeeping proteins are more stable and can stay on for a long time.  So protein degradation of normal proteins is a selective process, it happens.  And it was clear at that time that the levels, because of that, the levels of specific proteins in animal cells  can be regulated not only by changes in rates of synthesis, but also by changes in rates of degradation.  That was recognized by Shemke at around the 1970s.  So to me it was clear that protein degradation is important process because of these observations,  but it was not known how proteins are degraded in such a highly selective and regulated mode.  So this was the information when I got to the lab of Gordon Tomkins in the University of California in San Francisco  as a young postdoctoral fellow, and Gordon at that time was interested in how a certain protein in liver cells,  certain enzyme liver cells is induced by steroid hormones, how hormones can cause the induction, the rapid synthesis of these proteins.  So when I got there, I saw that it was a large lab, there were about 25 different postdoctoral fellows,  they were all working on different aspects of the induction of the synthesis of these proteins by steroid hormones.  I saw that this was a bit too congested and I didn't want to work on what everybody else was working,  so I asked Gordon, can I have another subject?  And he said, yeah, why don't you work on the degradation of the same enzyme, tyrosine amino transphalase,  because it may also regulate the level of the enzyme.  So this is how I got on the problem of protein degradation, on which I'm working ever since.  And here in this slide you see one of the first experiments that I did in the Tomkins lab,  and I found then quite by chance that the degradation of this protein is completely arrested  by adding an inhibitor of cellular energy production, such as potassium fluoride.  So that is the rapid degradation of this enzyme in the control tube.  And when I added potassium fluoride, there was complete stopping of the degradation,  which surprised me greatly because I actually saw that maybe it will be degraded even faster when the cells don't have energy.  So it was a surprising observation, but I was very much impressed by it,  because why would energy be needed for the degradation of a protein?  The degradation of exocellular proteins that were known at that time, such as proteins digested in our digestive tract by trypsin,  chymotrypsin, did not need any energy.  Actually, it released some energy.  So why would energy be needed for protein degradation?  I thought maybe it is needed for the selectivity.  So maybe we have here a completely novel system that uses energy to achieve the high selectivity of intercellular protein degradation.  So following my return to Israel, I continued because of that to work on the mechanisms of intercellular protein degradation  because of these reasons.  So as I said, it was known to be important for the control of levels of cellular proteins.  It was an important process, but the pathways were not known.  And the energy dependence of protein degradation that I just described now suggested that it may be some kind of a novel previously unknown  biochemical mechanism that carried out intercellular protein degradation.  And another reason for working on it, important reason was that not many were interested, so I did not have to worry about competition.  So I returned to Israel from my postdoctoral fellowship, and then I thought, how should I approach this problem?  And I thought the way to approach it, apparently a complex system, and the way to approach it is by the biochemical approach,  which is first to make an extract.  We have to open the cell to find out what happens inside.  So one has to open up the cell, but in a way that facefully reproduces the process in the test tube.  So it's very easy to open cells to make extracts, but it's not so easy to make extracts so that they will facefully reproduce the process in the test tube.  In my case, I looked for an energy-dependent protein degradation in the test tube, in these extracts.  Once one has extracts, one usually fractionates the extract because it has many components, several enzyme components.  We have to find out what are the different enzymes.  So we fractionate the extract, which has thousands of different enzymes, to find out what are the important enzymes for us,  and then purify each enzyme component, characterize the action of mode of action of each purified component.  And the last and most important step in the analysis is to reconstitute the activity of the complete system by the addition of all isolated and purified components.  So I can try to find out how a watch works, a mechanical watch.  We have to open it up carefully, gently.  Take out the different components, such as springs and wheels, whatever it is.  Look at them and try to figure out how they work.  And then to put them back again to the watch, if the watch again works, then we really understood how the watch works.  So that's what we tried to do.  And our first step in this direction was published in 1978 by BBRC, which is a very small, not very prestigious journal.  But I still like this paper because it was the first step in the right direction.  And the experiment was made, was done by Aaron Chachanover, who was my graduate student,  and then shared the Nobel Prize with me, as you heard, for his part in this story.  So what was done is we found that in a lysate from reticulocytes, which are immature red blood cells,  we looked at the degradation of a certain protein, globin, and we looked at the degradation with or without ATP.  ATP, as you may know, is the source of energy in cells.  It is how energy is transduced in cells.  So as you can see in the lysate, without ATP, there was very little degradation.  But there was much more degradation in the presence of ATP, of energy source.  So this told us that we indeed have here the cell-free system that facefully reproduces energy-dependent protein degradation in the test tube.  And then he did a fractionation, simple fractionation of reticulocyte lysate to two fractions on a certain ion exchange resin.  And fraction one, which is all the proteins that do not bind to the resin, there was no degradation in the absence of presence of ATP.  Fraction two, where all the other proteins were, had some activity, some degradation, but most of the ATP-dependent activity was lost.  So we thought maybe there is something in fraction one that is missing in fraction two.  We combined back fraction one and fraction two, and indeed we could get back the complete activity, ATP-dependent protein degradation.  So this very simple experiment told us that the system that degrades a protein's independence of energy is composed of at least two components.  Now we know there is much more than two. But then we knew that there are at least two.  So we tried to find out what are these two.  And I first decided first to, we have to purify, and decided first to purify the active component from fraction one.  And that was a good decision because the purification of the active component from fraction one was the key to the understanding of the mode of the action of this system.  So we purified this component. It found to be a small protein.  Here a protein is separated on a gel.  And if you get only one band, then the protein is quite pure.  Here we had an increasing amount of the protein, and we could see that the active component was a pure protein.  It was a small protein. We called it that time factor one of the system.  But later it was found that it is similar to ubiquitin, ubiquitously occurring small protein that previously unknown function.  So we tried to find out what is the function of this small protein, ubiquitin.  And here we had a great prize.  We found that ubiquitin is covalently linked to the substrates which have to be degraded by this system.  And here the original experiment is shown in which we took our pure protein, ubiquitin, labeled it by iodine,  mixed it with completely crude fraction two, incubated it without or with ATP,  and then separated all the products of the reaction on the other gel, on the SDS gel,  without, under denaturing conditions.  So in this gel, usually small proteins run ahead and they separate by size.  So the small proteins run ahead and the larger proteins migrate slower and run below.  So following incubation without ATP, ubiquitin remained free and it ran ahead in the gel.  But following incubation of ubiquitin with fraction two with ATP, ubiquitin was bound to a huge number of high molecular weight proteins.  And then we saw this.  We suddenly understood or we had a hypothesis.  Until now we did not have a hypothesis.  We had a hypothesis that maybe ubiquitin binds to the substrates of the system  because fraction two contains not only enzymes but also proteins, substrates that have to be degraded by this system.  Maybe it binds covalently and maybe with this binding it targets them for degradation.  And to examine this hypothesis, we added the substrate, lysosyme, which was not a natural substrate,  but a good substrate, and as you can see there were several higher molecular weight bands  that contained both lysosyme and ubiquitin.  And we measured the ratios of the radioactivity between lysosyme is labelled or if ubiquitin is labelled.  And we found that these bands are increasing numbers of ubiquitin molecules  bound to one molecule of the protein of substrates.  So based on that we proposed in 1980 that the covalent ligation of ubiquitin to proteins is the targeting,  is the labelling or marking which marks these proteins for degradation.  And by we, I mean my collaborators, Irwin Rose, whom you mentioned from Fox Chase Cancer Center,  and Aaron Chahanowale, who was my graduate student at that time.  So here is the original proposal in the upper part of this slide.  So we proposed that the ubiquitin or APF1 is linked to the protein that has been degraded  and the several molecules of ubiquitin are bound to the protein.  And the hypothesis was that following these marking there is some kind of an enzyme  that recognises proteins which are bound covalently to ubiquitin, degrades them,  and then ubiquitin is being released for another use.  So this hypothesis explains the energy dependence of protein degradation  because the energy is needed for the marking process.  You need energy to make an amide bond.  In this case there is an amide bond between ubiquitin and the lysine groups of proteins  to which it is linked.  And it also explained the selectivity, as I say later on,  because the marking is selective and ubiquitin is linked only to those proteins  that have to be degraded.  And in the following 10 years or so we found that this hypothesis was essentially correct,  we found much more detail and the binding of ubiquitin to protein  is actually not done by one enzyme but by three enzymes,  enzyme one, two, and three, that work one after the other.  Enzyme one is the enzyme that activates ubiquitin, so this is the energy dependence step,  and then ubiquitin is transferred to another enzyme,  so it is transferred to enzyme three or ubiquitin ligase, which ligates ubiquitin to the protein that has to be degraded.  So ubiquitin ligases recognize proteins that have to be degraded  and transfer ubiquitin to the lysine groups of these proteins.  And now we know that there are around 600 different E3 enzymes  in the ubiquitin protein ligases in the human genome,  and we need this large number of ubiquitin ligases in order to recognize different proteins,  because each ubiquitin ligase recognizes a certain motif or certain characteristic  in the protein substrate that has to be degraded.  Following the ligation of ubiquitin to a protein, usually a ubiquitin chain is made  in which each ubiquitin is bound to the previous ubiquitin,  and then proteins thus ligated to ubiquitin chains are degraded by a large complex,  the proteosome complex that degrades only proteins that have been marked with ubiquitin.  And subsequently, ubiquitin is indeed released, free ubiquitin is released,  so that it can be used again for degrading another protein.  So this is the biochemistry, the basic biochemistry of ubiquitin mediator protein degradation  that we found out, and later on I got interested in the roles of this system  in cell division cycle, but I won't go into it.  And I just mentioned that work by many other groups showed that ubiquitin mediator protein degradation  is involved in almost every basic cellular process, such as cell division, signal transduction,  embryonic development, and so on.  And in all these cases, ubiquitin mediator protein degradation is by degrading regulators.  So either a regulator has to be active for a certain amount of time, and then have to be removed,  or an inhibitor, a negative regulator is being removed, and then the process can start.  And of course, ubiquitin mediator protein degradation also has an important protein quality control  to remove abnormal proteins, as I have described.  So the ubiquitin system is also involved in diseases such as in cancer,  in neurodegenerative diseases in which abnormal proteins accumulate in certain cells of the brain,  such as Parkinson's, Alzheimer's disease, certain types of mental retardation,  and muscle wasting.  And the ubiquitin system is involved in cancer.  I skip over there because I want to get to the lessons part.  And the ubiquitin system is already being used as a target for new types of drugs,  against certain types of cancer, but I didn't have time to tell you about that.  But because I want to get to the lessons part, because I think this is important for a young audience such as you.  So what did I learn from my life in science thus far?  I'm not finished as you heard, but that's why what did I learn?  I learned, first of all, I learned how important it is to have good mentors in your beginning,  in your first steps in science.  So you cannot learn how to do science, good science just from reading the literature.  You should read the literature, you should read all the literature,  but you learn how to do science by watching a person, a mentor.  How does he approach a problem?  What does it tell you, what is important to approach a problem?  So you need this human touch and you get the human touch from mentors.  So I was very fortunate to have very good mentors in my early time in life in science.  My first mentor was Jacob Mager, with whom I did my PhD at the Hebrew University in Jerusalem.  He was a biochemist of unbelievable knowledge in all various fields of biomedical sciences.  He really knew everything.  He was also a very, very rigorous experimenterist.  Each experiment had to do with all the controls, all the positive controls, all the negative controls.  Each experiment had to be repeated in different ways to ensure that your result is indeed correct  before going on further and relying on these results.  So I learned a lot from Jacob Mager.  I had a very good basis of good biochemistry, good strong stringent biochemistry in my early life in science.  And then I went on to do my postdoctoral fellowship with Gordon Tomkins at the University of California in San Francisco.  And Gordon was very different from Mager.  He did not care too much about controls.  And because of that he got into trouble several times.  But he had a lot of imagination, a lot of inspiration.  He was a source of inspiration to many, many people at his times.  He was really a genius, I think, in inspiration.  So I learned from Gordon how to do, how that inspiration is important.  You have to get out of the box to think about ways, about things in a new way.  But in science it's very important after you have an idea, after you have a fresh, a new idea, to examine it very carefully,  very self-critically, whether your idea is indeed correct, to do the controls.  But don't do other controls after a couple of years, do the controls right after your experiment.  So I think that this combination of having these two mentors, Mager, the control, critical biochemist, and Tomkins is the inspiration,  taught me to have inspiration together with controls, I think.  That shows you how important are good mentors in science.  Now after you are learning to do some science with mentors, and after you become an independent investigator,  you have to find a subject on what to work in research.  And I think the lesson is to find an important subject that is not yet interesting to others.  Otherwise the big guys will get there before you, do not go with the mainstream.  There is in every period there is mainstream science.  There is the science that is right now, which seems to be the most important that is going on in science.  Don't join them, don't do that.  Because if you go with the mainstream, it will become kind of a competition. Who gets there first?  And you can be sure that the other guy will get there before you, because he has a bigger lab,  and he has many good people who work with him, so don't do that.  Don't go with the mainstream.  Try to find a research object that you believe it is important.  If it is not important, there is no reason to work on it, but it has to be important.  You have to believe it is important, and not to be mainstream.  As you heard, I was again lucky here, I started to work on protein degradation at the time  when most big laboratories were interested in protein synthesis.  So I did that, I guess it can be done. It's not easy to find some subjects, but it's possible.  Now, my next lesson was that accidental observations may be the most important ones.  And to grab your luck when you get it.  So I'm sure all of you that do experimental science know that we have many accidental observations.  We have almost every day accidental observations, which we did not expect.  Sometimes you get the opposite of what you expected. Sometimes you see something else.  Now, shall I follow it up, or shall I not follow it up? That's always a big question.  If you follow up every accidental observation, then you lose your direction.  So you have to think about accidental observations, which may be important to your direction.  You have to have a goal, so don't lose your goal.  But you can approach this goal in different ways.  And in my case, it was the finding that protein degradation requires energy, which was accidental,  which I didn't expect it, but I thought it was important and followed it up.  And I think it was, again, a good and lucky step in my work.  Now, another lesson that I learned is to use whatever experimental approach is needed to reach your objective.  It may not necessarily be the most fashionable or state-of-the-art technology.  Again, there are fashions in science, in everything else.  You have the most up-to-date technologies, and they are very powerful,  but are they good for your research objective? You have to find them.  Now, for example, we have all the omics, which are very powerful.  But are they good for what you really want? You should think about it.  If they are good, of course you should use it, because these are very, very powerful technologies.  But use new and state-of-the-art technologies only if they are in your objective.  If not, they don't use them. Use whatever is needed.  For example, in my case, in the early 1980s, the powerful methodologies of molecular biology,  molecular genetics came into general use.  And as most many biochemists at that time became molecular biologists,  but in my case, I saw that the only way to find out how proteins are degraded,  how the ubiquitin system works, is by biochemistry, by finding the different enzymes that are involved,  the different steps that are involved.  Of course, later, all these work could be the basis for molecular genetics,  for using genes or genetic manipulations in these enzymes to find out  what are the functions of the ubiquitin system.  So use whatever is good for your objective, but not necessarily the most state-of-the-art objective.  Now, one more lesson was that science should not be always a curiosity-driven adventure.  You should have a lot of excitement and fun in science.  You have a lot of excitement in discovery. That's great.  But science is not always fun.  Many times, people are working in science in order to get data.  They work to get data in order to publish a paper.  They publish a paper in order to get an appointment or to get a grant,  or to do the necessary things of publish or perish.  So I don't say that you do not do that, but I say that should not be your most important thing in science.  You should do that, but not as the main goal.  Your main goal should be excitement, fun.  You should follow up your curiosity.  You're curious about something.  You do an experiment in order to find out what's happening.  And that way, you will make discoveries.  So remember, science is fun.  And do whatever has to be done, but don't do only whatever has to be done.  And my last lesson, which may not be correct for everybody else,  is never to leave Benchwork, and you should continue to have a lot of excitement and fun.  As you heard, I am still doing Benchwork, and I love it, and I think it's great.  And I do it because it's very exciting.  When I do it myself, there is a lot of excitement until I know what are the results.  And also, sometimes I make good progress in this way.  So my advice is after you are getting senior, don't leave the bench and try to continue to benchwork.  Thank you very much for your time.  One more slide.  Sorry.  One more slide.  You cannot do everything by yourself in the bench, so you need people.  And I wanted to thank the people.  One more.  And I have many people in my lab, in the Technium, who helped me for many years, including my wife.  And I wanted to thank them.  I had many graduate students, including Aaron Chahanover, but many, many more, who helped me a lot in collaboration.  It's also important to have good collaborators, and I got a lot of help from these people.  Thank you very much.  Thank you.
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Thank you very much for your kind introduction. I would like to tell you about, or maybe to tell in a short way, the story of the discovery of the ubiquitin system for protein degradation. I'll do that later to look at it and to find what are the lessons that can be drawn for this story, mainly lessons for the younger people, for the young investigators, for the students in this audience. So I am interested for a long time in the problem of how proteins are degrading cells, as you just heard. And that was a subject that did not interest too many people at that time. Following the great discoveries of the structure of the DNA, the double helix, in the 1950s, and cracking of the genetic code in the 1960s, there was a huge and justified interest in molecular genetics. So it was known that the gene is a stretch of DNA that is the blueprint for the formation of a protein via an intermediary blueprint, the RNA. And then proteins are synthesized for amino acids in the process of protein synthesis, in which the amino acids are assembled in a sequence that is determined by the sequence of the bases in the DNA. So as I said, there was a huge and justified interest in this process of how proteins are synthesized, how the synthesis of proteins is turned on and off. And because of that, there was a very little interest in the opposite process of protein degradation, in which proteins are disassembled back to amino acids. And however, it was already clear at that time, around 1970, that protein degradation carries out important functions. And one important function is to eliminate abnormal proteins. So our proteins are very sensitive structures. They are very easily damaged, for example, by oxygen radicals, by hydro-damages, and then they lose their normal conformations. And the abnormal proteins can get in the way of the action of the normal proteins, and they can actually kill the cells in which they are. So they have to be eliminated. The protein degradation system recognizes these abnormal proteins and eliminates them in a very efficient way. However, it was already clear at that time that protein degradation is not simply just garbage disposal system to remove abnormal proteins, because some normal proteins, completely normal proteins, are also degraded in a selective rate. Usually proteins that have some regulatory functions have rapid turnovers, and they are degraded rapidly, whereas housekeeping proteins are more stable and can stay on for a long time. So protein degradation of normal proteins is a selective process, it happens. And it was clear at that time that the levels, because of that, the levels of specific proteins in animal cells can be regulated not only by changes in rates of synthesis, but also by changes in rates of degradation. That was recognized by Shemke at around the 1970s. So to me it was clear that protein degradation is important process because of these observations, but it was not known how proteins are degraded in such a highly selective and regulated mode. So this was the information when I got to the lab of Gordon Tomkins in the University of California in San Francisco as a young postdoctoral fellow, and Gordon at that time was interested in how a certain protein in liver cells, certain enzyme liver cells is induced by steroid hormones, how hormones can cause the induction, the rapid synthesis of these proteins. So when I got there, I saw that it was a large lab, there were about 25 different postdoctoral fellows, they were all working on different aspects of the induction of the synthesis of these proteins by steroid hormones. I saw that this was a bit too congested and I didn't want to work on what everybody else was working, so I asked Gordon, can I have another subject? And he said, yeah, why don't you work on the degradation of the same enzyme, tyrosine amino transphalase, because it may also regulate the level of the enzyme. So this is how I got on the problem of protein degradation, on which I'm working ever since. And here in this slide you see one of the first experiments that I did in the Tomkins lab, and I found then quite by chance that the degradation of this protein is completely arrested by adding an inhibitor of cellular energy production, such as potassium fluoride. So that is the rapid degradation of this enzyme in the control tube. And when I added potassium fluoride, there was complete stopping of the degradation, which surprised me greatly because I actually saw that maybe it will be degraded even faster when the cells don't have energy. So it was a surprising observation, but I was very much impressed by it, because why would energy be needed for the degradation of a protein? The degradation of exocellular proteins that were known at that time, such as proteins digested in our digestive tract by trypsin, chymotrypsin, did not need any energy. Actually, it released some energy. So why would energy be needed for protein degradation? I thought maybe it is needed for the selectivity. So maybe we have here a completely novel system that uses energy to achieve the high selectivity of intercellular protein degradation. So following my return to Israel, I continued because of that to work on the mechanisms of intercellular protein degradation because of these reasons. So as I said, it was known to be important for the control of levels of cellular proteins. It was an important process, but the pathways were not known. And the energy dependence of protein degradation that I just described now suggested that it may be some kind of a novel previously unknown biochemical mechanism that carried out intercellular protein degradation. And another reason for working on it, important reason was that not many were interested, so I did not have to worry about competition. So I returned to Israel from my postdoctoral fellowship, and then I thought, how should I approach this problem? And I thought the way to approach it, apparently a complex system, and the way to approach it is by the biochemical approach, which is first to make an extract. We have to open the cell to find out what happens inside. So one has to open up the cell, but in a way that facefully reproduces the process in the test tube. So it's very easy to open cells to make extracts, but it's not so easy to make extracts so that they will facefully reproduce the process in the test tube. In my case, I looked for an energy-dependent protein degradation in the test tube, in these extracts. Once one has extracts, one usually fractionates the extract because it has many components, several enzyme components. We have to find out what are the different enzymes. So we fractionate the extract, which has thousands of different enzymes, to find out what are the important enzymes for us, and then purify each enzyme component, characterize the action of mode of action of each purified component. And the last and most important step in the analysis is to reconstitute the activity of the complete system by the addition of all isolated and purified components. So I can try to find out how a watch works, a mechanical watch. We have to open it up carefully, gently. Take out the different components, such as springs and wheels, whatever it is. Look at them and try to figure out how they work. And then to put them back again to the watch, if the watch again works, then we really understood how the watch works. So that's what we tried to do. And our first step in this direction was published in 1978 by BBRC, which is a very small, not very prestigious journal. But I still like this paper because it was the first step in the right direction. And the experiment was made, was done by Aaron Chachanover, who was my graduate student, and then shared the Nobel Prize with me, as you heard, for his part in this story. So what was done is we found that in a lysate from reticulocytes, which are immature red blood cells, we looked at the degradation of a certain protein, globin, and we looked at the degradation with or without ATP. ATP, as you may know, is the source of energy in cells. It is how energy is transduced in cells. So as you can see in the lysate, without ATP, there was very little degradation. But there was much more degradation in the presence of ATP, of energy source. So this told us that we indeed have here the cell-free system that facefully reproduces energy-dependent protein degradation in the test tube. And then he did a fractionation, simple fractionation of reticulocyte lysate to two fractions on a certain ion exchange resin. And fraction one, which is all the proteins that do not bind to the resin, there was no degradation in the absence of presence of ATP. Fraction two, where all the other proteins were, had some activity, some degradation, but most of the ATP-dependent activity was lost. So we thought maybe there is something in fraction one that is missing in fraction two. We combined back fraction one and fraction two, and indeed we could get back the complete activity, ATP-dependent protein degradation. So this very simple experiment told us that the system that degrades a protein's independence of energy is composed of at least two components. Now we know there is much more than two. But then we knew that there are at least two. So we tried to find out what are these two. And I first decided first to, we have to purify, and decided first to purify the active component from fraction one. And that was a good decision because the purification of the active component from fraction one was the key to the understanding of the mode of the action of this system. So we purified this component. It found to be a small protein. Here a protein is separated on a gel. And if you get only one band, then the protein is quite pure. Here we had an increasing amount of the protein, and we could see that the active component was a pure protein. It was a small protein. We called it that time factor one of the system. But later it was found that it is similar to ubiquitin, ubiquitously occurring small protein that previously unknown function. So we tried to find out what is the function of this small protein, ubiquitin. And here we had a great prize. We found that ubiquitin is covalently linked to the substrates which have to be degraded by this system. And here the original experiment is shown in which we took our pure protein, ubiquitin, labeled it by iodine, mixed it with completely crude fraction two, incubated it without or with ATP, and then separated all the products of the reaction on the other gel, on the SDS gel, without, under denaturing conditions. So in this gel, usually small proteins run ahead and they separate by size. So the small proteins run ahead and the larger proteins migrate slower and run below. So following incubation without ATP, ubiquitin remained free and it ran ahead in the gel. But following incubation of ubiquitin with fraction two with ATP, ubiquitin was bound to a huge number of high molecular weight proteins. And then we saw this. We suddenly understood or we had a hypothesis. Until now we did not have a hypothesis. We had a hypothesis that maybe ubiquitin binds to the substrates of the system because fraction two contains not only enzymes but also proteins, substrates that have to be degraded by this system. Maybe it binds covalently and maybe with this binding it targets them for degradation. And to examine this hypothesis, we added the substrate, lysosyme, which was not a natural substrate, but a good substrate, and as you can see there were several higher molecular weight bands that contained both lysosyme and ubiquitin. And we measured the ratios of the radioactivity between lysosyme is labelled or if ubiquitin is labelled. And we found that these bands are increasing numbers of ubiquitin molecules bound to one molecule of the protein of substrates. So based on that we proposed in 1980 that the covalent ligation of ubiquitin to proteins is the targeting, is the labelling or marking which marks these proteins for degradation. And by we, I mean my collaborators, Irwin Rose, whom you mentioned from Fox Chase Cancer Center, and Aaron Chahanowale, who was my graduate student at that time. So here is the original proposal in the upper part of this slide. So we proposed that the ubiquitin or APF1 is linked to the protein that has been degraded and the several molecules of ubiquitin are bound to the protein. And the hypothesis was that following these marking there is some kind of an enzyme that recognises proteins which are bound covalently to ubiquitin, degrades them, and then ubiquitin is being released for another use. So this hypothesis explains the energy dependence of protein degradation because the energy is needed for the marking process. You need energy to make an amide bond. In this case there is an amide bond between ubiquitin and the lysine groups of proteins to which it is linked. And it also explained the selectivity, as I say later on, because the marking is selective and ubiquitin is linked only to those proteins that have to be degraded. And in the following 10 years or so we found that this hypothesis was essentially correct, we found much more detail and the binding of ubiquitin to protein is actually not done by one enzyme but by three enzymes, enzyme one, two, and three, that work one after the other. Enzyme one is the enzyme that activates ubiquitin, so this is the energy dependence step, and then ubiquitin is transferred to another enzyme, so it is transferred to enzyme three or ubiquitin ligase, which ligates ubiquitin to the protein that has to be degraded. So ubiquitin ligases recognize proteins that have to be degraded and transfer ubiquitin to the lysine groups of these proteins. And now we know that there are around 600 different E3 enzymes in the ubiquitin protein ligases in the human genome, and we need this large number of ubiquitin ligases in order to recognize different proteins, because each ubiquitin ligase recognizes a certain motif or certain characteristic in the protein substrate that has to be degraded. Following the ligation of ubiquitin to a protein, usually a ubiquitin chain is made in which each ubiquitin is bound to the previous ubiquitin, and then proteins thus ligated to ubiquitin chains are degraded by a large complex, the proteosome complex that degrades only proteins that have been marked with ubiquitin. And subsequently, ubiquitin is indeed released, free ubiquitin is released, so that it can be used again for degrading another protein. So this is the biochemistry, the basic biochemistry of ubiquitin mediator protein degradation that we found out, and later on I got interested in the roles of this system in cell division cycle, but I won't go into it. And I just mentioned that work by many other groups showed that ubiquitin mediator protein degradation is involved in almost every basic cellular process, such as cell division, signal transduction, embryonic development, and so on. And in all these cases, ubiquitin mediator protein degradation is by degrading regulators. So either a regulator has to be active for a certain amount of time, and then have to be removed, or an inhibitor, a negative regulator is being removed, and then the process can start. And of course, ubiquitin mediator protein degradation also has an important protein quality control to remove abnormal proteins, as I have described. So the ubiquitin system is also involved in diseases such as in cancer, in neurodegenerative diseases in which abnormal proteins accumulate in certain cells of the brain, such as Parkinson's, Alzheimer's disease, certain types of mental retardation, and muscle wasting. And the ubiquitin system is involved in cancer. I skip over there because I want to get to the lessons part. And the ubiquitin system is already being used as a target for new types of drugs, against certain types of cancer, but I didn't have time to tell you about that. But because I want to get to the lessons part, because I think this is important for a young audience such as you. So what did I learn from my life in science thus far? I'm not finished as you heard, but that's why what did I learn? I learned, first of all, I learned how important it is to have good mentors in your beginning, in your first steps in science. So you cannot learn how to do science, good science just from reading the literature. You should read the literature, you should read all the literature, but you learn how to do science by watching a person, a mentor. How does he approach a problem? What does it tell you, what is important to approach a problem? So you need this human touch and you get the human touch from mentors. So I was very fortunate to have very good mentors in my early time in life in science. My first mentor was Jacob Mager, with whom I did my PhD at the Hebrew University in Jerusalem. He was a biochemist of unbelievable knowledge in all various fields of biomedical sciences. He really knew everything. He was also a very, very rigorous experimenterist. Each experiment had to do with all the controls, all the positive controls, all the negative controls. Each experiment had to be repeated in different ways to ensure that your result is indeed correct before going on further and relying on these results. So I learned a lot from Jacob Mager. I had a very good basis of good biochemistry, good strong stringent biochemistry in my early life in science. And then I went on to do my postdoctoral fellowship with Gordon Tomkins at the University of California in San Francisco. And Gordon was very different from Mager. He did not care too much about controls. And because of that he got into trouble several times. But he had a lot of imagination, a lot of inspiration. He was a source of inspiration to many, many people at his times. He was really a genius, I think, in inspiration. So I learned from Gordon how to do, how that inspiration is important. You have to get out of the box to think about ways, about things in a new way. But in science it's very important after you have an idea, after you have a fresh, a new idea, to examine it very carefully, very self-critically, whether your idea is indeed correct, to do the controls. But don't do other controls after a couple of years, do the controls right after your experiment. So I think that this combination of having these two mentors, Mager, the control, critical biochemist, and Tomkins is the inspiration, taught me to have inspiration together with controls, I think. That shows you how important are good mentors in science. Now after you are learning to do some science with mentors, and after you become an independent investigator, you have to find a subject on what to work in research. And I think the lesson is to find an important subject that is not yet interesting to others. Otherwise the big guys will get there before you, do not go with the mainstream. There is in every period there is mainstream science. There is the science that is right now, which seems to be the most important that is going on in science. Don't join them, don't do that. Because if you go with the mainstream, it will become kind of a competition. Who gets there first? And you can be sure that the other guy will get there before you, because he has a bigger lab, and he has many good people who work with him, so don't do that. Don't go with the mainstream. Try to find a research object that you believe it is important. If it is not important, there is no reason to work on it, but it has to be important. You have to believe it is important, and not to be mainstream. As you heard, I was again lucky here, I started to work on protein degradation at the time when most big laboratories were interested in protein synthesis. So I did that, I guess it can be done. It's not easy to find some subjects, but it's possible. Now, my next lesson was that accidental observations may be the most important ones. And to grab your luck when you get it. So I'm sure all of you that do experimental science know that we have many accidental observations. We have almost every day accidental observations, which we did not expect. Sometimes you get the opposite of what you expected. Sometimes you see something else. Now, shall I follow it up, or shall I not follow it up? That's always a big question. If you follow up every accidental observation, then you lose your direction. So you have to think about accidental observations, which may be important to your direction. You have to have a goal, so don't lose your goal. But you can approach this goal in different ways. And in my case, it was the finding that protein degradation requires energy, which was accidental, which I didn't expect it, but I thought it was important and followed it up. And I think it was, again, a good and lucky step in my work. Now, another lesson that I learned is to use whatever experimental approach is needed to reach your objective. It may not necessarily be the most fashionable or state-of-the-art technology. Again, there are fashions in science, in everything else. You have the most up-to-date technologies, and they are very powerful, but are they good for your research objective? You have to find them. Now, for example, we have all the omics, which are very powerful. But are they good for what you really want? You should think about it. If they are good, of course you should use it, because these are very, very powerful technologies. But use new and state-of-the-art technologies only if they are in your objective. If not, they don't use them. Use whatever is needed. For example, in my case, in the early 1980s, the powerful methodologies of molecular biology, molecular genetics came into general use. And as most many biochemists at that time became molecular biologists, but in my case, I saw that the only way to find out how proteins are degraded, how the ubiquitin system works, is by biochemistry, by finding the different enzymes that are involved, the different steps that are involved. Of course, later, all these work could be the basis for molecular genetics, for using genes or genetic manipulations in these enzymes to find out what are the functions of the ubiquitin system. So use whatever is good for your objective, but not necessarily the most state-of-the-art objective. Now, one more lesson was that science should not be always a curiosity-driven adventure. You should have a lot of excitement and fun in science. You have a lot of excitement in discovery. That's great. But science is not always fun. Many times, people are working in science in order to get data. They work to get data in order to publish a paper. They publish a paper in order to get an appointment or to get a grant, or to do the necessary things of publish or perish. So I don't say that you do not do that, but I say that should not be your most important thing in science. You should do that, but not as the main goal. Your main goal should be excitement, fun. You should follow up your curiosity. You're curious about something. You do an experiment in order to find out what's happening. And that way, you will make discoveries. So remember, science is fun. And do whatever has to be done, but don't do only whatever has to be done. And my last lesson, which may not be correct for everybody else, is never to leave Benchwork, and you should continue to have a lot of excitement and fun. As you heard, I am still doing Benchwork, and I love it, and I think it's great. And I do it because it's very exciting. When I do it myself, there is a lot of excitement until I know what are the results. And also, sometimes I make good progress in this way. So my advice is after you are getting senior, don't leave the bench and try to continue to benchwork. Thank you very much for your time. One more slide. Sorry. One more slide. You cannot do everything by yourself in the bench, so you need people. And I wanted to thank the people. One more. And I have many people in my lab, in the Technium, who helped me for many years, including my wife. And I wanted to thank them. I had many graduate students, including Aaron Chahanover, but many, many more, who helped me a lot in collaboration. It's also important to have good collaborators, and I got a lot of help from these people. Thank you very much. Thank you.
lessons that can be drawn for this story, mainly of the genetic code in the 1960s, there was a fluoride. So that is the rapid degradation of degrades them, and then ubiquitin is being described. So the ubiquitin system is also you, what is important to approach a problem? So inspiration. So I learned from Gordon how to do, the lesson is to find an important subject that is not yet interesting to others. Otherwise the with the mainstream. Try to find a research about accidental observations, which may be your objective, but not necessarily the most you will make discoveries. So remember, science