I would like to tell you what I've learned from my life in science.
And that is a history, or ancient history if you wish,
but I think there is a good reason to talk about my history in science
because young people (and this is intended, really, for young students) may learn something
from my life in science.
And in this slide I've listed lessons from my life in science.
I labeled it "thus far" because I am not done as of yet.
I may have some more lessons as I go on. But, thus far.
So, lesson number one is how important are good mentors.
You cannot learn to do good science just from reading articles or books.
Of course, you have to read articles. You have to read books,
but you learn how to approach science from people, from mentors.
And I had...I was very fortunate to have great mentors
in my early life in science.
My first mentor was Jacob Mager at Hebrew University in Jerusalem.
He was a great biochemist. He was also a very rigorous experimentalist.
Every experiment had to be done with all the controls.
Every result had to be verified from all aspects.
So, I owe a lot to Jacob Mager for a strong background of rigorous biochemistry.
After I did my...after I finished my PhD,
I went on to do my post-doctoral training with Gordon Tomkins
from the University of California in San Francisco.
And Gordon was quite different from Mager.
He did not care too much about controls, but he had a lot of inspiration, imagination.
He was bursting with new ideas.
Now, it was very fortunate to have this combination of Mager and Tomkins
as my early mentors in science because in science it is important to have imagination,
but it's also important not to be carried away with your imagination
and to check rigorously whether your ideas are indeed correct.
So this combination of these two mentors had a great impact in my further life in science.
Now, my second, next lesson here is not to go with the mainstream
and try to find an object which is important, but which is not yet interesting to others.
So when I came as a post-doctoral fellow to the laboratory of Gordon Tomkins
he worked mainly on how steroid hormones caused increased synthesis of enzymes
using a certain enzyme. And when I got there, I saw it was a big lab with 20 post-docs,
more than 20 post-docs, working on different aspects of the synthesis of this protein.
So, I saw this was too crowded and I asked for something else.
And I got interested in the degradation of the same enzyme.
Now, protein degradation was not very much a point of interest at that time.
But I thought that the degradation of proteins is also important
as a way to regulate levels of proteins in cells.
So that's how I got my subject.
But make sure that you are working on a biologically important subject,
otherwise there is no point to do this research.
And then the third, number three, lesson that I learned
is that accidental observations may be the most important observations.
Sometimes when you make an accidental and unexpected observation,
grab it if you think it's important.
You don't have to go after all the unexpected observations, but after the important ones.
My unexpected result is an experiment that I did when I...
One of the first experiments that I did when I was a post-doctoral fellow.
I looked then, at the degradation of this enzyme that was studied in the laboratory,
the peptidyl aminotransferase, and you can see that it is degraded
quite fast with a half lifetime of about 2 to 3 hours.
So half of it was degraded between 2 to 3 hours. That is the control.
And then I added...I tested the effect of different compounds.
I thought that it would be degraded even faster when I add to it some poisons
such as potassium fluoride, a poison of energy production.
And actually what I got was just the opposite.
As you can see, potassium fluoride completely stopped the degradation of the enzyme.
Whenever it was added, it stopped it completely.
And so the result was just the opposite of what I thought it would be.
But then I began to think, and I was very much impressed by it
because it actually showed that you need energy to degrade proteins in cells.
And that turned out to be general--you need energy to degrade all proteins in cells.
And that is very different from the degradation of proteins outside of the cells.
For example, in our digestive system, when proteins are digested
actually you release energy. So I thought, "Why would you need energy?"
Thermodynamically, actually, it made sense
because you need energy to make order for selectivity
and protein degradation was known to be selective.
Some proteins were degraded very fast, some proteins were degraded slow.
For selectivity you need energy.
But what is the mechanism? There must be some kind of a new mechanism
in which an energy dependent step is involved in protein degradation.
So, I was so much impressed by this experiment that I continued to work on it
for many years until we found why energy was needed,
and how proteins are degraded in cells,
and why energy is needed for protein degradation.
That is my next lesson: Use whatever experimental approach is needed for your objective.
It may not be necessarily the most fashionable or so called "state of the art" technology.
So, I used biochemistry because I saw that we needed biochemistry
to dissect a completely unknown system.
And as I went along, that was in the early '80s,
the powerful methodologies of molecular biology came into general use.
But I saw that in order to find out how a completely novel system works,
you cannot use techniques of molecular genetics.
You can use them when you have some idea about the players
or the enzymes or the proteins involved in that process.
So I used old-fashioned biochemistry, if you wish,
at the times of modern molecular biology, but I thought that was the way to go.
So use whatever is necessary to get your objective.
Don't go only after the current fashions.
So using biochemistry, we isolated in '77 and '78
some of the players of the research: a small protein, ubiquitin,
which we found to be, in a cell-free system,
to be required for energy dependent protein degradation.
And by we I mean people in my lab at the Technion, including Aaron Ciechanover
who was then my graduate student.
And what this small protein is doing was found out two years later,
'79, '78, when we discovered that this ubiquitin becomes linked
to proteins that are destined for degradation, and we proposed that
the this linkage tags proteins for degradation.
And, again, here by we I mean people in my lab at Technion
including Aaron Ciechanover and in collaboration with Ernie Rose
in whose laboratory in the Fox Chase Cancer Center in Philadelphia
I spent a sabbatical year and returned there for many summers afterwards.
Now Ernie Rose was the third person who had a significant impact on my life in science.
He is very different from me. He likes problem solving.
He's very analytical and I am more intuitive so we kind of complimented each other
in that important combination of intuition and analytics.
He's also very sharply critical so he criticized me many times when it was needed,
when I got carried away inspite of my rigorous training with Mager.
So Ernie Rose had an important role in the discovery of ubiquitin mediated protein degradation.
The upper part of this slide shows the original marking hypothesis that we
made in 1980. I won't go into the details.
But what we found, what we proposed was that
proteins are marked for degradation by their linkage to ubiquitin
and that linkage requires ATP or energy
and that actually explains our original observation: why energy is needed for protein degradation.
It is needed for the tagging, mainly for the tagging reaction
of the linkage of ubiquitin or APF1 to proteins.
So, this elucidation of the basic biochemistry had an important
role to find out by others what are the physiological roles of this system,
and some are listed here. It is very important in the control of cell division
and I have been working on this personally in the past almost 20 years.
Certain types of signal transduction and so on--I won't go into all of them.
But, I always believed that protein degradation is important, but
I have to be frank and to say I was surprised by how many
destructive processes are used in biological regulation.
And because protein degradation is involved in so many processes
it's not surprising that the ubiquitin system is also involved in many diseases,
in many types of cancers and also neuro-degeneration and other diseases.
And there are even some new drugs that are being used based on these basic discoveries.
There is a proteasome inhibitor called Velcade, which is quite effective
for the treatment of an awful disease, multiple myeloma, a bone marrow cancer.
And because my original background is from medicine,
it is personally very gratifying to me that our basic research now can actually help sick people.
So, continuing with my lessons is when I look back on my life in science
I realize how much fun I had. I have a lot of fun, a lot of excitement.
And I think that this is the way to make discoveries.
In science, we have fun and we have chores.
We have to produce papers in order to find jobs, to get promoted, to get grants,
but we should not just...we should not let our chores become the main thing in our life in science.
The main thing is excitement. If you are excited, if you are having a lot of fun,
that's how you will make discoveries.
So, don't forget: don't let the chores overcome your excitement.
And then another lesson, my last lesson, is never to leave benchwork.
Some people when they get more senior leave benchwork,
and I have not. I always do like experiments.
I almost always do it on a daily basis, and I am continuing to have a lot of fun.
When you do experiments with your own hands instead of just telling somebody to do it,
there is a lot of involvement. You are personally involved.
You are very excited when you want to see the results, and
when you see the results that are unexpected you get even more excited,
and you try to find out why is that until you find the right answer.
So, continue to use benchwork and you will have a lot of excitement and fun.
Of course, you cannot do all the work by yourself.
You need the help of dedicated people--students, post-docs.
And I was very fortunate to have many and some of them are mentioned here.
I can't go through all of them, but these are some people in my lab at the Technion.
I had close to 30 graduate students, including Aaron Ciechanover
who shared the Nobel Prize with me,
and I would like again to mention the important contribution of Ernie Rose.
And the last, I would like to show some of the people who either
participated or witnessed this discovery.
This picture was taken at the end of the summer of 1979
when we made the breakthrough together with Ernie Rose
at the Fox Chase Cancer Center in Philadelphia.
In the center you can see Ernie Rose.
And I am sitting down there. Aaron Ciechanover is standing next to me.
So, we were all much younger at that time.