Well, where to begin?
I'm not going to tell you what this slide is about.
You'd have to come this afternoon, and we can talk about it.
But "Where Do Ideas Come From" is the title of my talk, and it's always a question of where to begin.
And I think this is a good place to begin because this is one of the joyful times
that happens to a Nobel Laureate that somebody decides they would like to remember
where you were at school, and I was at school here from age 5 to 11.
And they unveiled a plaque here, and some of the kids are there celebrating with me.
It's interesting to me because I already knew by the time I left this school at that age
that I wanted to be a scientist, but I didn't know the word.
The best I could come up with was I wanted to be an inventor,
as a result of reading comic strips about inventors.
And then I'd like you to see where it was that I lived.
I lived in a little village called Copley with a population
of only 1,500, and I'm curious, how many of you guys come from a village as small as that?
Not very many.
But it was a good place to live.
The school was about over here, and my home was up here, and there was a rather lovely
river there, the River Calder,
except for the fact that when I was a kid it was badly polluted, though it no longer is I'm happy to say.
If you go down this River Calder, you come to, there's Copley, and here is the River Calder...
You come to another town, Elland, and Elland has a population of 15,000, so it's a rather bigger town.
And it produced a Nobel Laureate in 1997 in chemistry.
If you go upstream from Copley, you come to another town, Todmorden, that also has a population of about 15,000.
It produced two Nobel Laureates. So the water?
(laughter)
Obviously not. (laughs)
The teachers is the answer.
The teachers inspire you and give you all sorts of thoughts.
And in fact, we can look at the teachers that were involved in all of these persons.
And Smithies had a good teacher in elementary school and two teachers in high school.
And Walker had a good science teacher.
And Cockcroft and Wilkinson both had the same science teacher, so that science teacher
was teaching for more than 20 years and produced, as it were, two Nobel Laureates.
So if you're a teacher, think how much influence you can have in the future.
Maybe you will have the enjoyment of being a teacher and being remembered.
Maybe you'll produce a Nobel Laureate, who knows?
So be a careful teacher when you're a teacher.
I had a grand teacher when I went to college.
I went to college in Oxford University, Balliol College.
And this is my teacher, "Sandy" Ogston.
He was trained in chemistry and then took a second degree in physiology and began to teach students,
in the medical curriculum, and I had won my scholarship to the college with physics,
but I for some reason that escapes me now, I decided to do medicine.
Anyway, "Sandy" Ogston was my teacher.
And he produced a Nobel Laureate in 1976 and another one in 2007,
so some teachers can really inspire you.
The way of teaching at that time in Oxford, and it still is the primary way, is a marvellous way,
and I wish we could do it more easily all over the world.
But it's an expensive way of teaching.
And that is that once a week, you would meet with your teacher,
in this case "Sandy" Ogston and present to him or her
an essay that you had written over the preceding week on a topic that had been assigned to you.
And you were expected to produce something that went back to the original literature.
You couldn't work with a textbook, or you might read
a textbook, you might read a review, but you were expected to write something original.
Might get a topic, "Oh, write me an essay on pain."
And that's all you'll be told, and you were expected to produce a learned article in a week. (laughs)
Well Sandy set me the topic, "Write me an essay, Oliver, on energy metabolism."
Now this was before the tricarboxylic acid cycle had been published, before Krebs' cycle.
And I set about this task.
And then I came across this.
And why would I show you a book?
I show you this book because what's in this book was so exciting that I remember where I was when I read it.
I remember what the book looked like.
I remember what the paper looked like.
It was so inspiring to read something that made sense out of what appeared to be nonsense.
And the nonsense was: Why doesn't the body just burn glucose and make carbon dioxide?
It goes through all these complicated things of adding phosphate and doing this and that and the other.
And why does it do it?
And this book contains the answer.
The answer is this little squiggle here, squiggle P, which means energy-rich phosphate,
an energy-rich phosphate bond.
And for the chemists, it's interesting that the energy-rich ones are all acid anhydrides,
and acid anhydrides are very powerful organic compounds,
have much more energy in them, for example, than a phosphate ester would have.
And anyway, true to form, I came back with an essay the following week.
And in it, I had Smithies' cycle.
And it was rather a neat cycle because you could start with an inorganic phosphate and make a phosphate ester,
and that's relatively low energy and take away a couple of hydrogens.
And you can convert the phosphate ester into an acid anhydride here,
and that's energy rich, from which you could make ATP.
And then go around here and add the hydrogen back,
and you could start over again, and you could produce energy for nothing.
Well, I wasn't completely stupid.
I did know it was wrong, but I didn't know why it was wrong.
And that was an interesting problem.
And "Sandy" Ogston proceeded to write an article on it eventually because it turned out
that people had forgotten in making the calculations that you had to think about the concentration of things,
not just about what was called standard free energies in those days,
where every reaction component was at one molar concentration.
And he worked out that there had to be a system that produced energy in moving electrons up the
electromotive scale, you might say, in the cell.
So he foresaw the importance of energy by concentration,
and he also realised that the system wouldn't work if the substrates dissociated from their enzymes.
They had to be handed over as it were without dissociating into free substrate.
Otherwise, the kinetics would be wrong, so it was a good article.
And he published it, and he was kind enough to add my name as a scholar of Balliol College,
and I felt pretty good about this.
And then this was 1948, so it's quite a long time ago.
But then somewhere around about, oh let's say, I don't know the exact date,
but say 1990 or thereabout somebody came up to me and said, you see 1990 would be
40 years later than this, and said, "Oh are you that Smithies who had an article in Physiological Reviews?"
And I rather modestly said, "Well as a matter of fact, I am."
(laughter)
And he said, "Oh I thought you were dead." (laughs)
(loud laughter)
So anyway, on with the game, and here's my PhD thesis, and you can see a lot of significant figures here.
And in fact those are real significant figures.
They're not due to not rounding off in a computer,
which is the common method of getting many significant figures.
But you can see that my experimental points are really rather closely together,
and I was measuring osmotic pressure.
It's not very important to know what that is,
but the points were so close that I had to interrupt the line to put the theoretical line on,
so I was very proud of this super precision method.
And I published it, "A Dynamic Osmometer for Accurate Measurements," a neat paper.
It has a record.
Nobody ever quoted it.
(laughter)
Nobody ever used the method again, and I never used the method again.
So you have to ask yourself, "Well what was the point of it?"
And I want you to think a moment.
Well the point of it was that I learned to do good science, and I enjoyed it.
And those are the critical things in the early stages of your career that you learn to do good work and to enjoy it.
It does not matter what you do.
It's absolutely unimportant.
You do not want to be a clone of your advisor.
You do not want to be a clone of your post-doctoral advisor.
You want to be yourself, but you can learn from these people
how to do good science, but you must be enjoying it.
Otherwise, you won't have that fire that's needed.
So I urge you, if you aren't doing what you like,
go to your advisor and say, "I need another problem. I'm not enjoying it."
If your advisor can't do that, change your advisor.
(laughter)
I'm serious.
It's so important because it's very unlikely, and I hope it is true that you will do work
of the same type that you did when you were a graduate student or when you were a postdoc.
You may use the skill, but you hope to do something different.
And I didn't achieve that in my graduate work or in my postdoc.
My postdoc was equally undistinguished, but I went to Toronto to get a job.
And there I was given a job by David Scott, and he was an early worker in the field of insulin work
because insulin was discovered in Toronto,
and he was the first person to crystalize it and make a long-lasting insulin.
And he said, "You can work on anything you like as long as it has something to do with insulin."
And I thought,
"Well, I read the literature, and I came to the conclusion that insulin was probably not the first product that was made.
There might be a precursor."
Well, we now know there is a precursor.
But in case you're waiting, I did not discover it, but I tried.
And on the way, I had to find a way of looking at insulin,
thinking I would find something slightly different in electrophoresis.
And in those days, much electrophoresis was done on filter paper, where you would soak a filter paper with buffer,
apply the protein, and allow it to migrate, and you can it just unrolled like a smear
and really was very poor, and I was rather frustrated.
And then I heard of the work of these two gentlemen:
Kunkel and Slater, and they'd use a box, a box about this big, this big and so on.
And they filled it full of starch grains, rather like a sandbox, except there were grains of starch,
and they had buffer around it, and they applied the sample in the starch.
And the advantage was that unlike the filter paper...
This is from their paper... Here's a protein applied on filter paper, and it smeared, just as my insulin smeared.
But when they put it on the starch grain, it came out as a nice peak.
But in order to find the protein, you had to cut it up into 40 slices and do a protein determination
on every slice, so you had to do 40 protein determinations for one electrophoresis run.
I didn't even have a dishwasher in my lab, didn't have a technician.
I couldn't do that.
But I remembered helping my mother do the laundry, well I was there anyway.
"Helping" might be in quotation marks.
(laughter)
She took starch powder and cooked it up with hot water and made a slimy mix,
which was used to apply to collars of my father's shirts, which needed to be stiff, and so it was ironed.
And when you tied it up at the end of the day, the starch, it set into a jelly.
And I thought, "Well my gosh, if I go back and make a starch gel out of the starch, cook it up,
and then I can stain it, and I will get rid of all of that problem of 40 slices."
Saturday morning was when I had that.
And by the afternoon, I'd started my first experiment with it.
There is a slot, and there is the insulin as a nice band and made the remark,
"The results are very promising."
And that was the beginning of gel electrophoresis.
It went on because some time later just for a rough test,
I put plasma or serum onto it,
and I could see the bands that were known of the proteins that were known to be present in blood at that time.
People thought there were five proteins: albumin, alpha-1, alpha-2, beta, and gamma globulin.
We now know there are about 700 or something like that.
But anyway at that time, people thought five, and I got these bands and set it up again, oh 12 midnight.
(chuckles) I was a bachelor.
And I could work at any time.
And excuse me, and then a little bit later,
I managed to see this sort of a pattern with many bands, and I had too many bands to label.
In fact, I could find 11 all together, and here's when if you have a good boss,
you can really make a step forward because I went to Scottie, as by then he and I called each other Scottie and Oliver.
I went to Scottie and said, "Scottie, I've really found something very interesting.
I'd like to stop working on insulin and work on this problem."
And he said, he was a good scientist, "By all means, change", and that I hope you have that experience.
You see I was long past my postdoc when it happened to me... That you get a time when you see you found something
that you ought to do that's different from what has happened in the past.
And I was ready to publish my work, and these are two of my friends.
I got tired of bleeding myself and so I got blood from my friends.
And I mean that's what they're for, isn't it?
And that's George Connell and Gordon Dixon, and why aren't there photographs?
My lab didn't own a camera.
It was such a poor lab at that time.
But I was about ready to get ready to publish and getting photographs made.
And then just by chance, I ran another sample from BW, and it was very strange, many extra bands.
And so what was funny about BW?
It was a woman.
This is the first time that I'd run a sample from a woman.
I thought I found a new method of telling men from women.
(loud laughter)
And I called one pattern the M pattern and the other pattern the F pattern: M for male, F for female.
And I could do two samples in a day for about a week or so, male and female always fit right.
And then the sixth time, they were changed.
And the man had changed into a woman.
We gave him a real hard time.
Come on Casey. Let's have look.
But anyway, such is youth you might say.
But here is my data file.
Just remarkable, but it turned out the difference between the types had nothing to do with gender.
It had nothing to do with the existing blood groups, and it was obviously something new.
And I show this for another reason.
It's a data file that's now, well what, almost 60 years old.
You won't be able to produce your data file 60 years from now if you don't make a hard copy.
You got to make hard copies of the important data that you have.
Don't rely on your computer because you can't read a floppy disc now, and there was a time
when that was what we had.
You won't be able to read a CD in 10 years from now, for sure.
Make some hard copies and keep good hard copies.
Well those differences that were here turned out to be genetic.
And just to close this story, it was a rather complicated genetic difference, and we worked it out with the help
of Norma Ford-Walker, who was a marvellous geneticist and taught me genetics.
And then as things moved on,
we changed from not being able to do protein sequencing to be able to protein sequence,
isolating genes, sequencing gene, and it began to become clear
that there was something that one might do about this.
For example, Linus Pauling and Harvey Itano and Vernon Ingram showed that the sickle cell mutation was
just due to a change of glutamic acid to a valine in the globin molecule.
And I began to think it ought to be possible to correct the gene by gene targeting.
We now are at a stage where we had cloned DNA, a normal DNA.
And I thought if I introduce a piece of normal DNA, I might be able to get some crossing over,
so SA lining up with SA and GE and change the bad gene into the good gene by crossing over.
I knew it was possible in yeast, and Jack is here today... I don't know whether he's here in the audience now,
but Jack and Terry Orr-Weaver had shown that in yeast
you could target a gene, and I was teaching, so I had taught this.
But the yeast genome is about, well what, two orders of magnitude smaller than the human genome.
And so whether it could be done in a human was not at all clear.
And then again in teaching "Where do ideas come from?"
When you teach, you have to understand.
And in order to understand, you sometimes have to spend
a long time reading a paper before you can understand it well enough to teach it.
And this was a paper that came out April 1st in 1982,
and they talked about a method of rescuing a gene, and I can't go into the details, except to say, because of time,
that it involved finding a piece of blue DNA, you might say, next to red DNA.
The red DNA was what they wanted to isolate, and the blue DNA was what they used to find it.
And I thought that I could use this method for gene targeting tests.
So here's, only three weeks after that paper came out, an assay for gene placement.
And my idea was to use their blue DNA, which you could score in bacteria
and try to target the beta globin gene and look for this fragment.
I should say: this is incoming DNA, this is the target.
If I could find a piece of DNA where these two were together, I would've proved that targeting had occurred
because this was not on the incoming DNA, and this was not on the target.
And with quite a lot of work, we got further down and got to the stage of simplifying it
and used a rather simpler plasmid, which looks very like the one that Terry Orr-Weaver had used,
and you could see that if you hit the gene, this is a restriction enzyme map that in the right way,
you could isolate a fragment of DNA that would be 11 kilobases if you didn't hit the gene.
If you hit the gene, then the size would be eight kilobases.
And a long set of experiments led to the final day,
when on a Saturday when I developed a film of testing different colonies,
and there is the one where the fragment is now a seven, eight kilobases long instead of larger,
so this proved that gene targeting was possible.
And once you've proved something is possible, then you can go and use it, and other people will start to do it.
But the frequency was hopelessly low and not practical for the original purpose,
which was to try to help a person with sickle cell anaemia.
So what to do?
Talk to somebody else, and I went and read about Martin Evans' work, which was using an embryonic stem cell.
Here is a blastocyst.
That's the part of the blastocyst that will give rise to the embryo.
And what Martin Evans and his students learned how to culture those in culture,
so that he had these cells growing in culture from a cream-coloured mouse.
And if you put these cream-coloured stem cells back into a blastocyst, they would remember where they came from,
and you could generate a mouse from this blastocyst by putting it back into a pseudopregnant female,
and you would get chimeric mice, mixtures.
And from them, you could breed out the gene that you were interested in.
So that was an obvious thing.
Let's use this method to alter gene.
But the assay was terrible.
And so we had to have help from a chemist, and we got help from Kary Mullis,
who got the Nobel Prize for inventing polymerase chain reaction.
And here is a little place in one of my notebooks, saying that we could use this method to detect the recombinant.
And I made an apparatus to do it.
This is my apparatus.
Why would you make an apparatus?
Well the reason was there wasn't one available.
You could not get an apparatus for doing PCR.
But I think this ought to have this label on it because that's what my graduate student friends used
to put on an apparatus that was lying somewhere on the floor.
And it stands for NBGBOKFO, no bloody good, but okay for Oliver
because I would always make stuff out of junk, you see, and so these are all junk things.
None of them were new, and yet that's the apparatus which we used and helped me towards the Nobel Prize.
The method was good, and here's a super article about it, and you notice I'm not an author.
I'm happy to say the author is down there.
She's my wife, and she went and made a marvellous animal that could get atherosclerosis.
"Impossible in the mouse," everybody said.
Well, so where to?
Well, I'm showing you this one more thing because I have one little more topic to talk about.
Here's "Sandy" Ogston again, but there's a little difference now because I've got the date of his death.
Because he asked, "When I die, Oliver, I'd like you to write my scientific memoirs."
That was something that the Royal Society liked to have.
And then you have to read all of his papers.
And I read all his of his papers.
And then he had this beautiful, little formula here, talking about the available space in a gel
to molecules of radius big R when the gel is composed of fibres
of radius little r, and there are n fibres per square centimetre.
He was talking about a cross section of the gel.
And this equation is beautifully precise.
It worked in every gel you ever heard of and has been tested inordinately.
These two guys in my lab, and they made this diagram to illustrate it, and I like it.
If you have a small solute, it can find lots of space in a gel.
But if you have a large solute, it can only find a limited space.
And so I thought this might apply to the kidney, and I wrote a paper on this that the idea being that here
the small molecules would come through the kidney easily.
And big molecules, if they had to pass through a gel, would come rather low concentration,
and I published a diagram illustrating the principle.
This is a cross section of a kidney at electron microscope dimension.
And these are the sizes of albumin molecules drawn to scale,
and this is the gel in the kidney through which I thought the thing might happen.
And so I went to our local person who was an expert in making a gold nanoparticle,
which I wanted to use, to see in the electron microscope.
And he said, I'm not going to make them for you, Oliver.
You make your own.
He said, "You'll learn more if you make them."
I got hooked.
They're marvellous, interesting things, and I spent a large amount of my personal time on them.
I'll just show you one example here.
That's what, four years ago.
And this was the time when I first learned... Was still working at the weekend.
This is the time when I found out that I could control the size of the molecule by varying the time
of a reaction step in the procedure.
I got a paper out of it in Langmuir, and I'm the first author.
And I'm the first author because I did the work,
not because I wrote the paper, though I did, but because the experiments were mine, most of them.
And so, think about it.
It's really rather neat to have a first author paper when you're 89 and especially if this is
the first paper I ever published in a chemistry journal.
But I have one more... Oh there's an example of working of it.
Here is plasma with the large molecules in clusters, and they can't get into the basement membrane.
It's more complicated than that, but that's an example.
I've one last, a little thing to show you, and that's this. And what am I showing an aeroplane for?
Wel,l partly because that's been a part of my life, but this is my instructor, Field Morey.
And he taught me to fly, and I was a nervous flyer.
And when I learned to fly with him, instructor sits here, and the pupil sit in the left seat.
And sweat used to pour off me, I mean literally.
And so one day I turned to him and said, "That was a good day for you. Only one drop dripped."
That gives you some idea.
Well, I later on learned to be an instructor, and I had a pupil, Jeff Bloch.
And when we went flying together, I was teaching him to glide, he would come back absolutely sodden.
His back would be completely sticking to himself.
He went by himself when the time came, and he came back, and he said, "Look Oliver, dry."
That's a very important lesson, not just for flying.
It tells you that you can overcome fear with knowledge.
If you're nervous about doing something new in science, you might say, "This guy over here, he's much smarter than me.
Or this lady, she knows what to do. I couldn't possibly do that."
You're frightened.
Go and learn.
Go and read.
You can do anything.
You can change fields.
You don't have to be stuck somewhere.
Go away and overcome fear with knowledge.
That's my motor glider, and here's my companion.
And if you're lucky, you will have a companion as I have in Nobuyo, and that's where I stop.
applause