Judah Folkman Interview (page: 4 / 6) Cancer Research	Print Interview

What kinds of frustrations and setbacks have you suffered in your career? How do you deal with them?

Judah Folkman: Many setbacks. Most of the most difficult ones have been in the experiments that I've been doing for the past 30 years, because there it's very clear. And always the problem is knowing when you should give up or not. That's the big problem, I always found, is how long should you persist?

There's a fine line between persistence and obstinacy, and you never know when you've crossed it. So mostly, as I observed other scientists and read about them, many of them had given up. Fleming gave up on penicillin. He discovered it in the late '20s, tried to purify it, failed, and wrote in 1932, "I give up." He said, "This will never be useful because it's too unstable." And so it waited until 1941 till Florey and Chaine could figure out how to purify it. All three got the Nobel prize. So had he persisted, he might have had it many years earlier. There are many, many, many examples in science.
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The obstacles mainly were in the very beginning, in the late '60s, when we proposed the idea that tumors need to recruit their own private blood supply. That was met with almost universal hostility and ridicule and disbelief by other scientists. Because the dogma at that time was that tumors did not need to stimulate new blood vessels, they just grew on old ones. And that even if they could, after we showed it, the next disbelief was it didn't make any difference; it was a side effect like pus in a wound. So if you said you were studying wound healing and you found pus, they said you were studying a side effect, it's not important. And then after we showed it was important, which took us about five years (and we said there would be specific signals, molecules that would stimulate this, everyone said -- pathologists, surgeons, basic scientists -- said, "No, that's non-specific inflammation. You're studying dirt." They used to say, "You're studying dirt. There will be no such molecules." And then when we actually proved that there was -- that was now 1983 (starting in the late '60s), we had the first molecule. They said, "Well, but you'll never prove that that's what tumors use." So it was each step.
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Now it's not only well accepted that tumors are using specific molecules, they're actually made now, manufactured. When we said, "You should be able to turn off this process," everybody said, "It's impossible. Once angiogenesis is turned on, once they recruit their blood supply..." In other words, now they were using our own theories against us. They said, "Once they recruit their own blood supply." That's all accepted now. Every article now, a thousand articles a year, start out with, "It is well accepted that tumors are angiogenesis dependent."

You didn't just meet setbacks; you ran into actual hostility. How did you persevere?

Judah Folkman: Oh, yes. Ridicule. A lot of people would walk out of my presentations. There were many critics, very great experts who kept saying this couldn't be. I had one advantage. I kept saying, "I'm pretty sure they're wrong." And the reason is that I had been a surgeon for years. I was surgery chief at Children's Hospital.

When you operate on cancer, it was different than any other thing. It never stopped bleeding. You could operate on a kidney, a liver, or do any other surgery, and if you lost blood, the organ would stop bleeding. It would turn white. All of the vessels would clamp down and the anesthetist would say, "Stop, we've got to give a transfusion." But in a tumor it would never bleed, and if they could just keep bleeding and bleeding, and there was massive bleeding, and you would use up pints of blood, and all surgeons know that. I knew there was something different about these blood vessels. And the pathologists who were criticizing for example, had never seen the blood, because once we hand them the tumor, it's white, and so to them it's bloodless. And the oncologists, a further step away, had never come to the operating room, so they were looking at x-rays. And the basic scientist has only seen cancer in a dish. And it began to dawn on me that they were missing something, and I said, "These people are wrong."
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I never said it to them, because you waste your time battling like that. You just keep doing the data. I remember a second thing. I was in my lab at Children's Hospital.

We had ten years of really tough ridicule. I was sometimes very upset. And John Enders' lab was right next door, and he had won the Nobel prize for polio virus, a very quiet, reserved person. He also had a pipe. And he said, "This is just..." when grants would be rejected, he said, "This just proves that there are no experts of the future. There are only experts of the past, and they sit on the study section." So he said that you just have to take this in stride.
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One time I wrote this big grant in the '70s that outlined the whole field as it almost is today. That there would be inhibitors and stimulators, and you could turn off blood vessel growth, and there wouldn't be drug resistance, and you shouldn't attack the tumor so directly. Laid it all out. And then I got cold feet, and I went to him and said, "I think I'm giving away too much." And he looked at it and he said, "No, it's theft-proof." He said, "They're never going to believe this. You'll have to ram it down their throat and it will take you ten years." He said, "Very interesting." And then also my wife Paula, many, many times. It would be very upsetting to get rejections from journals many, many times, and rejections from grants and things, and you think that the work is really -- I remember one time in the study section, "Haven't we funded this work long enough?" It didn't seem to be going anywhere. It was hard work. They were going to just stop all the funding. And Paula would always say, "Well, what do you care? If you really think it's right, you should go on."
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It's easier now because it's all accepted. In about 1983 there was a big experiment that we published, which overnight converted most of the critics to competitors. So we had And now the principles are established, we have hundreds of competitors. There are hundreds of labs. There are 90 companies working on this. But...

The nay-sayers keep coming. There are always nay-sayers. And now they say, "Well, it works in mice, but it won't work in people." So I say, "So what? Should we not test? Should I stop because you know for sure?" And people come up, stand up at meetings, "I'm very perturbed. It cannot work in people, must not work in people. This only works in mice." So I do two things. I say, "Will you sign?" I have a little book that I carry. I say, "Will you sign for me? Because you're so sure, I can just publish your remarks directly and save a lot of government and taxpayers' money, and we won't do the experiments. We won't test in humans. We'll just say it won't work." And then you get this body reaction. And then I also have -- there's a slide that I have for occasional -- I don't get this so much any more, but the slide is the New York Times, and it's 1903, and it's two Harvard professors, on the front page, have shown the exact mathematics of physics -- these professors of physics -- of why it is impossible for man to fly, because you can't build a motor that could lift its own weight. And three months later they took off at Kitty Hawk, or four months, something like that.
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People who make these predictions can slow down a field, but they can still be wrong. There's still a lot of nay-sayers. They're all over the place. I also have begun to notice that the same nay-sayers -- and I never mention their names -- call me at home at night when they have prostate cancer. So they do believe something. It's being tested now and being validated in the clinic. We have seen it ourselves. We have children who are alive and well today from therapy at Children's Hospital, who would be dead because every other therapy failed. One at a time, by using experimental angiogenesis inhibitors, getting permission from the FDA, compassionate approval, one case at a time, because there's not enough of the drug to do big trials. And they've done beautifully. So we have a forecast of what's to come.

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