@OmicsOmicsBlog The best thing we can do to cure cancer, might be to try not to cure cancer, but just fund basic research? accurate?— Kumar Thangudu (@datarade) November 8, 2016
I've been essentially out of cancer research for five years, which has been making writing this challenging. I don't think about these topics routinely. But I should.
In the interest of disclosure, and because I think it is pretty amazing stuff, my employer has a program targeting KRAS. My role in that program has mostly been foundational; our early genome mining efforts reduced the perceived risk with that strategy. That's a story for another place and time (especially since so little is in verifiable public sources), but since I hold equity in the company I could be perceived as holding a conflict of interest. So I'm declaring that possibility.
From my semi-outsider's perspective, I'd say we can divide the current oncology pharmaceutical world into three categories. I'm fully aware that trying to draw bright lines is often a mistake, particularly in biology. Traditional cytotoxics simply try to kill rapidly-dividing cancer cells faster than they kill the rest of our cells; there is no aspect of specifically targeting cancer cells. Targeted therapies aim at known aspects of tumor biology. Finally, a white hot field right now is immuno-oncology, approaches which enlist the immune system to attack cancer. If you look at both research and industry financing, I think think you'd find not much for cytotoxics and large amounts split between targeted and immuno-oncology. I fully recognize that each of these broad categories I've defined are very, very heterogeneous. For example, I-O includes checkpoint inhibitors, vaccines and engineered T-cells -- and probably a bunch more.
If you were selecting a portfolio of research priorities for cancer, how would you invest? In addition to the three options above, a fourth might be "none of the above". In particular, this option might be to try an indirect route to future therapies by further non-targeted work on basic cellular biology and genetics.
Bruce Booth wrote a nice piece this summer surveying both the excitement in immuno-oncology and the immense challenge. The excitement is because when I-O works, it really works: durable cures. The first problem is that we just don't understand which patients will and will not benefit from existing I-O therapies. Another problem is safety: these therapies are generally well-tolerated, but can make patients initially much sicker, can induce auto-immune diseases and most recently have been found to sometimes have off-tumor affects which can be lethal. A next round question is how to combine I-O agents with each other or with cytotoxics or with targeted therapies; as Booth explained the number of possible combinations far outstrips any reasonable capability to test them.
The other problem in the I-O space, which I've heard a few executives complain about, is that it is so white hot that everybody feels they must be in the game. So compounds are getting touted as I-O drugs that don't really belong there. In other words, there is the real danger of an I-O bubble arising, and like all other bubbles that would mean poor allocation of critical resources and ultimately patients being ill-served.
Targeted therapies have delivered value, but not the durable cures which were long hoped. I knew someone who died from complications of CML a few years before imatinib (Gleevec) was developed; I wish she had lived to get the gains from that drug, even if many patients do not achieve a cure. But too many targeted drugs in monotherapy have led to remissions on the order of a year -- a gift of a year to patients, but not the desired cures.
The logic behind many targeted therapies predate the Human Genome Project (HGP) and Cancer Genome Project (CGP), but the CGP and further cancer genomics efforts have led to a wealth of new oncogene and tumor suppressor candidates. More importantly, in my mind at least, is that cancer genomics has pegged specific genes to specific cancers on a scale far beyond what prior efforts had done. The basis for many of these connections is still a mystery, but it has helped guide us in which compounds should be used on which tumors.
Cytotoxics are largely out of vogue. They are still very important and dominate cancer care and interest in new ones never quite goes extinct, but they definitely aren't favored strategies. We have many indiscriminant poisons that somehow achieve usable results in a subset of tumors; why keep going down that road? There are special cases, new formulations like nanoparticles or linking them to antibodies, but not where the attention is.
So, if you were setting broad research policy, how should the bets be placed? Not only is there a limit on money, but also on skilled researchers and most importantly on patients. The last group will be the worst served if bad programs and poor compounds crowd out good ones. And in placing bets, how would you combine things?
For example, take targeted therapies. Growing consensus seems to be that targeted therapies will never work as monotherapies. But, you can't have combinations (either with cytotoxics, targeted therapies or I-O) unless you have individual compounds. Cancer genomics efforts are mushrooming; my fellow Blue Hen's "Cancer Moonshot" is certainly due to be scrubbed after this week's constitutional event, but a multitude of companies (such as Foundation Medicine) are making increasing inroads in the cancer space. So that means more targets and more subdivisions of cancer into molecular bins. How much do you invest generating compounds for those spaces or trying to understand the logic that cancer is hinting at by selecting these mutations?
Or perhaps you like an I-O focus, but here the same general questions apply. How many more I-O targets should be pursued? Are personalized cancer vaccines going to work? What combinations should be explored? Again, combinations here can mean I-O compounds, or different types of I-O strategies in combination (such as checkpoint inhibitors with personalized vaccines) or I-O with targeted or I-O with cytotoxics.
Finally, how much do you put on taking really long-range bets. Cancer researchers have often been convinced that major progress is just around the corner; we only need make the big push. The Emperor of All Maladies details this (and much else; if you haven't read it and/or watched it what are you waiting for?). I do think that persons such as Mary Lasker had convinced themselves that one great push would do that job. That was clearly not the case; the disease is far too complex. But humans love to look back, and should we someday discover we've been working on the right path for twenty years it will be natural to ask why we didn't shorten that to ten years. If you know someone with cancer, and I do know someone who is very ill right now, patience is in short supply.
But we know the disease is difficult. If it stayed put it would hard, but cancer evolves in a manner akin to infectious pathogens. Our tools are blunt and our ignorance great. If you were setting the cancer agenda, it takes a lot of courage to insist that the path to a cure two decades from now is to invest in seemingly irrelevant pursuits. But I would hazard a bet that we have not exhausted what yeast and roundworms and fruit flies and all the other magnificent models can tell us about basic cell processes. I am willing to bet there are fundamental biological processes that we are still ignorant of, and certainly amazing biological tricks we can co-opt once we find them.
This is very unusual for a natural science. For a long while I've pointed this out. The core of my introductory college physics book could have been written before the 1900s began. My intro chem book could have been written before WW2, and my organic chem class didn't go much further. But 25 years ago, none of my biology books talked about proteasomes (being discovered), RNAi or CRISPR, and the only paper on cloned mammals was a fraud. Biology is the one fundamental science where the freshman textbooks can be productively re-written for content at least as frequently as once a decade. Those sorts of big leaps don't come from targeted programs, they come from curious individuals spotting surprises and following them up.
So therein lies, in my view, the difficult problem of cancer (or any other) therapeutic area. We have many good options (and many bad ones too). Without an oracle, we can't know which is the best mix, so we must muddle along. I haven't even touched above the split between companies pursuits and public/charity funding. For example, while it can't be avoided altogether, it isn't good if the I-O combos that are tried are determined by which business development folks do and don't get along with each other. Still, knowing we can't be perfect is no excuse for not trying to get it right.
In the interest of disclosure, and because I think it is pretty amazing stuff, my employer has a program targeting KRAS. My role in that program has mostly been foundational; our early genome mining efforts reduced the perceived risk with that strategy. That's a story for another place and time (especially since so little is in verifiable public sources), but since I hold equity in the company I could be perceived as holding a conflict of interest. So I'm declaring that possibility.
From my semi-outsider's perspective, I'd say we can divide the current oncology pharmaceutical world into three categories. I'm fully aware that trying to draw bright lines is often a mistake, particularly in biology. Traditional cytotoxics simply try to kill rapidly-dividing cancer cells faster than they kill the rest of our cells; there is no aspect of specifically targeting cancer cells. Targeted therapies aim at known aspects of tumor biology. Finally, a white hot field right now is immuno-oncology, approaches which enlist the immune system to attack cancer. If you look at both research and industry financing, I think think you'd find not much for cytotoxics and large amounts split between targeted and immuno-oncology. I fully recognize that each of these broad categories I've defined are very, very heterogeneous. For example, I-O includes checkpoint inhibitors, vaccines and engineered T-cells -- and probably a bunch more.
If you were selecting a portfolio of research priorities for cancer, how would you invest? In addition to the three options above, a fourth might be "none of the above". In particular, this option might be to try an indirect route to future therapies by further non-targeted work on basic cellular biology and genetics.
Bruce Booth wrote a nice piece this summer surveying both the excitement in immuno-oncology and the immense challenge. The excitement is because when I-O works, it really works: durable cures. The first problem is that we just don't understand which patients will and will not benefit from existing I-O therapies. Another problem is safety: these therapies are generally well-tolerated, but can make patients initially much sicker, can induce auto-immune diseases and most recently have been found to sometimes have off-tumor affects which can be lethal. A next round question is how to combine I-O agents with each other or with cytotoxics or with targeted therapies; as Booth explained the number of possible combinations far outstrips any reasonable capability to test them.
The other problem in the I-O space, which I've heard a few executives complain about, is that it is so white hot that everybody feels they must be in the game. So compounds are getting touted as I-O drugs that don't really belong there. In other words, there is the real danger of an I-O bubble arising, and like all other bubbles that would mean poor allocation of critical resources and ultimately patients being ill-served.
Targeted therapies have delivered value, but not the durable cures which were long hoped. I knew someone who died from complications of CML a few years before imatinib (Gleevec) was developed; I wish she had lived to get the gains from that drug, even if many patients do not achieve a cure. But too many targeted drugs in monotherapy have led to remissions on the order of a year -- a gift of a year to patients, but not the desired cures.
The logic behind many targeted therapies predate the Human Genome Project (HGP) and Cancer Genome Project (CGP), but the CGP and further cancer genomics efforts have led to a wealth of new oncogene and tumor suppressor candidates. More importantly, in my mind at least, is that cancer genomics has pegged specific genes to specific cancers on a scale far beyond what prior efforts had done. The basis for many of these connections is still a mystery, but it has helped guide us in which compounds should be used on which tumors.
Cytotoxics are largely out of vogue. They are still very important and dominate cancer care and interest in new ones never quite goes extinct, but they definitely aren't favored strategies. We have many indiscriminant poisons that somehow achieve usable results in a subset of tumors; why keep going down that road? There are special cases, new formulations like nanoparticles or linking them to antibodies, but not where the attention is.
So, if you were setting broad research policy, how should the bets be placed? Not only is there a limit on money, but also on skilled researchers and most importantly on patients. The last group will be the worst served if bad programs and poor compounds crowd out good ones. And in placing bets, how would you combine things?
For example, take targeted therapies. Growing consensus seems to be that targeted therapies will never work as monotherapies. But, you can't have combinations (either with cytotoxics, targeted therapies or I-O) unless you have individual compounds. Cancer genomics efforts are mushrooming; my fellow Blue Hen's "Cancer Moonshot" is certainly due to be scrubbed after this week's constitutional event, but a multitude of companies (such as Foundation Medicine) are making increasing inroads in the cancer space. So that means more targets and more subdivisions of cancer into molecular bins. How much do you invest generating compounds for those spaces or trying to understand the logic that cancer is hinting at by selecting these mutations?
Or perhaps you like an I-O focus, but here the same general questions apply. How many more I-O targets should be pursued? Are personalized cancer vaccines going to work? What combinations should be explored? Again, combinations here can mean I-O compounds, or different types of I-O strategies in combination (such as checkpoint inhibitors with personalized vaccines) or I-O with targeted or I-O with cytotoxics.
Finally, how much do you put on taking really long-range bets. Cancer researchers have often been convinced that major progress is just around the corner; we only need make the big push. The Emperor of All Maladies details this (and much else; if you haven't read it and/or watched it what are you waiting for?). I do think that persons such as Mary Lasker had convinced themselves that one great push would do that job. That was clearly not the case; the disease is far too complex. But humans love to look back, and should we someday discover we've been working on the right path for twenty years it will be natural to ask why we didn't shorten that to ten years. If you know someone with cancer, and I do know someone who is very ill right now, patience is in short supply.
But we know the disease is difficult. If it stayed put it would hard, but cancer evolves in a manner akin to infectious pathogens. Our tools are blunt and our ignorance great. If you were setting the cancer agenda, it takes a lot of courage to insist that the path to a cure two decades from now is to invest in seemingly irrelevant pursuits. But I would hazard a bet that we have not exhausted what yeast and roundworms and fruit flies and all the other magnificent models can tell us about basic cell processes. I am willing to bet there are fundamental biological processes that we are still ignorant of, and certainly amazing biological tricks we can co-opt once we find them.
This is very unusual for a natural science. For a long while I've pointed this out. The core of my introductory college physics book could have been written before the 1900s began. My intro chem book could have been written before WW2, and my organic chem class didn't go much further. But 25 years ago, none of my biology books talked about proteasomes (being discovered), RNAi or CRISPR, and the only paper on cloned mammals was a fraud. Biology is the one fundamental science where the freshman textbooks can be productively re-written for content at least as frequently as once a decade. Those sorts of big leaps don't come from targeted programs, they come from curious individuals spotting surprises and following them up.
So therein lies, in my view, the difficult problem of cancer (or any other) therapeutic area. We have many good options (and many bad ones too). Without an oracle, we can't know which is the best mix, so we must muddle along. I haven't even touched above the split between companies pursuits and public/charity funding. For example, while it can't be avoided altogether, it isn't good if the I-O combos that are tried are determined by which business development folks do and don't get along with each other. Still, knowing we can't be perfect is no excuse for not trying to get it right.
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