The Apollo program occupies a very special place in my psyche. I get a thrill out of watching recordings of President Kennedy giving the call to arms ("we choose to do this and the other things, not because they are easy, but because they are hard"), almost as big as the thrill of watching footage of a Saturn V taking off. Some of my first memories are of watching astronauts on one of the last missions (I was mystified how the rover could fit in the lunar lander). It irks me that nobody who was there can tell me if I was in front of the TV set for Neil Armstrong's historic steps, let alone whether my year-old self was awake or asleep. I had a toy model of the Saturn V (in an inaccurate red, white and blue; I was thrilled when I found an accurately colored one for TNG), which I ran through the mission sequence into destruction. I later built moon rockets from Legos, lamenting their angular cross-section.
I also a high opinion of Bill Gates and his foundation, much better than my tolerate/hate relationship products of the company he launched (full disclosure: I've been a paid consultant a few times for the Gates Foundation, reviewing proposals). Gates and company have taken on difficult problems in developing nations which market-driven first world economies tend to ignore.
And it certainly isn't that I don't take seriously the urgency of the problem. Sadly, I know a number of members of the previous generation who suffer from progressive dementias, and I've lost one family member already. I periodically spend time with one individual who rarely forms new memories (I wish I could crack the secret as to the memories that are formed); over the course of a weekend there are many cycles through a small set of questions, sometimes with only a few minutes between repetitions. Another individual I knew no longer sees anyone but the closest of family; the disease has robbed him of his gentle and generous personality. Alzheimer's and similar diseases are a scourge.
But it isn't some misguided hero worship of Apollo or annoyance with Microsoft that drives my frustration, but rather with the whole idea of moonshots in clinical medicine. There are two fundamental problems with this entire mentality.
The first is the one which is frequently leveled (Derek Lowe has deployed it often): there is a huge difference between science and engineering. Apollo was an engineering program, not a science one (though it yielded important science). Actually, the engineering was largely in Gemini. Look through the Gemini program, and each mission tested out a key set of technologies needed for the moon mission. Space walks, orbital rendezvous and docking, using tools in low gravity, restarting a rocket motor in space, living 2 weeks in low gravity and tight quarters -- and many more. Mistakes were made along the way; the first spacewalk nearly ended in disaster when Ed White's spacesuit wouldn't fit easily back through the hatch; Alexey Leonov had experienced a similar phenomenon on the first ever spacewalk but Cold War politics kept that a secret. The first efforts to work on spacewalks highlighted Newton's laws of motion and the need for foot grips and handholds.
Note that nowhere there did I describe experiments asking whether it was possible to use rocket propulsion to move through space. A few scientists seriously suggested that the lunar surface was deep powder which might swallow a lander, which was disproved by the soft landing Surveyors. But for the most part, the body of information then available suggested that a moon landing was scientifically feasibly, requiring an acceleration of technologies already in development and the working out of techniques. You've heard of many technologies that are attributed to Apollo; the vast majority were accelerated or used heavily, but few were actually created by Apollo. Gates follows in this lamentable tradition as well, crediting the moon project with communication satellites and weather satellites. Reality: the first communication ( Echo ) and weather (TIROS-1) satellites flew before Kennedy was even elected.
There's good reason for that: time. Kennedy gave his speech in September 1962; the first Saturn V would fly just five years later. That's not a lot of time to design a very complicated machine, even if you know all the relevant science. If truly fundamental questions as to the science of how to build the booster existed, it would have been a hopeless task.
I don't have a strong knowledge of the neurodegenerative field, but what I do have fills me with gloom. Trial after trial of drugs targeting the amyloid hypothesis have failed. We've learned much about neurons and the brain, but we're far from a confident understanding of the fundamental pathogenic mechanisms. Even if we did, there's the whole challenge of finding druggable targets, and then those drugs need to get across the brain. And what if the window of opportunity for treatment is before symptoms are apparent? Are the animal models any good?
Just imagine if Kennedy had met with von Braun (and yes, his involvement is a permanent stain on the program) and the rocket scientist had said: "we think there's a limited number of spots on the moon that can support a landing, but we don't know where they are -- nor are we confident we can find them. Even if we can find them, there's this barrier that would keep most lander designs out, particularly ones that could land on those spots."
But there's an even greater yet simpler reason why smart people need to stop sticking these silly moonshot labels. It's really easy to understand in cancer. In cancer, the standard for considering a patient cured is five year survival. Showing tumor shrinkage or improved quality of life isn't sufficient; cures require survival. Surrogate endpoints are useful for early evaluations, but there are more than a few examples of trials which show a delay in progression, but no improvement in survival. So you want to end cancer in a decade? You don't have ten years to come up with a plan; you have five so the other five can prove you right. Furthermore, this isn't NASA which can launch rockets at will - and blow up the ones that go astray. You're going to need to test your solution in a series of patient populations of increasing size, demonstrating safety and efficacy and learning an appropriate dosing scheme.
There's two fundamental negative effects of these moonshots. First, they unnecessarily raise public hopes - and engender renewed cynicism when they predictably fail to deliver their unrealistic goals. But second, they further shift scientific resources, such as funding, away from basic research.
Cas9/CRISPR is one of the most exciting technologies in biotechnology right now, accelerating a wide range of techniques and offering new possibilities for repairing broken genes in patients. Did Cas9 come from some targeted effort? No, it fell out of sequencing bacteria. PCR was enabled by someone's curiosity of what bacteria might grow near a geyser. Illumina and Pacific Biosciences sequencing technologies rely on decades-ago curiosity of how do cells replicate their DNA. Immunotherapy, one of the most exciting advances in cancer therapy, required decades of teasing apart the intricacies of the immune system.
I'm impatient too for cures, but while determination can accelerate a project with a clear path forward, determination can sometimes mask haste, with disastrous consequences. Neil Armstrong could have easily been lost in space when his Gemini craft went into an uncontrollable roll during a docking; he was also nearly killed by the bizarre lunar lander simulator craft. Worse, White along with Gus Grissom and Roger Chaffee were killed in the Apollo I fire, a tragedy which can be traced to both poor design decisions but also shoddy, rushed construction. In the clinical world, rushing can kill patients. Prudent Phase I trials often mean slowly adding patients and slowly escalating doses.
But it isn't sexy to say we need to invest now for payoffs a few decades out. It isn't headline grabbing to admit that clinical science resembles more a snail-pace trudge through deep, sucking mud than an Usain Bolt sprint for the finish on a pristine indoor track. We certainly need to constantly search for prudent ways to speed trials by better patient recruitment and selection and speeding the proper collection, verification and analysis of data. But equally investments must be continued to be made in very basic biology, such as nailing down the functions of proteins and exploring organisms which have never been models. Invest in simply exploring key pathways, such as autophagy cited by the Nobel Foundation this week, without trying to chart a direct course to a cure. And so much more.
But don't make empty promises of cures in the next decade, or even the decade after that. The problem isn't some magical lack of verve, it's a lack of knowledge. Eureka just can't be scheduled.