Unfortunately this post does not give me much confidence that YC will replicate its success in biotech. To illustrate why I’m just going to focus on the first example they give, Shasqi, because coincidentally this is the type of idea I and my colleagues would regularly propose to each other and play “find the flaw.”

In this case, this falls into the bin of, “are you absolutely sure this is the reason why cancer therapies fail?” Localized drug delivery sounds great in paper, but to my knowledge and what I’ve learned talking to people who know more than me, its not the most important issue - its actually hard to even be absolutely sure that the effects of chemical chemotherapy are fully explained by tumor-local effects (there’s a huge immune system component to it), so its efficacy compared to real chemotherapy is hard to predict.

Their publication also reads like one of tens of thousands of similar papers and approaches that often get published in the hundreds or thousands of journals. The paper is not bad at all, its a good proof of concept of the _chemistry_ and the fact that it does at least something inside a living organism (as opposed to chemical methods and derivatives that are not even biocompatible), but it does not convince me a bit that this is actually a worthwhile method to think about.

While there are numerous issues that lead to it, the most important is the fact that this (and virtually every other) paper that tries to show efficacy in cancer therapy uses xenograft mouse models to show it; this is where you take mice which have most of their immune system knocked out and inject HUMAN cancer cells (that have been cultured in petridishes for decades) to make a tumor and then try out various drugs to see which cures the tumor. Why do we need to use immune-compromised mice? Because otherwise the mouse’s own immune system will recognize any cell that did’t originate from its own body as foreign and quickly kill it. So now, we have a system where this drug-modification is compared to its baseline (which as I mentioned above, is probably going to need a viable immune system to function as it does in a real patient) in a system that inherently stifles it. So even if it shows to be better in a wildly artificial model, it says nothing about its efficacy in a human. I’ll go out on a limb and say that there’s actually enough evidence in their papers that this will never be better than regular chemo in a human (will be glad to go into detail if anyone’s interested) but even otherwise there’s not enough info available to say that this will work in humans.

While that might have been more detailed than some might like, the point is that I’d personally not even consider myself an “expert” in cancer therapy; I merely did a PhD in a lab that used to do some stuff related to it. But I can already see so many red flags in this single effort (I’ve seen similar reflags, wherever I knew some stuff, in other YC funded companies too). So, at least for therapeutic areas, I’m still not convinced that optimistic outlooks towards such projects is a good thing.

Of course, just saying you shouldn’t be optimistic with biotech projects is not enough, and I’ve struggled till now to put it in reasonable words why biotech (especially therapeutic) is different from technology companies and projects. But this article solidified it in my head and I boil it down to two points:

1. In tech, when you show a proof of concept for a product, you have essentially created the final product in the final environment as its going to be used by at least some users. Almost always, the main things you need to figure out are how you can “scale” it, and how you can make it appeal to a wider audience; but the premise of the product is proven with the prototype. With biology however, the premise is most definitely not proven with anything short of a phase II clinical trial. Almost all animal models (or anything in a lab dish) are significantly different from humans in ways that are fundamentally important for the mechanisms of action for these drugs. The only way to be absolutely sure that a drug has a really good chance of working in a human being is to inject it into a human with that disease and see if they die. So no matter how fancy the xenograft model or what caliber the nature publication might be, its still at best comparable to a deck of powerpoint slides in the tech VC pitch analogy and not anything comparable to a real prototype.

2. In tech, its a reasonable assumption that you can build more or less anything as functionality in an app/website, as long as it makes reasonable physical sense, because many engineers can have a fully comprehensive mental model of what is and is not physically and computationally possible inside computers. In biology its not at all a good assumption that if it makes sense in your head, then it will work in a human being, because no single person (not even a mythical House MD) has a full mental model of what we currently understand about all our biological systems. Our systems are too complicated and intricate (and without an organized creator) to keep in head by anyone, so its really hard to predict what will fail and cause a problem with our hypothesis. To some extent, every biotech project we do, even as an expert, is akin to someone who has barely used a smartphone coming up with an app idea - of course once in a while its going to make sense and be brilliant, but most of the time they have no idea how technology works in the backend and hence cannot say what is and is not possible.

Given these fundamental differences between biotech and tech, I’m going to remain skeptical until someone tells how they have figured out a solution to them.