新药研发和角色扮演游戏《龙与地下城》有些相似之处
但是作者发现新药和角色扮演游戏《龙与地下城》有些相似之处。现在新药研发有两个学派。一个是所谓的“pick the winners” ，即选择了一个方向就坚定不移，无论怎么困难都不放弃直到成功为止。另一派就是作者这一派，所谓 “kill the losers”，即同时选择多个方向，随着数据的采集停止那些希望较小的项目然后集中精力开发希望较大的项目。因为这是作为新药研发的战略选择，咱也就用战争做个对比。Pick the winners相当于集团军作战，司令部说2天之内攻下0号高地，不管敌人炮火如何猛烈你也得前进。Kill the losers相当于游击战。敌进我退，敌退我进，专挑软柿子捏。
David Grainger是Kill the losers战略的极力倡导者。他的主要根据是一个项目开始的时候几乎永远不会有足够的信息让你能选择一个胜率较大的方向。这基本是被新药研发的历史所证实的事实，不管项目如何吸引人绝大多数项目还是以失败告终。所以同时开始多个方向，随着数据的增加逐渐评估每个项目的可行性，这比一开始就定下主攻方向更高效。
但是也有很多人支持pick the winners策略，理由是不管什么项目如果遇到困难就停止也不可能最后成功。这也被新药研发的历史所证实。几乎所有的首创药物都在开发过程中有过差点被终止的经历，你要是严格遵循Kill the losers策略那这些药物很可能上不了市。事实上几乎可以肯定有些被终止的项目如果坚持是可以上市的。
那到底哪个策略更高效呢？和任何复杂问题一样，正确的答案是it depends，或者叫具体情况具体分析。打个通俗的比方，对于首个想登珠穆朗玛峰的人他可以试着从不同路径登上，但是如果遇到险情就换路线的话估计永远也上不了山顶。但如果不管什么险情也不改变路线估计也只能牺牲在路上。
但什么时候放弃什么情况坚持呢？这显然是个个人选择问题。小的生物制药公司一旦开始一个项目基本就得像过河卒子，没有该换项目的余地。而大企业则可以随时评估项目可行性，所以可以kill the losers。当然这不等于大药厂都轻易停止一个项目，比如礼来就以敢于冒险和坚持不懈名扬于江湖。去年Nature Biotechnology有一篇文章分析800多个制药公司的研发效率，显示小公司作为一个群体效率更高，表面上似乎说明pick the winners在目前的科技水平下更有效，但是因为小公司经常财力有限，一个失败的临床实验就可以令其破产，所以失败的小公司可能比大公司终止的项目还多。所以这个数据可能更支持Kill the losers策略。
今年8月Nature review drug discovery有一篇分析发现新药研发假阳性在15-35%之间，假阴性在5-15%之间效率最高，作者预测这个搭配比现在普遍接受的5%/20%的行业标准组合成本能下降6-7%。这个数据说明制药工业已经过多过早地终止了研发项目，似乎又在支持pick the winners策略。我个人认为新药研发在战略上应该多元化而在战术上要坚韧不拔，当然一切都是在资源的限制之下。
源地址：http://www.forbes.com/sites/davi ... the-dungeon-master/
D&D On R&D - Lessons For Pharma From The Dungeon Master
The discovery and early development phases of pharmaceutical R&D are notoriously challenging. Success (even marked by regulatory approval, let alone meaningful sales) is a distant vision. The cost of prosecuting each project is high, and rises very rapidly as development progresses, yet the vast majority of projects – no matter how compelling initially – eventually fail.
Faced with such challenges, there is little wonder R&D productivity is so low, with each new approval costing the industry something in the region of $2billion (estimated by dividing global annual R&D spend by average annual drug approvals). It also makes selecing the optimal strategy for managing an early R&D portfolio critical, if you are going to play such a high-stakes game at all.
Unfortunately, there are few (if indeed any) other business processes to guide our strategy – certainly none with parameters so extreme. Innovation in other technologies, such as IT, may fail as frequently but typically take neither as much time nor capital to prosecute before reliable indicators of eventual success begin to mount.
Inspiration, therefore, must come from a different source.
Dungeons and Dragons (or D&D), it turns out, is an excellent model for early R&D in the pharmaceutical industry. Winning strategies for wizards and warriors are, consequently, useful guides for R&D chiefs whether in global pharma companies or virtual biotechs.
Struggling to see the parallels? Read on.
A party of doughty adventurers awake to find themselves in a prison cell somewher in the middle of a maze-like dungeon. Stripped of their possessions by their captors, they have only one goal that counts for anything: escaping alive. Right now, though, locked in a cell that seems a distant prospect (much like approval of a preclinical drug candidate).
There are, however, intermediate goals that, while having little value in of themselves, nevertheless increase the likelihood of eventual success. Getting out of the cell, finding food, armour and weapons and staying alive while exploring the dungeon in search of the exit are essential pre-requisites for eventual escape.
As with drug R&D, there are many plausible paths to take, and (at least initially) very little information to guide the selecion of one way over another. Yet the options available at each step are completely dependent on all the steps taken up until that point. You will only find the magical armour in the locked chest if you initially went east – west lies the dragon!
While seeking the correct sequence of actions to secure escape, the party of adventurers has a strictly limited amount of resources – torches, food and stamina, for example. The game then rides upon finding a winning combination before time runs out, using imperfect information at every step.
That is a perfect model for drug development. Both are represented by a sequence of decisions based on very little information, to deliver a distant goal when the intermediate milestones have very little value, and to do so before the available resources have been exhausted.
What sort of strategy is likely to be successful?
One approach is to pick the most likely direction for escape, based on virtually no information, and then go after that even if you need to break down the walls with a pick-axe…
… or, being big pharma, with the most resource-intensive machinery on the planet
But if the original direction was wrong, even after enormous effort the attempt will end in failure.
One option is to commit the available resources to one particular solution. Let’s call that “pick the winners”. Our adventurers look out the door, and decide it looks lighter and brighter to the west – so they commit every ounce of their effort to going west, no matter what. If going west turns out to be the right direction, they are going to be successful. But, of course, making such a decision on so little information means that, more often than not, its entirely the wrong direction.
The alternative is to split up and try several possible routes, conserving the resources until the moment when it’s much clearer which direction looks the most promising. The key to success with this strategy is to gain information about the eventual way out in as many ways as possible, using as little as possible of the stockpile of torches, food and stamina.
If one direction looks unpromising because there is a dragon in the way, selec an alternative path
Even if an unpromising path (such as a staircase down) DOES eventually lead to the exit, it may be the wrong choice if torches and food will run out before you get there
As the adventurers start to open doors, some of them will look decidedly unpromising. The first door reveals a dragon, perhaps. The second a spiral staircase going deep into the bowels of the earth. Its important to remember that either of these routes might still be the way out. The exit door might be behind the dragon. The path out might involve going down to the deepest dungeon and then back up again somehow.
But they are still the wrong routes to take, if the party judges they have insufficient resources to complete either journey. If the dragon kills you, or you run out of torches before you re-surface, you have lost no matter which is the “correct” way out.
If you pick the direction too early (based on very little information) and its the wrong direction you will expend all your resources but never make it to the exit
Our adventurers, then, rightly “kill the losers”. They eliminate from play the unpromising alternatives, and devote the resources to the remaining options. Gradually, over time, they are left with only a few plausible options – and the best possible chance that one of them leads them to safety before the lights go out.
The pharmaceutical industry faces exactly these same strategic options.
Even expensive consultants have recommended “pick the winners” as a strategy. Arguing that there is insufficient resources to pursue every possible project, the sensible approach – they claim – is to selec the most promising and focus the limited resources (money and talented people) on those.
Such a strategy makes sense, though, only if there is enough information to reliably identify the winners. Focusing resources early (like committing to a direction of travel to escape the dungeon, no matter what) works if you are right about the chosen target. But early in drug discovery and development there is rarely anything like enough data to justify such a decision.
Instead, R&D managers need to focus on killing the least promising projects and keeping as broad a range of irons in the fire as possible. Doing so requires an incessant focus on keeping the cost per project as low as possible, allowing as many of these “not dead yet” options to be pursued to the next level.
As with the intrepid adventurers, some of the projects that were eliminated might, in the end, have yielded a positive outcome. But the same arguments apply: the cost of finding out if an unpromising option really is a winner can be so high that it renders the entire drug discovery and development activity uneconomic. Each failure that is pursued almost to the end of the road drains so much resource from the system that hundreds of promising, earlier stage, projects are denied their moment in the sun as a consequence.
The lessons for pharma R&D managers from D&D are, therefore, practical and actionable. Faced with demands to lower the overall R&D budget, do not cut the number of projects (which is what the “pick the winners” strategy demands); instead cut the cost per project by ensuring only the data critical for the next “kill or continue” decision is generated.
This way, you are ruthlessly filtering out projects on the basis of the information you decided in advance was the most important to inform the decision.
“Picking the winners” is inherently more attractive to the human psyche: after all, it derives success from being clever at picking the right projects. By contrast, a “kill the losers” strategy looks dangerously close to random, keeping everything going and carrying the implicit message from the R&D leaders that “we are not clever enough” to pick the best projects.
No-one likes to admit they are not smart enough to pick the winners. But when there is insufficient information available to make that call, there is surely no stigma to remaining humble. After all, like the warriors and wizards who only survive to fight another day if they make it out of the dungeon, the very existence of pharma R&D is under threat unless productivity improves dramatically over the coming years. And after more than a decade of steep declines in productivity, hubris among R&D leaders hardly seems justified. It may not be the meek who inherit the earth, but it will likely be the humble.
This piece is based on the Opening Address I delivered at the 10th Index Forum, held in Rome, Italy, in August 2014. The annual Index Forum is an invitation-only gathering of about 100 senior leaders from the global pharmaceutical, biotech and life science venture capital industries. Cartoons by Dice Design
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