---
author: TED
date: '2026-02-27'
guest: ''
layout: post.njk
source: https://www.youtube.com/watch?v=aMB8JWgejIw
speaker: TED
tags:
  - ai-research
  - innovation-stifled
  - exploration-exploitation
  - scientific-breakthrough
  - talent-acquisition
title: 竞争如何扼杀AI突破：呼唤探索式研究的复兴
summary: 演讲者 Llion Jones 认为，当前AI领域的巨大成功伴随着空前的竞争压力，这反而导致研究方向的狭窄化，扼杀了创新与突破。他对比了 Transformer 诞生时的有机自由环境与当下研究者面临的“被抢先”恐惧及追求“低垂果实”的诱惑。Jones 强调“探索-利用”权衡，呼吁拥抱原创性、高自主性的探索式研究，并以自然为灵感。他指出，这种环境比金钱更能吸引顶尖人才，并倡导将竞争转向合作，共同加速AI的进步。
insight: ''
draft: true
series: ''
category: ai-ml
area: tech-engineering
project: []
people: []
companies_orgs:
  - OpenAI
products_models:
  - Transformers
  - ChatGPT
media_books: []
status: evergreen
---
### 创新之源：有机生长与自由环境的失落

作为 Transformer 架构的作者之一，我深知其在当前人工智能领域的关键作用，它是 ChatGPT 的核心驱动力，支撑着绝大多数前沿 AI 技术。回溯 Transformer 的研发历程，那是一段极为有机、自下而上的项目时光。想法源于午餐时的交流，或是办公室白板上的随意涂鸦。更重要的是，当我们认为有了好点子时，我们拥有充足的自由去投入时间和精力去实现它。管理层没有任何压力，无论是要求我们必须攻克某个特定项目、发表多少论文，还是达成某个量化指标。我希望大家心中能浮现出这样的画面：正是这种环境，孕育了 Transformer 的诞生——有机、开放且充满自由，允许我们追寻那些我们认为有趣且重要的想法。然而，我深切担忧的是，当前的人工智能行业恰恰缺乏这样的环境。接下来，我将探讨为何如此，以及我们能做些什么。

当前人工智能研究乃至整个行业面临着一个核心悖论：尽管前所未有的兴趣、资源、资金和人才涌入，这反而导致了我们研究方向的日益狭窄。在我看来，原因显而易见：随之而来的巨大压力。这种压力来自寻求投资回报的投资者，也来自个体层面——这个行业已过度拥挤，脱颖而出异常艰难。研究人员正切实体会到这种压力。假设你正在进行一项标准的人工智能研究，你几乎可以肯定会有三到四个其他团队在做非常相似甚至完全相同的事情。因此，你不得不花费大量时间去确认自己是否已被“抢先”（scooped），是否已有他人在你之前发布了你的想法。即使在学术界，本应享有更多自由的象牙塔里，也存在着发表论文的压力。面对一个可能产生有趣成果的绝妙想法，和一个可能只带来一篇普通论文的平庸想法，研究者往往会屈从于诱惑，选择“低垂的果实”。不幸的是，这种压力损害了科学本身，人们急于发表论文，却牺牲了创造力。

<details><summary>Original English</summary>
So, as mentioned,
I'm probably most well-known
as one of the transformers authors.
Transformers are, of course,
the T in ChatGPT,
and are the architectures that run
most of the state-of-the-art
artificial intelligence.
If I think back to that time
when we were working
on the transformers,
I remember it as a very organic,
bottom-up kind of project,
where the idea came
from talking over lunch
or scribbling randomly
on the whiteboards in the office.
And importantly, when we felt
like we did actually have a good idea,
we had the freedom
to actually spend the time
and go and work on it.
And even more importantly,
we didn't have any pressure
that was coming down from management.
No pressure to work
on any particular project,
publish a number of papers,
to push a certain number up.
So that's the image I want you
to have in your mind, right?
That is the kind of environment
that allowed the transformer
to come into existence.
An organic, open-ended
and with a lot of freedom
to pursue the ideas
that we thought
were interesting and important.
And my deep concern
is that right now in the AI industry,
we do not have this kind of environment.
And I want to talk about why not
and what can we do about it.
So the main paradox that I see
in artificial intelligence research,
or the industry in general right now,
is that despite the fact
that there's never been so much interest
and resources and money and talent,
this has somehow caused a narrowing
of the research that we're doing.
And to me, I think
the reason is fairly obvious.
It's because the immense amount
of pressure that comes with that, right?
Pressure from investors
that are going to ask
for a return on their investment
and pressure that comes from individuals,
because this is such
an overcrowded industry right now,
where it is very difficult to stand out.
And the researchers are really
feeling this pressure, right?
If you're doing, let's say,
standard AI research right now,
you kind of have to assume
that there's maybe
three or four other groups
doing something very similar
or maybe exactly the same.
So you have to spend the time
checking to see if you've been scooped,
to see if someone else
has put your idea out there.
And even in academia,
where you would hope
you would have more freedom,
there's pressure to publish, right,
and to have your papers published.
So if you have an interesting idea
that could create
something very interesting,
or you have kind of a mediocre idea
that it'll probably get a paper
and probably get accepted,
the temptation is to go
for the low-hanging fruit.
So unfortunately,
this pressure damages the science,
because people are rushing out papers,
and it's reducing the amount
of creativity that we have.
</details>

### 探索困境与历史的警示

为了更好地理解当前困境，我们可以借鉴人工智能自身的设计原理。在设计 AI 搜索算法时，我们必须权衡一个叫做“探索-利用”（exploration-exploitation）的取舍。当你寻找解决方案时，你可以选择投入时间去“探索”未知领域，或者去“利用”已知最优解。如果将所有时间都用于探索，你可能会发现大量新颖的解决方案。但如果只是一味地利用，你可能会错失其他更优的、可以被更好地利用和改进的替代方案。我们几乎可以肯定，当前的人工智能行业正处于这种“过度利用”的境地。因此，我今天真正想请大家思考的是，能否稍微调整一下这种平衡，加大“探索”的力度？

我清晰地记得 Transformer 出现之前的时代。那时，我的主要印象是涌现出大量论文，它们总是对当时的主流架构——循环神经网络（Recurrent Neural Networks, RNNs）进行各种排列组合式的改进，尝试不同的门控机制、不同的层结构，但大多只带来边际效益的提升。而 Transformer 问世后，那些用于改进 RNN 的工作，在某种程度上显得有些徒劳。或许这样说有些过于严厉，但请设想一下：如果那些研究者知道 Transformer 就在不远处，他们还会投入那么多时间去改进 RNN 吗？事实证明，我们需要的是一次更长远的观念飞跃，需要彻底抛弃循环机制。我再次担忧，我们正处于类似的情境：过度专注于一种架构，对其进行微调和各种尝试，而真正的突破可能就在拐角处。如果突破确实存在，我们就应该像迎接它一样去行动。下一次的重大突破，几乎可以肯定，将源于这种开放式、更具投机性的研究。而规避错过下一个重大事件的唯一方法，就是投资于这类研究。

<details><summary>Original English</summary>
So I want to take an analogy
from AI itself.
So when we're designing
AI search algorithms,
we have to trade off something called
the exploration-exploitation trade off.
When you're searching for a solution,
you can either spend your time
exploring or exploiting.
If you spend all your time exploring,
then you will probably only find
a large number of medical solutions.
If you spend your time just exploiting,
then you might lose out
on finding other alternative solutions
that you might be able
to exploit better and improve better.
And we are almost certainly
in that situation right now
in the AI industry.
So all I really want to ask you today
is to consider just changing
that balance a little bit, right?
Just turning up the dial
and exploring more.
So I actually remember what it was like
just before the transformers,
and I want to paint that picture
for you as well.
Back then, my main memory was
there were a lot of papers coming out,
and they were always permutating
the current architecture,
which was recurrent
neural networks at the time,
just endlessly trying different things,
different gates, different layers,
mostly for incremental gains.
And then after the transformer came out,
all of that work that was spent
on improving the recurrent neural network
kind of felt a bit pointless.
Maybe that's a bit too harsh,
but think of it like this.
How much time do you think
those researchers would have spent
trying to improve
the recurrent neural network
if they knew something like transformers
was around the corner, right?
It turned out we needed
a longer conceptual leap.
We needed to throw away
recurrence completely.
And again, I am worried
that we're in that situation right now
where we're just concentrating
on one architecture
and just permuting it
and trying different things
where there might be a breakthrough
just around the corner.
And if there is, then
we should be acting like it.
The next breakthrough,
almost by definition,
has to come from this sort of open-ended,
much more speculative research, right?
And the only way to really hedge your bets
against missing out on the next big thing
is to invest in this kind of research.
</details>

### 孕育突破：灵感、自主与协作

如果我只是在此抱怨现状，那这场演讲将毫无价值。因此，我想提出几点建议。首先，在我所在的**OpenAI**公司，我们倡导“受自然启发”（nature-inspired）的研究。人类大脑仍有许多当前最先进的 AI 无法企及的能力，或许从中汲取灵感，能帮助我们获得这些特质。当然，这带有我个人的偏见。更普适的原则是：你应该追随那些让你自己感到好奇和兴奋的方向。我两周前听到的一句话非常契合我的观点：“**你应该只做那些如果不是你在做，就不会发生的研究**”（You should only do research that wouldn’t happen if you weren’t working on it）。这句话完美地概括了核心思想。如果我们都能遵循这一点，就不会互相踩踏，研究探索的效率也会大大提高。

我举一个具体的例子：我们近期发表了一项名为“**连续思想机**”（Continuous Thought Machine）的研究。我们只是从自然界汲取了一点灵感。在人脑中，同步化（synchronization）至关重要。我们尝试将这种同步化机制引入人工神经网络。我记得当时一位员工带着这个想法来找我，我告诉他：“好的，先做一周看看效果。”后来他告诉我，在他之前的公司或学术职位上，他很可能会因为这个想法受到质疑，被告知是在浪费时间。但经过那一周的探索，他发现了该模型更多有趣的特性，这个项目最终获得了成功，并在今年的 NeurIPS 会议上获得了**Spotlight**奖项。我认为这有几个原因：一是市场对这种新颖、差异化的研究存在渴求；二是更有趣的是，在整个项目过程中，我们从未担心过“被抢先”的问题。这使我们能够从容地进行科学研究，并运行我们想要的基准测试。我认为这才是我们应该追求的研究模式。

希望我的阐述能表明，我并非只是在做一场“听起来不错”的演讲。我真心相信这一点，并且正在身体力行。我正在努力创造那种允许 Transformer 诞生的环境。我不太确定是否应该透露这一点，因为它确实是公司目前的一个优势，但它是一种非常、非常有效的吸引人才的方式。仔细想想：有才华、聪明、有抱负的人，自然会寻求这种高自主性的环境。我们近期一些最优秀的招聘，正是因为这个原因。而且，这种环境比单纯的金钱更能奏效。想想那些年薪百万的“超级明星”，他们开始新职位时，真的感到有能力去尝试那些疯狂、更具投机性的想法吗？还是他们会感受到巨大的压力，急于证明自己，从而再次选择“低垂的果实”？

我认为还有另一个原因，可能导致我们探索的效率不如预期，那就是 Transformer 本身“太好用了”。我知道，这听起来有点自大（笑）。但说真的，我的意思是，当我们回望 AI 历史的这个节点时，可能会发现，正是因为当前技术如此强大和灵活，它反而阻止了我们去寻找更好的东西。这很合理，不是吗？如果当前技术更糟糕，就会有更多人去寻找更好的替代品。

在此，我想澄清两点。首先，我并非认为当前没有大量有趣的研究在进行。我只是说，鉴于我们目前拥有的才华和资源，我们完全有能力做得更多。我和许多其他研究者都相信，我们尚未完成探索，应该继续寻找更好的方法。其次，我也不是说应该抛弃现有技术。不，在当前技术上仍有大量重要的研究有待进行，并且将在未来几年带来巨大价值。我个人在今年年初就已决定，将大幅减少在 Transformer 上的投入。我正明确地转向探索和寻找下一个突破点。听到一位 Transformer 的作者站在这里说他“厌倦了它们”，这或许有些争议，但也是情理之中。毕竟，我投入其中的时间比任何人都长，可能除了另外七个人。

那么，我们足够大胆吗？研究者们，你们是否足够大胆，愿意花更多时间在那些你认为重要且有趣的想法上？管理者们，你们是否足够大胆，给予研究者更多自由去追寻这些想法？企业领袖们，你们是否足够大胆，去创建那些能让管理者感到有能力给予研究者自由的企业环境？投资者们，你们是否足够大胆，去投资那些在我看来，将孕育下一次重大突破的企业？

最后，我想说，正如我之前提到的，很多压力来自于竞争——公司之间、产品之间、研究者之间，为了同一个想法而争夺。但从我的视角来看，这并非真正的竞争。我们拥有共同的目标：希望这项技术臻于完善，以便我们都能从中受益。因此，如果我们能集体地调高“探索”的旋钮，并公开分享我们的发现，我们就能更快地达成共同的目标。谢谢大家。（掌声）

<details><summary>Original English</summary>
So if I came up here and did nothing
but just moan about the current situation,
I don't think it would be a great talk.
So I want to give you
a couple of suggestions.
First of all,
in my company, we champion
having nature-inspired.
So there are still things,
plenty of things
that the human brain can do,
that current state-of-the-art AI can't do.
So maybe if we take
some inspiration from nature,
we can get some of those properties.
But that's kind of my bias.
You should follow
what's interesting to you?
There's actually a quote I heard
two weeks ago and I thought,
that's perfect,
I'm having that for my talk.
And I think I'm stealing it
from a guy called Brian Chung.
And it goes like this.
“You should only do research
that wouldn’t happen
if you weren’t working on it.”
And I think that captures it perfectly.
And if we all did that,
we wouldn’t be stepping
on each other’s toes,
and we'd be exploring
much more efficiently.
So I want to give you a concrete example.
There's a piece of research
that we put out recently
called the Continuous Thought Machine.
And all we did is we just took
a little bit of inspiration from nature.
So in the human brain,
synchronization is very important.
And we try to add
this kind of synchronization
into artificial neural networks.
I remember the employee
coming to me with the idea
and I said,
OK, work on it for a week,
and we’ll see what happens.
That employee later confided in me
that in his previous employment,
or even in his academic
position before that,
that he probably would have gotten
skepticism and told not to waste his time.
But after that week,
he started to find much more
interesting properties of this model.
And the project became a success.
We actually announced that we got
a spotlight at NeurIPS this year.
And I think there's a couple
of reasons for that.
I think there's a hunger for this kind
of new and differentiated research,
and more interestingly,
at no point, when we were
working on this project,
did we have to worry about being scooped.
So we could take our time, right,
to do the science properly
and run the benchmarks
that we wanted to run.
And I think that's the kind
of research we should be doing.
So hopefully, from that you can tell
that I'm not just up here
trying to make a talk that sounds good.
I actually believe this, right?
I am putting my money where my mouth is,
and I am creating this kind
of environment,
the kind of environment
that allow transformers
to come into existence at my company.
I'm not sure if I should tell you this,
because it's a bit of an advantage
that the company has right now,
but it's a really,
really good way of getting talent.
Think about it.
Talented, intelligent people,
ambitious people,
will naturally seek out
this kind of environment
with high autonomy.
And some of our best hires recently
have been explicitly
because of this reason.
And by the way,
it works better than just money.
Think about it.
These superstars that are
apparently being snapped up
for literally a million dollars
a year in some cases,
do you think that when
they start their new position,
they feel empowered
to try their mad ideas,
their more speculative ideas?
Or do they feel immense pressure
to prove their worth
and will once again go
for the low-hanging fruit?
So there's another reason, I think,
that maybe we're not exploring
quite as efficiently as we should be.
And that's because
transformers are too good.
I know, modesty.
(Laughter)
But seriously, I mean,
what can I mean by that?
What I mean is, I think
the punchline is going to be
that when we look back
at this point in AI history,
the fact that the current technology
is so powerful and flexible
that it stopped us
from looking for better.
It makes sense, right?
If the current technology was worse,
more people would be looking for better.
So there's two points
I would like to clarify.
First of all,
I'm not saying that there isn't already
plenty of very interesting
research happening.
I'm just saying that given the amount
of talent and resources
that we have currently,
we can afford to do a lot more, right?
I and several other,
many other researchers
believe we're not done
and we should be looking for better.
But I'm also not saying that we should
throw away the current technology.
No, there's still plenty
of very important research to be done
on the current technology
and will bring a lot of value
in the coming years.
I personally made the decision
at the beginning of this year
that I'm going to drastically reduce
the amount of time
that I spend on transformers.
I'm explicitly now exploring
and looking for the next thing.
Now it might sound
a little controversial, maybe,
to hear one of the transformers
authors stand on stage
and tell you that he's
absolutely sick of them,
but it's kind of fair enough, right?
I've been working on them
longer than anyone,
with the possible exception
of seven other people.
So ...
Are we bold enough?
Researchers,
are you bold enough
to spend more time on the ideas
that you think are important
and interesting?
Managers.
Are you bold enough
to give the researchers some more freedom
to pursue these ideas?
Business leaders.
Are you bold enough to create businesses
that create these kind of environments
that will allow the managers
to feel like they can afford
to give the freedom to their researchers?
And investors.
Are you bold enough
to invest in these kind of businesses,
where, in my opinion,
these are the kind of businesses
is where the next breakthrough
is going to come from.
And I will leave you with this.
A lot of the pressure, like I said,
comes from competition, right?
Competition between companies,
between products,
between researchers,
fighting over the same idea.
But genuinely, from my perspective,
this is not a competition.
We all have the same goal.
We all want to see
this technology perfected
so that we can all benefit from it.
So if we can all, collectively,
turn up the explore dial
and then openly share what we find,
we can get to our goal
much faster.
Thank you.
(Applause)
</details>