[MURG] x prize write up

[Joseph J. Strout]

At 7:39 PM -0400 10/11/04, Eric Zilli wrote:

>But unlike those that you mention, we like to believe mind uploading
>is possible--and it would make a good headline (if you can find a way
>to concisely describe it).

Oh yes, it's certainly possible -- but not within 10-20 years.

>I imagine you're saying this by analogy with, for instance,
>nanotechnology which was initially greeted quite coldly and has only
>recently taken off. I think the delay between introduction of an idea
>and acceptance of it will always occur though: had Drexler waited 15
>years to publish his work, my guess is there still would have been a
>good decade or so before people started to really take the idea
>seriously. If that's so, introducing mind uploading as early as
>possible would be for the best, as the period of unacceptance would
>end that much faster.

Ah, but introduce *how*?  Drexler introduced it by writing a 
nontechnical speculative book (Engines of Creation).  It generated a 
lot of popular buzz and a collective cold shoulder from the 
scientific community.  He then, much later, wrote a highly technical 
book (Nanosystems).  This produced much less popular reaction, but a 
much warmer reception from scientists.  One could argue that it is 
Nanosystems that is largely responsible for nanotech finally becoming 
the acceptable buzzword that it is today.  (I'm not convinced that 
Engines of Creation had any real benefit.)

It would be ideal if the same thing could be done with uploading: 
someone with good neuroscience credentials might write a highly 
technical book about uploading: theoretical arguments about why it 
must be possible and plausible, detailed proposals about how it might 
be accomplished.

(I started such a book when I was in grad school, but alas, it was 
too much work to finish properly while keeping up with my research. 
And since then, I have changed careers, and am no longer the right 
person to write such a book anyway.)

In an environment lacking such a detailed, technical, and coherent 
argument, we are going to have a hard time getting anyone to take us 
seriously.  (Though the recent NBIC report is highly encouraging.)

>  > By the time we can do this with rats, we'll be probably only 5-10
>>  years away from doing it with humans.  But that's probably 50-75
>>  years in the future.  We need to start much, much smaller (by orders
>  > of magnitude).
>
>I agree with the rat->human timescale, but I really hope it isn't
>50-75 years in the future.

Well, me too, but I believe that it is.  Researchers would love to 
have detailed 3D maps at 10-nm resolution of all their favorite 
organisms and tissues (e.g., retinal circuitry, leech ganglion, 
Aplysia ganglion, etc.), but the only organism that has *ever* been 
mapped out to that level is C. elegans -- a creature whose entire 
body is less than 1 mm long, and that was a herculean effort that 
took years of highly skilled labor.

Even today, the best computerized EM labs in the world (e.g. the 
Ellisman lab at UCSD, where I studied for a couple of years) still 
rely on highly skilled labor for ultramicrotoming and photography, 
and in any particular sample, there is a huge amount of damage and 
loss.  The pictures you see in the journals are the good areas; pan 
over a bit from any of those, and you'll find tears, holes, sections 
fried by the electron beam, etc.

Add up the amount of labor it requires, even today, to image even a 
small volume of tissue, and you'll see that it would take years to 
scan in 1 mm^3 this way, even if you could ignore all the gaps in the 
resulting data.

So, what's needed is a machine that can automate the 
ultramicrotoming, as well as the microscopy.  This requires 
specialized MEMS -- not nanotech, thank goodness, but not the sort of 
thing you can order in your lab supply catalog either.  It requires 
serious invention, and the early models will probably not be much 
faster than human hands (if even that).

That's why I think scanning in 1 mm^3 is a good goal -- it will 
probably still take 10-20 years, unless a benefactor decides to pour 
many millions of dollars into it.  But it's achievable, and once 
we've gone that far, we'll be able to make much faster progress by 
improving the size, speed, and quality of that machine.

>Perhaps the best solution is to propose multiple mind uploading prizes
>(as suggested by Shane). One could be the uploading of a small
>creature (e.g. C. Elegans) and another could be for uploading a human.
>Or do you think there's still too large a gap between the two?

I think even the uploading of a small creature is asking too much. 
I'd suggest focussing on the structural scanning at this point; 
uploading requires a solution of all the emulation issues too, which 
is going to be couple career's worth of work after we have good 
digital ultrastructure in hand.

However, a machine that can replicate the pioneering C. elegans 
structural study, but in a few days rather than years, would be a 
very good goal.

>I think it's slightly less bleak than that. I agree that, with respect
>to what we need for uploading, there's been rather little progress in
>the past 20 years. But if we extend our field of view to other
>disciplines, we see more of the growth we want to see. For instance,
>physics and electrical engineering have come a long way and we'll need
>their discoveries. Computers are also increasing in speed at a rapid
>pace as, you know, and this allows for discoveries to come at a
>proportional rate. Neuroscience may be the slowest growing piece of
>the puzzle, but we can't ignore the rapid progress in other areas that
>will aid both uploading and neuroscience itself.

I don't think my picture is bleak.  Futurists tend to make two 
mistakes: they're too optimistic in the short run, and not optimistic 
(or imaginative) enough in the long run.  I think you're falling into 
this common trap.  It's easy to look at a problem, seeing the big 
picture, and think a solution is right around the corner -- but in 
reality, the problem is in the details, and they take years and years 
to resolve one by one.  Progress, on a close-up scale, is slow.  It's 
just when you step back and look at a sweep-of-history level that it 
seems so fast.

Combine this general tendency for near-term progress to be slower 
than you would expect, with the fact that virtually nobody is making 
any concerted effort towards uploading technology, and you see why I 
have made my cryonics arrangements (even though I'm only 31).  Nobody 
is working on those MEMS machines which can slice and ferret away and 
image frozen neural tissue.  There isn't a demand for it, nor is 
there an easy way to explain to funding agencies or investors why it 
is worth what it would cost to develop.

Please understand, I do believe it'll happen -- in fact, it is slowly 
happening already, with every tiny advance in neuroscience and 
related fields.  But it's not rapid progress.  Researchers spend 
entire careers studying one small family of ion channels or whatnot. 
That's just the way things go.

>Without such prizes, yes, but the aim of the prizes is to make this
>sort of secondary research into primary research, and it should also
>stimulate the slow growth of neuroscience you described above.

Prize money can't fund primary research.  You have to pay grad 
students and lab techs; you have to pay for equipment and reagents 
and the building and electricity.  No researcher would put any 
serious time into work that isn't being funded directly with cold, 
hard cash -- not the possibility of cash at some point in the future 
if nobody else beats them to it first.

The way this could be made into primary research would be through a 
granting organization.  I don't know think you could yet convince any 
to make such grants, though.  And I don't think we have the resources 
at the moment to start a new one.

What prize money can do is add a little extra interest to work 
researchers are already doing, or get them to spend a little bit of 
extra time on a side project directed towards the prize.  That can 
certainly be better than nothing.

>Mind uploading should also be a candidate for funding by groups like
>the NIH, or other neuroscience supporting groups--not because it's
>related to neuroscience, but because it'd be extraordinarily useful to
>it.

Yes, if it were described not in terms of mind uploading but in terms 
of the research it would enable, or other immediate results.  Indeed, 
that's probably how researchers who care about uploading are funding 
their research now.

>Presently techniques for recording ensembles of neurons are growing as
>we discover that recording from single neurons don't provide
>information on the network dynamics that we need. If one could get
>ahold of an uploaded rat (it only has to be done once, then the
>program can be given out for others to use), you'd have information
>about every neuron at any point in time. The amount of knowledge we
>could get from such a system is hard to imagine.

Heh -- that's like an 18th-century person saying, if we could build a 
craft that goes to the moon, it would teach us revolutionary things 
about how our horses relate to their carts.  In other words, by the 
time we are able to upload a rat, we'll be long past studying the 
things you study with electrode arrays.  (Indeed, without those 
studies, I doubt you could solve the emulation problems that 
uploading will require.)

>  Given that, I'd be surprised if serious researchers don't start 
>aiming at the general idea in the next ~5 years.

OK.  Let's reconvene this discussion in 5 years and see.  :)  It's 
now been, what, 10 years since I first launched the Mind Uploading 
Home Page, so I don't mind sticking around for another 5!

Best,
- Joe

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