Here is another concern I have with current practices in the field of
cosmology.
A crucial distinction that is increasingly being blurred in
astrophysics is the distinction between true predictions and
retrodictions. A true prediction of a result or phenomenon must be
made before the relevant experimental results are known, while a
retrodiction only demonstrates a theory’s ability to reproduce known
results.
For example, Einstein’s General Theory of Relativity predicted that
mass "warps" spacetime (which was previously unknown) and retrodicted
the advance in the perihelion of Mercury (which was known but
unexplained for over a century).
If a theory can make multiple retrodictions, it increases our
confidence in the theory’s internal consistency, scope and potential
correspondence with natural phenomena.
A definitive prediction, on the other hand, is identified prior to
testing and cannot be arbitrarily adjusted afterwards. These
requirements are much more stringent, and successful predictions
demonstrate what appears to be a unique correspondence between theory
and nature. No theory can be proven absolutely, but two or three
verified predictions mean that a theory almost certainly represents an
advance in our understanding of how nature actually works.
Molding an adjustable model so that it can retrodict observational
results is a common and useful technique in science, but true
predictions are not involved in this process, and the health of
theoretical science depends on carefully maintaining this distinction.
If retrodictions are elevated to the status of true predictions, then
the integrity of science is compromised.
If anyone is interested in this topic I would like to use the Big Bang
paradigm as a case in point for studying this issue.
Rob O.
A word that some people in astronomy research use is "postdiction"
instead of "retrodiction", but the idea is the same: to try to avoid
misleading use of the word "prediction".
But you’re attempting a very tough battle. Telescope time committees and
satellite project developers dislike "true predictions", they are just
too risky – they might yield… negative results. Postdictions are more
convincing, especially when disguised as "predictions". By definition,
true predictions based on new hypotheses are most of the time wrong, so
the maximum profit ideology discourages this.
boud
[Mod. note: top-posted quoted article deleted. My own experience of
time allocation committees is that they like alternatives: this model
predicts this, but that model predicts that, therefore we can
distinguish between them. Without this, it's obviously possible that
the observing time will be wasted. Contrary to popular belief, time
allocation committees do not have a big book of canonical science to
compare proposals to... -- mjh]
On Mon, 19 May 2003 00:16:58 GMT, rlolders…@amherst.edu (Rob
Oldershaw) wrote:
>If anyone is interested in this topic I would like to use the Big Bang
>paradigm as a case in point for studying this issue.
I would be interested in reading your ideas.
Mike
[Mod. note: top-posting fixed, entire quoted article trimmed down to
the relevant lines. Folks, could you PLEASE learn to do this for
yourselves? -- mjh]
Mike Valdez <mikev…@mchsi.com> wrote in message <news:mt2.0-24092-1053390792@star.bris.ac.uk>…
> On Mon, 19 May 2003 00:16:58 GMT, rlolders…@amherst.edu (Rob
> Oldershaw) wrote:
> >If anyone is interested in this topic I would like to use the Big Bang
> >paradigm as a case in point for studying this issue.
> I would be interested in reading your ideas.
> Mike
> [Mod. note: top-posting fixed, entire quoted article trimmed down to
> the relevant lines. Folks, could you PLEASE learn to do this for
> yourselves? -- mjh]
OK, here goes.
Consider the Big Bang Theory as a case in point. It could not have
predicted the general expansion of the observable universe or the
approximate abundances of H and He because these observations were
made well before the Big Bang Theory existed. Rather, the Big Bang
model retrodicted these phenomena. The existence of the cosmic
microwave background with a black body spectrum, on the other hand,
appears to have been a genuine prediction. When we consider refined
observations of the light element abundances, the CMB temperature and
the CMB flucuations, things get interesting. The Big Bang Theory made
predictions about these phenomena, but the original predictions were
usually off by substantial margins.
The fact that the theory can now account for these results much more
accurately is due to a decades long interplay between observational
advances and theoretical adjustments. Many of the "predictions"
credited to the Big Bang Theory really should be classified as
retrodictions. To my knowledge, the sole definitive prediction that
we can attribute to the theory is a CMB with a black body spectrum.
This is a major accomplishment, but far less than is usually claimed.
The Big Bang Theory did not predict the Dark Matter that constitutes
most of the mass of the observable universe, nor can it retrodictively
identify a unique candidate for this enigmatic phenomenon. Then there
is the vacuum energy fiasco, the galaxy formation problem, etc.
>From a strictly scientific standpoint, all we are allowed to say with
confidence is that there is a high probability that at roughly 10 to
20 billion years ago the observable region of the spacetime
experienced a global expansion from a hot, dense state wherein
subatomic particles were decoupled. This is at least an order of
magnitude less than what cosmologists are currently claiming that we
know.
When we seek a more detailed and causative understanding of the basic
Big Bang paradigm, we pass into the realm of scientific conjecture.
There is nothing wrong with exploring ideas that go beyond empirical
knowledge . In fact, science would not get very far without this
creative spark, but it is crucial to know and acknowledge where the
dividing line lies between knowledge that has been backed up by
successful predictions and more speculative ideas whose "successes"
are primarily based on retrodictions.
If you will permit a little chutzpah, let’s see M.T, C.F., etc. get on
here and join the discussion.
Rob O.
In article <mt2.0-7844-1053303…@star.bris.ac.uk>,
- Hide quoted text — Show quoted text -
rlolders…@amherst.edu (Rob Oldershaw) writes:
> Here is another concern I have with current practices in the field of
> cosmology.
> A crucial distinction that is increasingly being blurred in
> astrophysics is the distinction between true predictions and
> retrodictions. A true prediction of a result or phenomenon must be
> made before the relevant experimental results are known, while a
> retrodiction only demonstrates a theory’s ability to reproduce known
> results.
> For example, Einstein’s General Theory of Relativity predicted that
> mass "warps" spacetime (which was previously unknown) and retrodicted
> the advance in the perihelion of Mercury (which was known but
> unexplained for over a century).
> If a theory can make multiple retrodictions, it increases our
> confidence in the theory’s internal consistency, scope and potential
> correspondence with natural phenomena.
> A definitive prediction, on the other hand, is identified prior to
> testing and cannot be arbitrarily adjusted afterwards. These
> requirements are much more stringent, and successful predictions
> demonstrate what appears to be a unique correspondence between theory
> and nature. No theory can be proven absolutely, but two or three
> verified predictions mean that a theory almost certainly represents an
> advance in our understanding of how nature actually works.
> Molding an adjustable model so that it can retrodict observational
> results is a common and useful technique in science, but true
> predictions are not involved in this process, and the health of
> theoretical science depends on carefully maintaining this distinction.
While I agree in general, I think that one needs to distinguish between
two types of retrodiction. Sticking with the example of the precession
of the perihelion of Mercury, while it is true to say that the problem
was known before Einstein solved it, his retrodiction is qualitatively
different from others—say, that there is another planet (Vulcan), or
that the Sun is more oblate than otherwise assumed, without any
additional evidence for these hypotheses. In other words, SINCE there
is no additional evidence for these hypotheses, the parameters can be
adjusted arbitrarily to get the desired result, while in the case of
Einstein’s retrodiction the result follows naturally from the theory,
from "first principles". In other words, the value of the precession of
the perihelion of Mercury was not in any way used as an input parameter
to determine other parameters in GR.
>>>>> "RO" == Rob Oldershaw <rlolders…@amherst.edu> writes:
RO> Consider the Big Bang Theory as a case in point.
I’m still not sure that I understand your distinction between pre-d
and post-d, but ….
RO> It could not have predicted the general expansion of the
RO> observable universe or the approximate abundances of H and He
RO> because these observations were made well before the Big Bang
RO> Theory existed.
On the contrary, the Big Bang model is simply an application of
general relativity. General relativity *did* predict a nonstatic
Universe, as was recognized in about 1916 or so. However, the
prevailing scientific notion at the time was that the Universe was
static, so Einstein added the cosmological constant. (For that
matter, Newtonian gravitation also predicts a nonstatic Universe, and
Newton simply invoked God to avoid a problem.)
RO> Rather, the Big Bang model retrodicted these phenomena. The
RO> existence of the cosmic microwave background with a black body
RO> spectrum, on the other hand, appears to have been a genuine
RO> prediction. When we consider refined observations of the light
RO> element abundances, the CMB temperature and the CMB flucuations,
RO> things get interesting. The Big Bang Theory made predictions
RO> about these phenomena, but the original predictions were usually
RO> off by substantial margins.
This is what I don’t understand. Is that good or bad? Is a vague
pre-d (there will be a CMB) "better" than a detailed post-d that
illustrates that the model can reproduce the observations? Why?
RO> The fact that the theory can now account for these results much
RO> more accurately is due to a decades long interplay between
RO> observational advances and theoretical adjustments. Many of the
RO> "predictions" credited to the Big Bang Theory really should be
RO> classified as retrodictions. To my knowledge, the sole definitive
RO> prediction that we can attribute to the theory is a CMB with a
RO> black body spectrum.
As I illustrate above, the expansion of the Universe was a
prediction. I don’t know enough of the history, but a consequence of
the BB model is that there are only 3 flavors of neutrinos, which I
think qualifies as a successful pre-d (in the sense that you are using
the word).
RO> This is a major accomplishment, but far less than is usually
RO> claimed. The Big Bang Theory did not predict the Dark Matter that
RO> constitutes most of the mass of the observable universe, nor can
RO> it retrodictively identify a unique candidate for this enigmatic
RO> phenomenon. Then there is the vacuum energy fiasco, the galaxy
RO> formation problem, etc.
As usual, many people’s problems with the BB model stem from trying to
apply it to situations to which it does not apply. The basic starting
point for applying general relativity to the Universe is to model the
Universe as having a uniform density. Now general relativity still
applies to the small scales (relevant to galaxy formation), but the
problem becomes far more difficult because one has to take into
account a number of different effects. While we don’t understand
galaxy formation, that doesn’t mean we don’t understand the evolution
of the Universe.
As to the vacuum energy "fiasco," I pointed out above that the BB
model is quite comfortable with the presence of a cosmological
constant. It’s not clear to me what the "fiasco" part of its
existence is. The fact that the observations show that the dark
energy density is close to the critical value while the particle
physicists predict that it should be orders of magnitude larger? That
general relativity doesn’t predict a value for the cosmological
constant? By this logic, QED is a poor theory because it doesn’t
predict the mass of the electron.
–
Lt. Lazio, HTML police | e-mail: jla…@patriot.net
No means no, stop rape. | http://patriot.net/%7Ejlazio/
sci.astro FAQ at http://sciastro.astronomy.net/sci.astro.html
boud <b…@astro.uni.torun.pl> wrote in message <news:mt2.0-24092-1053390683@star.bris.ac.uk>…
> A word that some people in astronomy research use is "postdiction"
> instead of "retrodiction", but the idea is the same.
Good. I think postdiction is a much better term.
> satellite project developers dislike "true predictions", they are just
> too risky – they might yield… negative results. Postdictions are more
> convincing, especially when disguised as "predictions".
Worrisome. This is probably why serendipity (finding something you
were not looking for) plays such a significant role in discovery.
> boud
> [Mod. note: top-posted quoted article deleted. My own experience of
> time allocation committees is that they like alternatives: this model
> predicts this, but that model predicts that, therefore we can
> distinguish between them. Without this, it's obviously possible that
> the observing time will be wasted. Contrary to popular belief, time
> allocation committees do not have a big book of canonical science to
> compare proposals to... -- mjh]
Oh, oh. In science negative results are important too and sometimes
"low probability" ideas are right. The emphasis on getting
"guaranteed" positive results is understandable, but a dubious
log-term policy.
Rob O.
Joseph Lazio <jla…@adams.patriot.net> wrote in message <news:mt2.0-8920-1053474274@star.bris.ac.uk>…
> >>>>> "RO" == Rob Oldershaw <rlolders…@amherst.edu> writes:
> RO> Consider the Big Bang Theory as a case in point.
> I’m still not sure that I understand your distinction between pre-d
> and post-d, but ….
I see that.
> RO> It could not have predicted the general expansion of the
> RO> observable universe or the approximate abundances of H and He
> RO> because these observations were made well before the Big Bang
> RO> Theory existed.
> On the contrary, the Big Bang model is simply an application of
> general relativity. General relativity *did* predict a nonstatic
> Universe, as was recognized in about 1916 or so. However, the
> prevailing scientific notion at the time was that the Universe was
> static, so Einstein added the cosmological constant. (For that
> matter, Newtonian gravitation also predicts a nonstatic Universe, and
> Newton simply invoked God to avoid a problem.)
Can we accept GR = BB? Seems too crude to me. Parenthetically,
Einstein said that it was not valid to push GR into the strong (and
super-strong) field setting and expect to always get reasonable
answers.
GR models were consistent with expansion, contraction and (with a
fudge factor) stasis. You call that a prediction?! It’s unlawful for
a prediction to include all possible outcomes of the test.
> RO> Rather, the Big Bang model retrodicted these phenomena. The
> RO> existence of the cosmic microwave background with a black body
> RO> spectrum, on the other hand, appears to have been a genuine
> RO> prediction. When we consider refined observations of the light
> RO> element abundances, the CMB temperature and the CMB flucuations,
> RO> things get interesting. The Big Bang Theory made predictions
> RO> about these phenomena, but the original predictions were usually
> RO> off by substantial margins.
> This is what I don’t understand. Is that good or bad? Is a vague
> pre-d (there will be a CMB) "better" than a detailed post-d that
> illustrates that the model can reproduce the observations? Why?
In my opinion the successful prediction of a blackbody background
radiation is more impressive than the postdictions. Because, after
the fact, you can usually mold a plastic model to fit the
observations.
> RO> The fact that the theory can now account for these results much
> RO> more accurately is due to a decades long interplay between
> RO> observational advances and theoretical adjustments. Many of the
> RO> "predictions" credited to the Big Bang Theory really should be
> RO> classified as retrodictions. To my knowledge, the sole definitive
> RO> prediction that we can attribute to the theory is a CMB with a
> RO> black body spectrum.
…I don’t know enough of the history, but a consequence of
> the BB model is that there are only 3 flavors of neutrinos, which I
> think qualifies as a successful pre-d (in the sense that you are using
> the word).
No! We had good evidence about the flavors of neutrinoes before
cosmologists postdicted them. Sigh. They could make a prediction
about the exact nature of the Dark Matter, but don’t hold your breath.
> As usual, many people’s problems with the BB model stem from trying to
> apply it to situations to which it does not apply. … While we don’t understand galaxy formation, that doesn’t mean we don’t understand the evolution
> of the Universe.
You can say that, but …
> As to the vacuum energy "fiasco," I pointed out above that the BB
> model is quite comfortable with the presence of a cosmological
> constant. It’s not clear to me what the "fiasco" part of its
> existence is.
There is a truly amazing conflict between cosmology and particle
physics here. But don’t take my word for it. Let’s have a brief
summary of this issue from a professional astrophysicist who currently
favors the BB model. Perhaps Ned Wright?
Rob O.
hel…@astro.multiCLOTHESvax.de (Phillip Helbig—remove CLOTHES to reply) wrote in message <news:mt2.0-29012-1053426460@star.bris.ac.uk>…
- Hide quoted text — Show quoted text -
> In article <mt2.0-7844-1053303…@star.bris.ac.uk>,
> rlolders…@amherst.edu (Rob Oldershaw) writes:
> >A crucial distinction that is increasingly being blurred in
> > astrophysics is the distinction between true predictions and
> > retrodictions (or better, postdictions).
> While I agree in general, I think that one needs to distinguish between
> two types of retrodiction. Sticking with the example of the precession
> of the perihelion of Mercury, while it is true to say that the problem
> was known before Einstein solved it, his retrodiction is qualitatively
> different from others—say, that there is another planet (Vulcan), or
> that the Sun is more oblate than otherwise assumed, without any
> additional evidence for these hypotheses. In other words, SINCE there
> is no additional evidence for these hypotheses, the parameters can be
> adjusted arbitrarily to get the desired result, while in the case of
> Einstein’s retrodiction the result follows naturally from the theory,
> from "first principles". In other words, the value of the precession of
> the perihelion of Mercury was not in any way used as an input parameter
> to determine other parameters in GR.
Yes, I definitely agree. The GR postdiction in question was
especially "clean" and natural. The fewer ad hoc adjustments and
added variables, the higher the quality of the postdiction.
Predictions and postdictions can range from high quality to low
quality. High quality predictions are highly unique to the specific
theory, are testable, and are non-adjustable.
Does a high quality postdiction trump a medium quality prediction?
Don’t ask me to go there!
rlolders…@amherst.edu (Rob Oldershaw) wrote:
> Can we accept GR = BB? Seems too crude to me. Parenthetically,
> Einstein said that it was not valid to push GR into the strong (and
> super-strong) field setting and expect to always get reasonable
> answers.
> GR models were consistent with expansion, contraction and (with a
> fudge factor) stasis. You call that a prediction?! It’s unlawful for
> a prediction to include all possible outcomes of the test.
One thing that GR does is pick up on the successes of Newtonian
physics. In the case of Mercury, Newtonian physics gives us a
framework in which to understand systematic discrepancies from the
predictions of the theory. GR adopts this, and explains the physical
significance of the final 43 arc sec/century (out of a far greater
number accounted for using Newtonian methods also available to GR).
GR gives us physical significance to deviations from given
cosmological models. That Einstein failed to grasp this immediately is
unfortunate as this actually speaks to the success of GR as a research
program.
> In my opinion the successful prediction of a blackbody background
> radiation is more impressive than the postdictions. Because, after
> the fact, you can usually mold a plastic model to fit the
> observations.
The blackbody prediction is nice, but can also be accounted for by
rival theories. However, newer info from the CMB cannot be accounted
for by many of these rival theories. What is important here is that
the CMB is a phenomena that is explained by GR and measurements of the
CMB in turn help us determine parameters of GR models. It’s not that
these are plastic theories that can be fitted to the phenomena, but
that the phenomena that the theory explains give accurate and agreeing
measurements of the parameters of the theory.
> No! We had good evidence about the flavors of neutrinoes before
> cosmologists postdicted them. Sigh. They could make a prediction
> about the exact nature of the Dark Matter, but don’t hold your breath.
Cosmologists _do_ give details about the nature of dark matter. What
they do not do is give an account of the mechanism of dark matter. But
to demand a mechanism is exaclty what Huygens, Leibniz et al. demanded
of Newton, and exactly where they went astray. Newton established
causal explanation that any mechanism would have to account for. The
exact mechanism, while certainly interesting, need not be a challenge
to a theory. Especially if the mechanism is _mere hypothesis_ and has
no basis in phenomena derived from empirical inquiry.
> There is a truly amazing conflict between cosmology and particle
> physics here. But don’t take my word for it. Let’s have a brief
> summary of this issue from a professional astrophysicist who currently
> favors the BB model. Perhaps Ned Wright?
There may be few candidates in particle physics for WIMPs. I will
reiterate, however, that to demand such evidence in the face of the
evidence from the phenomena that cosmology is providing is tantamount
to rejecting Newton because he cannot provide an account of the
vortices that cause the inverse-square centripetal acceleration fields
that surround the sun and the planets.
In article <mt2.0-21914-1053696…@star.bris.ac.uk>,
rlolders…@amherst.edu (Rob Oldershaw) writes:
> > RO> Consider the Big Bang Theory as a case in point.
> > As to the vacuum energy "fiasco," I pointed out above that the BB
> > model is quite comfortable with the presence of a cosmological
> > constant. It’s not clear to me what the "fiasco" part of its
> > existence is.
> There is a truly amazing conflict between cosmology and particle
> physics here. But don’t take my word for it. Let’s have a brief
> summary of this issue from a professional astrophysicist who currently
> favors the BB model. Perhaps Ned Wright?
I would say that almost ANY professional astrophysicist "currently
favours the BB model".
Astrophysically, the case is clear. The supernova people used classical
cosmology (work out the dependence of an observable quantity on
redshift, do the observations, and fit for the cosmological parameters)
to arrive at a firm result, which has since been confirmed by many other
cosmological tests, resulting in a "standard model" which is not in
conflict with any observations (not always the case with "standard
models" in the past—and make sure not to confuse the term with the
"standard model" of particle physics!). It looks like a cosmological
constant, it smells like a cosmological constant. They COULD have found
something else, i.e. something with a different equation of state. But
they didn’t. (Constraints on this aren’t as tight unless one assumes a
flat universe, but now we can do this safely based on the latest CMB
data which doesn’t use the other observational data leading to a
cosmological constant as input.)
The problem is with particle physics. This is obvious. The naive
back-of-the-envelope calculation results in something which is 120
orders of magnitude too large, so it’s obviously wrong. All the
"serious conflict" indicates here is that the envelope needs to be much
bigger. Where I think many particle-physics types go to far is when
they say that this one huge cosmological constant must be offset by some
OTHER contribution (i.e. a negative cosmological constant) and that
since it is improbable that they NEARLY cancel then they MUST cancel
EXACTLY. This was often used as an argument for lambda=0 before the
observations showed otherwise. Some folks (Weinberg for example) thinks
that there is such a cancellation but that it is NOT exact.
In experimental particle physics, the rule is that if something is not
forbidden then it will happen. If it is forbidden, then one has a new
conservation law etc. Obviously, the burden of proof in this case is on
the shoulders of the person suggesting such a new conservation law. So
the "natural" state of affairs is for lambda not to be zero; if nature
has a degree of freedom, it is used unless something suppresses it. So
it seems logical to accept the cosmological constant from the
particle-physics viewpoint, even aside from the fact that it has now
been observed.
The astrophysical case is so tight here, and the particle-physics one so
shaky, that I find it astounding that folks use this "conflict" as
evidence against a cosmological constant. If anything, it shows us how
far particle physics has to go.
hel…@astro.multiCLOTHESvax.de (Phillip Helbig—remove CLOTHES to reply) wrote in message <news:mt2.0-4164-1054026790@star.bris.ac.uk>…
> Astrophysically, the case is clear. …
> The problem is with particle physics. This is obvious. …
> The astrophysical case is so tight here, and the particle-physics one so
> shaky, that I find it astounding that folks use this "conflict" as
> evidence against a cosmological constant. If anything, it shows us how
> far particle physics has to go.
Your assessment may be correct.
But in addition to being more careful in our use of terms like
prediction, postdiction, observable universe, etc., I think we should
try to be more humble. The tongue-in-cheek comment (Landau’s?) that
"cosmologists are often wrong, but never in doubt" is all too true.
Because our knowledge is often quite limited and uncertain, we would
be well-advised to sprinkle our discussions with qualifiers like "on
the basis of existing data", "unless we are missing something
important", "seems to be indicated", "if all relevant parameters are
accounted for", "given current assumptions", etc.
At the risk of sounding too preachy, I think we all need to work on
this.
Rob O.
>>>>> "RO" == Rob Oldershaw <rlolders…@amherst.edu> writes:
RO> Joseph Lazio <jla…@adams.patriot.net> wrote in message
RO> <news:mt2.0-8920-1053474274@star.bris.ac.uk>…
RO> It could not have predicted the general expansion of the
RO> observable universe or the approximate abundances of H and He
RO> because these observations were made well before the Big Bang
RO> Theory existed.
>> On the contrary, the Big Bang model is simply an application of
>> general relativity. General relativity *did* predict a nonstatic
>> Universe, as was recognized in about 1916 or so. However, the
>> prevailing scientific notion at the time was that the Universe was
>> static, so Einstein added the cosmological constant. (…)
RO> Can we accept GR = BB? Seems too crude to me.
Because it is. The Big Bang model is an application of GR under
certain assumptions. GR is far more than just the Big Bang model.
RO> Parenthetically, Einstein said that it was not valid to push GR
RO> into the strong (…) field setting and expect to always get
RO> reasonable answers.
Parenthetically, Einstein also didn’t like quantum mechanics, but it
works.
RO> GR models were consistent with expansion, contraction and (…)
RO> stasis. You call that a prediction?! It’s unlawful for a
RO> prediction to include all possible outcomes of the test.
In part, this is why I am often careful to call the Big Bang a
"model." The Big Bang can describe a number of potential Universes,
ones that are destined to expand forever, ones that are destined to
collapse, ones in near stasis because the cosmological constant
balances the gravitational attraction of matter, etc. That’s because
the Big Bang depends upon certain parameters, like the Hubble constant
and mass-energy density of the Universe, parameters that cannot be
obtained ab initio from GR but have to be measured.
[...]
RO> The fact that the theory can now account for these results much
RO> more accurately is due to a decades long interplay between
RO> observational advances and theoretical adjustments.
Which you seem to consider "bad," yet that’s how most science works.
We make some measurements, build up a theoretical edifice to
understand these measurements, use the theory to predict new
measurements, make new measurements, and iterate. On rare occasions,
the entire edifice is overthrown (e.g., the conclusion that the
Universe is evolving, not static, which occurred in the mid-twentieth
century), but more generally, the edifice is just modified slightly.
RO> Many of the "predictions" credited to the Big Bang Theory really
RO> should be classified as retrodictions. To my knowledge, the sole
RO> definitive prediction that we can attribute to the theory is a CMB
RO> with a black body spectrum.
>> …I don’t know enough of the history, but a consequence of
>> the BB model is that there are only 3 flavors of neutrinos, which I
>> think qualifies as a successful pre-d (…).
RO> No! We had good evidence about the flavors of neutrinoes before
RO> cosmologists postdicted them. Sigh. They could make a prediction
RO> about the exact nature of the Dark Matter, but don’t hold your
RO> breath.
Re-read my statement. It was not that flavors of neutrinos existed,
it was a prediction about the *number* of flavors. In order for the
Big Bang nucleosynthesis to work, there cannot be too many flavors of
neutrinos. This prediction, stemming from the Big Bang model, was
confirmed later by measuring decays of the Z (or was it W?) boson.
–
Lt. Lazio, HTML police | e-mail: jla…@patriot.net
No means no, stop rape. | http://patriot.net/%7Ejlazio/
sci.astro FAQ at http://sciastro.astronomy.net/sci.astro.html
Apparently on date Thu, 29 May 2003 11:57:38 GMT,
rlolders…@amherst.edu (Rob Oldershaw) said:
>But in addition to being more careful in our use of terms like
>prediction, postdiction, observable universe, etc., I think we should
>try to be more humble. The tongue-in-cheek comment (Landau’s?) that
>"cosmologists are often wrong, but never in doubt" is all too true.
>Because our knowledge is often quite limited and uncertain, we would
>be well-advised to sprinkle our discussions with qualifiers like "on
>the basis of existing data", "unless we are missing something
>important", "seems to be indicated", "if all relevant parameters are
>accounted for", "given current assumptions", etc.
>At the risk of sounding too preachy, I think we all need to work on
>this.
Might this have to do with the nature of the practice of research?
To get anywhere much, a new proposal needs to have "champions" who are
then identified with and have something to lose if the proposal is
discarded.
If it was all anonymous… but then you need to motivate…
[Mod. note: quoted text trimmed -- mjh]
In article <mt2.0-25762-1054285…@star.bris.ac.uk>, Joseph Lazio
<jla…@adams.patriot.net> writes:
> RO> Can we accept GR = BB? Seems too crude to me.
> Because it is. The Big Bang model is an application of GR under
> certain assumptions. GR is far more than just the Big Bang model.
And BB is far more than just GR. Relativists tend to see cosmology as
an application of GR, whereas cosmologists tend to see GR as one of many
ingredients in a recipe for understanding the universe.
Joseph Lazio <jla…@adams.patriot.net> wrote in message <news:mt2.0-25762-1054285502@star.bris.ac.uk>…
> >>>>> "RO" == Rob Oldershaw <rlolders…@amherst.edu> writes:
> RO> Can we accept GR = BB? Seems too crude to me.
> Because it is. The Big Bang model is an application of GR under
> certain assumptions. GR is far more than just the Big Bang model.
Surely you jest, Lt.
> RO> Parenthetically, Einstein said that it was not valid to push GR
> RO> into the strong (…) field setting and expect to always get
> RO> reasonable answers.
> Parenthetically, Einstein also didn’t like quantum mechanics, but it
> works.
Sigh. Reality is so much more complex and subtle.
> RO> GR models were consistent with expansion, contraction and (…)
> RO> stasis. You call that a prediction?! It’s unlawful for a
> RO> prediction to include all possible outcomes of the test.
> In part, this is why I am often careful to call the Big Bang a
> "model." The Big Bang can describe a number of potential Universes,
> ones that are destined to expand forever, ones that are destined to
> collapse, ones in near stasis because the cosmological constant
> balances the gravitational attraction of matter, etc. That’s because
> the Big Bang depends upon certain parameters, like the Hubble constant
> and mass-energy density of the Universe, parameters that cannot be
> obtained ab initio from GR but have to be measured.
This is precisely why we have to be more careful about attributing
"predictions" to the plastic BB models.
> [...]
> RO> The fact that the theory can now account for these results much
> RO> more accurately is due to a decades long interplay between
> RO> observational advances and theoretical adjustments.
> Which you seem to consider "bad," yet that’s how most science works.
> We make some measurements, build up a theoretical edifice to
> understand these measurements, use the theory to predict new
> measurements, make new measurements, and iterate. On rare occasions,
> the entire edifice is overthrown (e.g., the conclusion that the
> Universe is evolving, not static, which occurred in the mid-twentieth
> century), but more generally, the edifice is just modified slightly.
In the book Subtle Is The Lord, A. Pais distinguishes model-building
from ‘theories of principle’, like GR. The distinction is crucial.
Both play a role in science. Metaphorically, the former are like
artificial diamonds, while the latter are rare natural diamonds.
> RO> No! We had good evidence about the flavors of neutrinoes before
> RO> cosmologists postdicted them. Sigh. They could make a prediction
> RO> about the exact nature of the Dark Matter, but don’t hold your
> RO> breath.
> Re-read my statement. It was not that flavors of neutrinos existed,
> it was a prediction about the *number* of flavors. In order for the
> Big Bang nucleosynthesis to work, there cannot be too many flavors of
> neutrinos. This prediction, stemming from the Big Bang model, was
> confirmed later by measuring decays of the Z (or was it W?) boson.
Please study the history of this subject, then cite the paper that
actually predicted 3 "flavors" before there was any reason to think
that 3 was the correct number. Good luck, and as the law clearly
states, Officer Lazio,: ‘ignorance is no excuse’.
Rob Oldershaw <rlolders…@amherst.edu> wrote:
> Please study the history of this subject, then cite the paper that
> actually predicted 3 "flavors" before there was any reason to think
> that 3 was the correct number.
Yang et al., Ap. J. 227 (1979) 697-704 predicts a maximum of three
families of leptons with light neutrinos, long before there was any
reason to expect this from particle physics. It wasn’t until 1989 that
measurements of the Z^0 width confirmed this in the laboratory.
Steve Carlip
Steve Carlip <sjcar…@ucdavis.edu> wrote in message <news:mt2.0-18619-1054721957@star.bris.ac.uk>…
> Yang et al., Ap. J. 227 (1979) 697-704 predicts a maximum of three
> families of leptons with light neutrinos, long before there was any
> reason to expect this from particle physics. It wasn’t until 1989 that
> measurements of the Z^0 width confirmed this in the laboratory.
If this is a clean prediction, I will be impressed and my thinking on
this issue will be changed. Let me take a close look at the paper and
the prevailing particle physics wisdom prior to its publication. May
take a few days. Nice, specific post. Thanks.
Rob
[Mod. note: quoted text trimmed -- mjh]
rlolders…@amherst.edu (Rob Oldershaw) wrote in message <news:mt2.0-29405-1054897544@star.bris.ac.uk>…
> Steve Carlip <sjcar…@ucdavis.edu> wrote in message <news:mt2.0-18619-1054721957@star.bris.ac.uk>…
> > Yang et al., Ap. J. 227 (1979) 697-704 predicts a maximum of three
> > families of leptons with light neutrinos, long before there was any
> > reason to expect this from particle physics. It wasn’t until 1989 that
> > measurements of the Z^0 width confirmed this in the laboratory.
> If this is a clean prediction, I will be impressed and my thinking on
> this issue will be changed. Let me take a close look at the paper and
> the prevailing particle physics wisdom prior to its publication. May
> take a few days. Nice, specific post. Thanks.
> Rob
> [Mod. note: quoted text trimmed -- mjh]
Alas, our library has sent anything before 1985 to the depository.
I’ll tentatively accept that Yang et al made a clean predition, until
the relevant article can be dredged out.
But in 1975 Martin Perl and his colleagues discovered the tau lepton.
There was good reason to think that this was paired with a new
neutrino. That would have made 3 families of neutrinos. I regard the
1979 prediction that there are just 3 families of neutrinos as a valid
prediction. But I hope that you will agree that it was not all that
definitive. Had they predicted 3, and only 3, when only 1 was known,
or predicted 5 in 1979 and then had that verified, it would have been
very impressive. I do not belittle their actual prediction, but think
its merits should be judged in context of what was known at the time.
>>>>> "RO" == Rob Oldershaw <rlolders…@amherst.edu> writes:
RO> rlolders…@amherst.edu (Rob Oldershaw) wrote in message
RO> <news:mt2.0-29405-1054897544@star.bris.ac.uk>…
>> Steve Carlip <sjcar…@ucdavis.edu> wrote in message
>> <news:mt2.0-18619-1054721957@star.bris.ac.uk>…
>>> Yang et al., Ap. J. 227 (1979) 697-704 predicts a maximum of
>>> three families of leptons with light neutrinos, long before there
>>> was any reason to expect this from particle physics. It wasn’t
>>> until 1989 that measurements of the Z^0 width confirmed this in
>>> the laboratory.
>> If this is a clean prediction, I will be impressed and my thinking
>> on this issue will be changed. [...]
RO> Alas, our library has sent anything before 1985 to the depository.
RO> I’ll tentatively accept that Yang et al made a clean predition,
RO> until the relevant article can be dredged out.
Note that this article is available online, for free, through the ADS,
<URL:
http://adsabs.harvard.edu/cgi-bin/nph-bib_query?bibcode=1979ApJ…227... >.
RO> But in 1975 Martin Perl and his colleagues discovered the tau
RO> lepton. There was good reason to think that this was paired with
RO> a new neutrino. That would have made 3 families of neutrinos. I
RO> regard the 1979 prediction that there are just 3 families of
RO> neutrinos as a valid prediction. But I hope that you will agree
RO> that it was not all that definitive. Had they predicted 3, and
RO> only 3, when only 1 was known, or predicted 5 in 1979 and then had
RO> that verified, it would have been very impressive. I do not
RO> belittle their actual prediction, but think its merits should be
RO> judged in context of what was known at the time.
So a "clean" prediction is not "all that definitive"? Why do I have
the feeling that the goalposts just moved?
Let us consider the situation in 1979. A new neutrino had been
discovered, on average, once per decade:
1956 electron neutrinos
1962 mu neutrinos
1976 tau neutrinos
Why not expect a new lepton family to be discovered in about ten years
after an increase in accelerator energies? Indeed, in the absence of
any other evidence, how can one conclude that there are not N more
lepton families?
–
Lt. Lazio, HTML police | e-mail: jla…@patriot.net
No means no, stop rape. | http://patriot.net/%7Ejlazio/
sci.astro FAQ at http://sciastro.astronomy.net/sci.astro.html
Rob Oldershaw <rlolders…@amherst.edu> wrote:
> I’ll tentatively accept that Yang et al made a clean predition, until
> the relevant article can be dredged out.
> But in 1975 Martin Perl and his colleagues discovered the tau lepton.
> There was good reason to think that this was paired with a new
> neutrino. That would have made 3 families of neutrinos. I regard the
> 1979 prediction that there are just 3 families of neutrinos as a valid
> prediction. But I hope that you will agree that it was not all that
> definitive. Had they predicted 3, and only 3, when only 1 was known,
> or predicted 5 in 1979 and then had that verified, it would have been
> very impressive. I do not belittle their actual prediction, but think
> its merits should be judged in context of what was known at the time.
The prediction was not “at least three,” it was “only three.” At the
time, there was absolutely no reason within particle physics to expect
that there would not be a fourth generation, or more. There’s *still*
no good theoretical understanding of this number, though it has now
been confirmed by laboratory experiments.
Why is a prediction, “There won’t be five generations,” subsequently
verified, any less impressive than a prediction, “There will be five
generations”?
Steve Carlip
[Mod. note: HTML part of multipart message removed. Please post only
in plain text -- mjh.]
With respect, it would seem to me that your distinction between prediction
and retrodiction is more a matter of serendipity than anything else. Surely
you would agree with me that there is no physical causal linkage between the
creation of a hypothesis and the identification of evidence relevant to that
hypothesis. If I had a hypothesis that I kept to myself for years because I
thought it was unprovable, and I later find evidence "predicted" by the
theory, does it matter whether I find the email in which I made the
prediction? If the confirmatory evidence existed before I made the
prediction, does that restore its status as predictive instead of
retrodictive?
Let’s use a recent example appearing in the public press. It has recently
come to light that a key element of confirmatory evidence for Watson &
Crick’s identification of DNA was actually a retrodiction of a discovery
made by another researcher in the lab. This, if true, may have much to say
about integrity, and, since the uncredited researcher was female, much to
say about gender equity and fairness, but I posit that it tells us little as
to whether our genetic structure is contained within DNA.
What we should really be worried about, then, is deluding ourselves into
believing that our hypotheses are the only explanation of observational
evidence, regardless of the serendipitous sequence of theory and
observation; the sequence in which we encounter the hypothesis and the
evidence doesn’t change the evidence, but it may change whether we are
deluded by the evidence. The social sciences are equally concerned about
self-delusion generated by "prediction." They have given that form of
self-delusion the name "selective perception." History has taught too many
times that, with our wonderful minds, we are singularly capable of deluding
ourselves regardless of sequence!
Formal scientific method has a partial answer to this, though some modern
writers criticize current practices on the grounds that we are not following
strict scientific method. (Sorry, can’t find the book right now.) What you
label retrodictions could be stage one of the scientific method, in which we
observe on the way to stage 2, in which we form a hypothesis. We must then
test the hypothesis with further observations and then seek intersubjective
agreement. But, the serendipity of the prediction occurring outside the
observation of the scientist prior to or after the creation of the
hypothesis must surely be irrelevant.
– Richard S. Sternberg
Rich…@NOspamRSSternberg.org
- Hide quoted text — Show quoted text -
Joseph Lazio <jla…@adams.patriot.net> wrote in message <news:mt2.0-3889-1055024620@star.bris.ac.uk>…
> >>>>> "RO" == Rob Oldershaw <rlolders…@amherst.edu> writes:
> RO> rlolders…@amherst.edu (Rob Oldershaw) wrote in message
> RO> <news:mt2.0-29405-1054897544@star.bris.ac.uk>…
> >> Steve Carlip <sjcar…@ucdavis.edu> wrote in message
> >> <news:mt2.0-18619-1054721957@star.bris.ac.uk>…
> >>> Yang et al., Ap. J. 227 (1979) 697-704 predicts a maximum of
> >>> three families of leptons with light neutrinos, long before there
> >>> was any reason to expect this from particle physics. It wasn’t
> >>> until 1989 that measurements of the Z^0 width confirmed this in
> >>> the laboratory.
> >> If this is a clean prediction, I will be impressed and my thinking
> >> on this issue will be changed. [...]
> RO> Alas, our library has sent anything before 1985 to the depository.
> RO> I’ll tentatively accept that Yang et al made a clean predition,
> RO> until the relevant article can be dredged out.
> Note that this article is available online, for free, through the ADS,
> <URL:
> http://adsabs.harvard.edu/cgi-bin/nph-bib_query?bibcode=1979ApJ…227... >.
> RO> But in 1975 Martin Perl and his colleagues discovered the tau
> RO> lepton. There was good reason to think that this was paired with
> RO> a new neutrino. That would have made 3 families of neutrinos. I
> RO> regard the 1979 prediction that there are just 3 families of
> RO> neutrinos as a valid prediction. But I hope that you will agree
> RO> that it was not all that definitive. Had they predicted 3, and
> RO> only 3, when only 1 was known, or predicted 5 in 1979 and then had
> RO> that verified, it would have been very impressive. I do not
> RO> belittle their actual prediction, but think its merits should be
> RO> judged in context of what was known at the time.
> So a "clean" prediction is not "all that definitive"? Why do I have
> the feeling that the goalposts just moved?
> Let us consider the situation in 1979. A new neutrino had been
> discovered, on average, once per decade:
> 1956 electron neutrinos
> 1962 mu neutrinos
> 1976 tau neutrinos
> Why not expect a new lepton family to be discovered in about ten years
> after an increase in accelerator energies? Indeed, in the absence of
> any other evidence, how can one conclude that there are not N more
> lepton families?
I’ll stand by what I have said on this topic (quoted above). I called
it a "valid prediction", but I would rate it as good rather than
excellent, for the reason given. Also, according to your post, can we
now say with scientific certainty that there are just 3 families? Has
the testing come to an end? Is the answer final? What would you say
if a 4th family was found?
- Hide quoted text — Show quoted text -
Steve Carlip <sjcar…@ucdavis.edu> wrote in message <news:mt2.0-23076-1055062525@star.bris.ac.uk>…
> Rob Oldershaw <rlolders…@amherst.edu> wrote:
> > I’ll tentatively accept that Yang et al made a clean predition, until
> > the relevant article can be dredged out.
> > But in 1975 Martin Perl and his colleagues discovered the tau lepton.
> > There was good reason to think that this was paired with a new
> > neutrino. That would have made 3 families of neutrinos. I regard the
> > 1979 prediction that there are just 3 families of neutrinos as a valid
> > prediction. But I hope that you will agree that it was not all that
> > definitive. Had they predicted 3, and only 3, when only 1 was known,
> > or predicted 5 in 1979 and then had that verified, it would have been
> > very impressive. I do not belittle their actual prediction, but think
> > its merits should be judged in context of what was known at the time.
> The prediction was not “at least three,” it was “only three.” At the
> time, there was absolutely no reason within particle physics to expect
> that there would not be a fourth generation, or more. There’s *still*
> no good theoretical understanding of this number, though it has now
> been confirmed by laboratory experiments.
I did not say "at least three"! I said "just three", which if I am
not mistaken is equal to "only three". Have we confirmed that there
are only 3? I think you will find that many assumptions underlie any
‘final confirmation’. I think my assessment of the strength of the
prediction was fair.
> Why is a prediction, “There won’t be five generations,” subsequently
> verified, any less impressive than a prediction, “There will be five
> generations”?
I regard the prediction of a specific number, x, more impressive than
the prediction of SOME number <x.
"Richard S. Sternberg" <bestfa…@RSSternberg.org> wrote in message <news:mt2.0-23076-1055062608@star.bris.ac.uk>…
[...]
> Formal scientific method has a partial answer to this, though some modern
> writers criticize current practices on the grounds that we are not following
> strict scientific method. (Sorry, can’t find the book right now.) What you
> label retrodictions could be stage one of the scientific method, in which we
> observe on the way to stage 2, in which we form a hypothesis. We must then
> test the hypothesis with further observations and then seek intersubjective
> agreement. But, the serendipity of the prediction occurring outside the
> observation of the scientist prior to or after the creation of the
> hypothesis must surely be irrelevant.
[Mod. note: entire quoted article trimmed ... please do this
yourselves -- mjh.]
Is this a Deconstructionist hoax?