Monday, May 04, 2020

Predictions are overrated

Fortune Teller. Image: Vecteezy.
The world, it seems, is full with people who mistakenly think that a theory which makes correct predictions is a good theory. This is rubbish, of course, and it has led to a lot of unnecessary confusion. I blame this confusion on the many philosophers, notably Popper and Lakatos, who have gone on about the importance of predictions, but never clearly said that it’s not a scientific criterion.

You see, the philosophers wanted a quick way to figure out whether a scientific theory is good or not that would not require them to actually understand the science. This, needless to say, is not possible. But the next best thing you can do is to ask how much you can trust the scientists. It is for this latter purpose, to evaluate the trust you can put in scientists, that predictions are good. But they cannot, and should not, ultimately decide what the scientific value of a theory is.

The problem is well illustrated by a joke that my supervisor used to make. He liked to tell his students that whenever you predict something, you should also predict the opposite, because this way you can never be wrong. Haha. In case you are a student, let me warn you that this is bad career advice; You’d also inevitably be wrong, and it tends to be the dirt that sticks. So, don’t /end{advice}. But this joke makes clear that just because a theory makes a correct prediction doesn’t mean it’s good science.

Oh, you may say, you can get away with this once, but then you wouldn’t be able to make several correct predictions. If you said that, you’d be wrong. Because repeated correct predictions, too, are easy to accomplish. In fact, your naïve belief that correct predictions somehow speak for a theory is commonly exploited by scammers.

See, suppose I plan to convince someone that I can correctly predict the stock market. What do I do? Well, I pick, say, 3 stocks and make “predictions” for a week ahead, but that are really just guesses which cover all reasonably possible trends. I then select a large group of victims. To each of them I send one of my guesses. Some of them will coincidentally get the correct guess. A week later, I know which people got the correct guess. To this group, I then send another set of guesses for the week ahead. Again, some people will get the correct guess by coincidence, and a week later I will know which one it was. I do this a third time, and then I have a group of people who have good “evidence” that I can tell the future.

Amazing, no?

What’s the problem here? The problem is that correct predictions don’t tell you whether someone’s theory is good science.

As we have just seen, one of the problems with relying on predictions is that they may be correct just by coincidence. The larger the pool of predictions – or the pool of scientists making predictions! – the more likely this is to happen. The other problem is that relying on predictions makes fundamentally no sense. If I have a scientific theory, it is either a good description of nature, or it is not. At which time someone made a calculation for an observable quantity is entirely irrelevant for a theory’s relation to nature.

This is a point which is often raised by string theorists, and they are correct to raise it. String theorists say that since string theory gives rise to general relativity, it deserves as much praise as general relativity. That’s because, if string theory had been discovered before general relativity, it would have made the same predictions: light deflection on the sun, precession of Mercury, black holes, gravitational waves, and so on.

And indeed, this would be a good argument in favor of string theory – if it was correct. But it isn’t. String theory does not give rise to general relativity. It gives rise to general relativity in 10 dimensions, with supersymmetric matter, a negative cosmological constant, and dozens of additional scalar fields. All this extra clutter conflicts with observations. To fix this conflict with observations, string theorists then have to make several additional assumptions. With that you get a theory that is considerably more complicated than general relativity, but that does not explain the data any better. Hence, Occam’s razor tells you that general relativity is preferable.

Of course, it’s this adding of ad hoc assumptions to fix a mismatch with observation that the philosophers were trying to prevent when they requested testable predictions. But it’s the ad hoc assumptions themselves that are the problem, not the time at which they were made. To decide whether a scientific theory is any good what matters is only its explanatory power. Explanatory power measures how much data you can fit from which number of assumptions. The fewer assumption you make and the more data you fit, the higher the explanatory power, and the better the theory.

Ok, I admit, it’s somewhat more complicated than that. That’s because it also matters how well you fit the data. If you make more assumptions, you will generally be able to fit the data better. So there is a trade-off to be made, which needs to be quantified: At which point is the benefit you get from more assumptions not worth a somewhat better fit to the data? There are statistical tools to decide that. One can argue which one of those is the best for a given purpose, but that’s a fight that experts can fight in the case at hand. What is relevant here is only that the explanatory power of a theory is quantifiable. And it’s the explanatory power that decides whether a theory is good or not.

That’s obvious, I know. But why then do philosophers go on (and on and on) about predictability? Because it’s a convenient rule of thumb. It prevents scientists from adding details to their theory after they have new data, and doing so tends to reduce explanatory power. So, in many cases, asking for predictions is a good idea.

However, if you rely on predictions, you may throw out the baby with the bathwater. Just because no one made a prediction doesn’t mean they necessarily will add assumptions after an observation. In fact, the very opposite can happen. Scientists sometimes remove unnecessary assumptions when they get new data. A theory, therefore, can become better when it has been updated.

Indeed, this has happened several times in the history of physics.

Remember Einstein introducing the cosmological constant and then calling it a blunder? He had mistakenly made a superfluous assumption and then removed it after he learned of the observations. This increased, not decreased, explanatory power. Or think of Dirac’s supposed discovery of anti-particles. When his mathematics revealed a positively charged equivalent of the electron, he argued it would be the proton, which had already been observed at the time. This required the ad hoc assumption that somehow the difference in the masses between the electron and proton didn’t matter. When the positron was discovered later, Dirac could remove the ad hoc hypothesis, thereby improving his theory.

By now I hope it is clear that you should not judge the scientific worth of a theory by looking at the predictions it has made. It is a crude and error-prone criterion. Unfortunately, it has become widely mistaken as a measure for scientific quality, and this has serious consequences, way beyond physics.

Epidemic models, for example, have been judged erroneously by their power to correctly predict the trends of new cases and deaths. But such predictions require modellers to also know what actions society takes to prevent the spread. They require, basically, to predict the minds of political leaders. This, needless to say, is asking for somewhat too much. But, yell the cranks, if it doesn’t make predictions, it’s not science! Nonsense. You should judge epidemic models – any model, really – by how much data they have been able to describe well, and how many assumptions were needed for this. The fewer assumptions and the better the fit to data, the higher the scientific value of the model.

A closely related confusion is the idea that scientists should not update a theory when new data comes in. This can also be traced back to Popper & Co who proclaimed that it is bad scientific practice. But of course a good scientist updates their theory when they get new data. That, after all, is the essence of the scientific method! You update your theory so that it has the highest explanatory power. In practice, this usually means recalibrating free parameters if new information is available.

Another example where this misunderstanding matters are climate models. Climate models have correctly predicted many observed trends, from surface temperature increase, to stratospheric cooling, to sea ice melting. That’s an argument commonly used against climate change deniers. But the deniers then go and dig up some papers that made wrong predictions. This, so their claim, demonstrates that really anything is possible and you can’t trust predictions.

In defense, the scientists say the wrong predictions were few and far between. The deniers then respond – entirely correctly – that there may have been all kinds of reasons for the skewed number of papers that have absolutely nothing to do with their scientific merit.

By now we are arguing about the integrity of scientists and the policies of their journals instead about science. The scientists are clearly losing the argument. And why is that? Because relying on predictions is not a scientific argument. It is inherently a sociological argument. It’s like claiming that a study must be wrong because the lead author has a conflict of interest. That’s reason to be skeptical, yes. But it does not follow that the study is necessarily wrong. That would be a logically faulty conclusion.

What, then, is the scientific answer for the climate change deniers? It’s that climate models explain loads of data with few assumptions. The simplest explanation for our observations is that the trends are caused by human carbon dioxide emission. It’s the hypothesis that has the highest explanatory power.

To add an example that is closer to home: Many non-physicists ridicule hypotheses like supersymmetry and certain types of particle dark matter because they can be eternally amended and hence make no predictions. But that is not the problem with these models. Updating a theory when new data comes in is totally fine. The problem with these models is that they have assumptions that were entirely unnecessary to explain any data to begin with.

Adding supersymmetry to the standard model or details about dark matter particles to the concordance model is superfluous. It lowers the explanatory power of these theories, instead of increasing it. That’s what’s unscientific about it. And of course once you have an assumption that was superfluous in the first place, you can eternally fiddle with it. But it’s the use of superfluous assumptions that’s the unscientific part, not updating them.

In brief, I think the world would be better place if scientists talked less about predictions and more about explanatory power.

144 comments:

  1. So, I'm a little confused... I thought that what separates science from philosophy was that scientific assertions (i.e. hypotheses and theories) are testable. That is, theories and hypotheses explain phenomena AND can be falsified by proposing in some form tests. In simplistic form, "If theory xxx is correct then experiment yyy should produce result zzz".

    If a proposed description of some aspect of reality does not result in testable predictions, is it scientific?

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    1. hybrid,

      "I thought that what separates science from philosophy was that scientific assertions (i.e. hypotheses and theories) are testable."

      I don't know why people believe this. Making testable predictions is trivial, and does not tell you that someone used good scientific practice. I explained this here.

      "If a proposed description of some aspect of reality does not result in testable predictions, is it scientific?"

      As I explained in the blogpost that you are commenting on, the answer is yes.

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    2. "The world, it seems, is full with people who mistakenly think that a theory which makes correct predictions is a good theory. This is rubbish, of course, and it has led to a lot of unnecessary confusion. I blame this confusion on the many philosophers, notably Popper and Lakatos, who have gone on about the importance of predictions, but never clearly said that it’s not a scientific criterion."

      Isn't that a caricature? Which serious scientist or philosopher ever claimed that making predictions was sufficient for a scientific theory?

      The point is that making potentially falsifiable predictions is a necessary, but by no means sufficient, criterion for a scientific theory.

      Of course, no theory can every be proven to be correct. However, theories can be proven to be incorrect. One way to do that is that if a theory makes a clear prediction which is falsified by observation, then it is a strong indication that the theory is wrong.

      In other words, a theory which doesn't make falsifiable predictions is not a scientific theory. That does not imply (and, again, who has ever seriously suggested this?) that any theory which makes any prediction is a scientific theory.

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  3. I think your argument against falsification is a bit of a straw-man argument. Popper himself was never that crude, and other philosophers of science have debated and amended his ideas (Lakatos, et al.)

    https://plato.stanford.edu/entries/lakatos/#ImprPoppScie

    Maybe physicists who don't study the philosophy of science but simplify it into the most narrow interpretation are your real target!

    First, I think predictions and falsifiability were emphasized against the background in which it was thought measurements could PROVE a theory like math was proved. The emphasis on predictions went with the shift that theories could only be DISPROVED or stand up to strong attempts to disprove them. Until the early 20th century when relativity and QM made correct predictions (star light bent in the 1919 eclipse, etc.) that Newtonian physics failed at, that long run of success of the Newtonian framework had fooled people into thinking it was basically proved. They'd forgotten an experiment in a new domain could show its limits. And the philosophers of science were not so naive to frame their argument so that a predictor could made numerous predictions and then claim on the basis of ONE of them succeeding that the theory was right--they tried to couch their arguments in probabilistic form. They argued about "hypothesis bundles" and "auxiliary hypotheses"; for example the apparent superluminal neutrinos from a few years ago could have "falsified" relativity or could instead have falsified the idea that the experiment was working...

    Maybe it's just your emphasis... I don't disagree with:

    it’s a convenient rule of thumb. It prevents scientists from adding details to their theory after they have new data, and doing so tends to reduce explanatory power. So, in many cases, asking for predictions is a good idea.

    and that in real practice things are complicated.

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    1. I am not arguing against falsification here. I did this here. This blogpost is about the requirement that a theory makes predictions. You can falsify a theory very well with data that predates the theory, so these are two separate things.

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  4. Interesting argument, and persuasive analogies marshalled in support of it.

    However, while "explanatory power" is no doubt something "nice" for a theory to have, one might wonder what value it has if it can't make useful predictions, if it can't be used as a guide, and as a tool to improve society and human flourishing.

    Absent such "proofs of the pudding", it's hard not to see such theories as little better that the "Philosophick Romances" that P.B. Medawar argued was characteristic of "eighteenth-century philosophizing" in his "Art of the Soluble".

    But no doubt, testable predictions are often hard to come by, particularly when the social & monetary costs for testing may well be prohibitive. May often require something in the way of "faith" to proceed on the assumption that they are accurate.

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    1. Steersman,

      Well, for one there is a value in understanding the past even if it does not help you shape the future. People just want to know how they and the world came into being, even if that knowledge has no practical use.

      Having said that, when I explain that predictions should not be used to decide whether a theory is good not not, then this does not mean that the theory will continue to not make prediction. But if you discard it erroneously, it certainly won't.

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  5. "Climate models have correctly predicted many observed trends, from surface temperature increase, to stratospheric cooling, to sea ice melting."

    How do you reconcile that with your entry on "Real Butterfly Effect", where you convincingly wrote "deterministic system predictions may only be possible for a finite amount of time"

    The climate modelers would have us believe they can predict 30 cm ocean level rises >80 yrs in the future.

    Of course, researchers won't get further gov't $ grants to "study the problem" if they also adopt the policy position "human ingenuity will adapt". Something like 1/2 of Netherlands is already below sea level There's a strong career incentive to be overly alarmist & keep he grant money coming

    Indeed, you've often written fo the perverse incentives motivating theoretical physicists to keep inventing new unobservable fields & particles.

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    1. TomH,

      Have you really still not understood that it is very well possible to predict average trends of a partly chaotic system even if you in the short run cannot predict the detailed evolution? How often do people have to tell you that weather isn't the same as climate?

      "Indeed, you've often written fo the perverse incentives motivating theoretical physicists to keep inventing new unobservable fields & particles."

      Climate change is observable.

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  6. A physicist not explaining why the predictions in question are more promising than the next best alternative predictions, is like an economist not caring about opportunity costs and therefore failing to be a good economist.

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  7. To be fair to Popper - his claim was not that science in order to be science has to make "good predictions"; his claim is, rather, that it has to be falsifiable, meaning you have to be able to make predictions, any predictions, and it does not matter wether they are good or bad. His goal was not to avoid having to study domain knowledge (physics or what not), but rather to eliminate what he thought is pseudo-science, say, psychoanalysis. Actually, I have no idea what prompted you to frame it this way as you yourself stated a couple of posts ago the real problem with the Popper's position: falsifiability is a necessary but not sufficient condition for science to be science proper. I like your way of defining science as an activity that (1) gathers raw data (2) develops a model to explain/fit the data (3) does so with smallest amount of assumptions possible. In order words, falsifiability is a logical corollary of your definition (the second step in your definition).

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  8. David Deutsch offers a good criterion: good theories are "rigid". They are hard (or better impossible) to square with incompatible evidence. There is, of course, also Quine's dictum that science is like a force-field with the boundary condition of experience and thus *any* new evidence can be accommodated if one is prepared to make a drastic enough adjustment. But the rigidity requirement is still a good one, I think.

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    1. Deutsch also said something like "an explanation has to convince". I feel that gets to the heart of the matter.

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  9. May be a good time to point out this common misunderstanding.
    The problem with public discourses is, that the real criterion explanatory power often is hardly available to a broader public or worse, the substitute plausibility works against science or scientists. For non-experts predictions are a kind of stand-in for explanatory power they can hardly judge - including the philosophers you mentioned and more so the common fellow citizen.
    " It’s like claiming that a study must be wrong because the lead author has a conflict of interest. That’s reason to be skeptical, yes. But it does not follow that the study is necessarily wrong."
    Right, but it too often indicates, that the study may be biased and not really trustworthy, especially if the conflict is hidden.

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  10. I had read this essay before posting in Twitter and I read it now again and can't make sense of it, hence the question I made in Twitter (Making predictions is a necessary condition, but not sufficient, no?) still stands.

    I am trying to understand the meaning of "scientific theory" that is used here, especially how it can be *good*. Science gives results that are correct or incorrect, hence a scientific theory can be a set of statements with a single truth value. If one develops a new exposition that explains the results of already known experiments, this new theory is good from the pedagogical, cultural or whatever point of view, but would it make sense to call it good from the scientific point of view, while it doesn't produce any new results?

    One can make predictions right and left for opposite results, but these predictions are not coming from a theory (at least not from a scientific one), because a theory should not lead to contradicting results. On the other hand, a tautology can't be a scientific theory, it's only an exercise in logic.

    Explanatory component of a theory is extremely important, but that's not the entire theory, because why would one want then two names for the same thing? (Explanation and Theory, to state it explicitly. And, yes, I know that synonyms exist, but this is not what we have here and I am not being pedantic.)

    I guess it is obvious that I consider theory to contain both parts: explanation and prediction, both important in equal measure. What is wrong with this? Why throwing the baby (Prediction) with the bath - and here I am referring to the statements that the worth of a scientific theory should not be judged based on predictions it has made? Hell, this is not throwing only the baby, but also the Father (I am referring to the Experiment here). Because, why one needs experiments then?

    Models are not theories and I don't understand why would one confuse them. Epidemic, climate or other models of complex systems have large errors, hence predictions that they make cover a really wide spectrum of phenomena. Based on the climate theory I am certain that summers will be warmer that winters, but my model can't tell with the same certainty tomorrow's weather. It's easy to calculate the chances of getting a result correctly by pure/random guessing or by running the calculations of a given model. In fact, there is an entire theory of unpredictable although deterministic systems, which still predicts that it can't predict the outcome of a given experiment.

    In any case, I thought that these discussions were settled, especially now that we might be at the dawn of some insights different from the ones discussed in this essay (I have in mind the insights or results that AI might provide, for example). But, I might be wrong, so these things are not settled at all.

    This being my first comment in this blog, I should conclude by saying that I enjoyed Lost in Math.

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    1. No, making predictions is not necessary. As I have explained in my blogpost, at which time someone happened to make a calculation is entirely irrelevant for the question whether a theory is a good description of nature.

      Look, if we had made the same observations in the past as we have done, but general relativity would only be proposed tomorrow, would you claim that it's not a good theory because it explains data that was already available rather than having predicted it? That would be entirely insane because you would be discarding the best explanation of your observations.

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    2. All I am saying is that one can't call something Theory if it doesn't have the following statement in it: all that was claimed thus far, will be true tomorrow.

      I think Lagrangian mechanics (vs Newtonian) is a good example.

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  11. Sabine, Everytime I read your articles I am inspired... I say - At least one scientist sees the big problem in the big picture and realizes that the approaches currently being made to advance science (more specifically theoretical physics) are 1) Not sufficient and 2) Is taking us away from science. In the next year I hope you will look into Hierarchy of Energy theory when it is made available as a free online download. I think it may bring some scientific excitement into the world.

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  12. There is really not intrinsic difference between an "explanation" or a "prediction" aside from the fact that an explanation assumes the fact/phenomena/measurement already known/observed but any explanation can be considered as a prediction of an unknown fact that needs empirical validation. From a logical standpoint they are exactly the same.

    But obviously is a lot easier to "explain" than to predict the result of a given experiment or observation( hindsight will give you 20/20 ), the history of Science fully support that with plenty of examples, and not by chance making valid predictions in fundamental Science brings usually a lot of social recognition and prestige. There is an army out there "making" explanations but very few are making valid predictions or discovering new facts or phenomena.

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  13. The last third of this comic definitely resonates with your post I think, regarding modelling, assumptions, predictions etc.

    https://fivethirtyeight.com/features/a-comic-strip-tour-of-the-wild-world-of-pandemic-modeling/

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  14. One curious problem with conditioning a theory's validity on its predictive power occurs when you run out of things to predict, and stand in a paradoxical situation where you know all the things you have wanted to know, but are not allowed to claim you understand them.

    Consider this scenario: The new Oppressively Large Hadron Collider (OLHC) has recently been built. Elsewhere, a physicist is working a model of particle physics that is more elegant than the standard model and explains everything the standard model can't, such as baryon asymmetry, neutrino oscillation and maybe even the mass ratios. The physicist immediately sets to work on fleshing it out and searching for ways it could be tested, and finds only one - his model has one additional particle that the standard model lacks. He's so engrossed in his work that he doesn't talk to friends and doesn't browse the web.

    Eventually he finishes the first treatment of his paper and submits it to Arxiv. Once he's done, he rests while checking the news... and his heart sinks. OLHC had announced the discovery of a new particle three weeks ago, with a mass and charges almost exactly the same as his. He can't reasonably claim to have predicted it independently.

    So now there will be those who will recognize in the new model more appealing features than the prediction of that particle and will choose to accept it over the standard model, but there will also be those who will refuse to accept it for not technically passing that bureaucratic hurdle that a theory should pass and will carry on treating baryon asymmetry as an unexplained mystery.

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  15. I don't know about Popper, but if you're saying that Lakatos that "didn't understand the science," I believe it's wrong ... I've read his book Proofs and Refutations, and it's clear he understood mathematics quite well. And his degree was in math, physics, and philosophy, so I suspect he also understood physics quite well.

    (Of course, that doesn't mean that he got his philosophy of science correct.)

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    1. I didn't say that philosophers didn't (or don't) understand science. Fwiw, most philosophers I know happen to have a PhD in physics. I said that they were not looking for a criterion that would require an actual understanding of the science. They were looking for a one-size-fits-all approach of telling science from pseudoscience. Asking for predictions is not a bad idea to that end. But it doesn't always work, as the examples in my blogpost demonstrate.

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    2. To paraphrase Goethe: One can convince one self while viewing a great collection of scientific works that nearly each master had a different way of approaching nature. In my opinion, what is required in science is the same thing that is required in art, namely "taste" and "judgment."

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  16. A physics analogy: this reminds me of a lecture on Landaus quantum liquid. When calculating the mass of fermion that makes up the liquid, one gets an effective mass m* that includes all ‘collective effects’, so to speak. Interestingly enough, this m* depends on variation of Fermi level e(p) so that adding complexities actually increases it. So your theory is in special kind of trouble if calculated effective mass m* is greater than measures effective mass m’ because adding more interactions into the theory will only enlarge discrepancy |m*-m’|. This is the case with superconducting cuprates; heterostructure GaAs in another example.

    So that’s a clear signal that the way forward is to get back to the blackboard and start trimming down! On the other hand, it is easy for solid state gals and guys to talk like this; they actually can get m’.

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  17. You're making a distinction between prediction and retrodiction (explanation post hoc), but I'm not sure I agree. Beyond intellectual curiosity retrodictions aren't that interesting. What we want is to know about the future, in terms of harms, potentials, etc.

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    1. Tam,

      Whether a scientific theory is "interesting" is a different question altogether. And it is ultimately a value decision, so not one that we are going to answer, here or elsewhere. But let me ask you this, suppose string theorists managed tomorrow to calculate the masses of all the particles of the standard model correctly to within measurement precision. Would you call that uninteresting?

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    2. Tam says: Beyond intellectual curiosity retrodictions aren't that interesting.

      I object. Didn't all of Darwin's evolution begin as a retrodiction? Most of us consider that very interesting.

      And don't forget, nobody has ever seen a Brontosaurus or T-Rex, their existence is 100% retrodiction.

      Oh wait, so is the Big Bang Theory, Inflation, and pretty much all of astrophysics. We are just retrodicting what most likely happened based on what we see now.

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  18. This is wonderfully illuminating. Thank you.

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  19. Dr. Hossenfelder,

    A quick typo correction: "gone one about" in your first paragraph should be "gone on about".

    Now a question: You say that adding supersymmetry to the standard model is unscientific because it lowers the explanatory power of the theory. Is this a statement with which all competent scientists working in good faith would agree? If so, I wonder why nobody blew the whistle on this practice when it first happened.

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    1. Mike,

      Thanks for spotting this typo, I have fixed it.

      As to supersymmetry. Lots of people have "blown the whistle" on this, but it makes no difference. The reason is quite simply that physicists can earn a living writing papers about useless theories, and they have fun doing so, so of course they continue doing it. If you could make money having fun with doing something useless, would you stop it voluntarily?

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    2. It appears that supersymmetry is the easy whipping boy here. The problem is that supersymmetry does work a hole in the Coleman-Mandula no-go theorem on the inability to unify gauge fields with gravitation. With a and a^† the raising and lowering operators for bosons and b and b^† the raising and lowering operators for fermions then Q = a^†b and Q^† = b^†a respectively replace a fermion with a boson and replace a boson with a fermion. These define brackets and an anticommutator generates Lorentz boosts. It has to be admitted that at least on a theoretical front this is a way spacetime symmetry and quantum statistics have some unification. There are IMO other connections and I see SUSY as a slice through that.


      What is dead is the idea of low mass or low energy SUSY. The idea was that by breaking SUSY there was an associated field disturbance that had certain physics with the spectra of elementary particles. The null results of the LHC has cratered these proposals. I have to feel a bit sorry for Gordon Kane and others in that industry, which has included thousands of people. Early on I had some reservations about this, for I saw this connection between quantum statistics and spacetime as a quantum gravitation physics more in the UV.

      I would not consider SUSY dead, or even as zombie science. I think it is a hypothesis that one should keep in their toolbox. I think it may fit into a different setting with QFT. For instance, I think Philip Anderson had it right that emergent particles are of importance. If we think of particles as entanglements of states associated with topological quantum numbers then really elementary particles can be seen as emergent as well.

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    3. But if Coleman-Mandula says it is impossible to unify gauge fields with gravity AND the SUSY hole is apparently closed, then... maybe indeed it is impossible to unify these? Is this logical possibility considered seriously in the Quantum Gravity world? Maybe the inability to reconcile QFT with GR is the answer, not a question? Why, in principle, can't we have two physics co-existig in the real world (not the necessarily incomplete descriptions thereof) and being what they are by pure coincidence and in no relation to each other?

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    4. Any theorem is only as good as its assumption and physics isn't math. If you don't like the conclusions, change the assumptions. SUSY does not fulfill the assumptions of the theorem. I explain that in my book, btw.

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    5. Sabine,

      I merely point out that demanding unified, yet perhaps still undiscovered physics is one more assumption about its existence. If I put an apple and an orange to a basket and hand it over to you, you are free to whatever you want with that. You may, for example, try to explain the content of the basket. You may even consider the fruit to be the results of a broken symmetry of a fully symmetric orple. Your colleague might postulate appranges instead, realisable only in 69 dimensions, of which 7 are time-like. You both might be enjoying your frameworks, but the truth is that there has never been any link between them. Your all attempts have been built on a wrong and unjustified assumption.

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    6. SUSY is really a form of quantum superposition or entanglement between fermions and bosons. There is an intertwining Grassmann number involved. SUSY could be just one part of a general theory of superposition, Schmidt decomposition of states and entanglement.

      As I said, when I was an undergraduate I read about SUSY and thought initially it was about quantum gravitation, which a part of it is. However, I found it interesting to see the largest research industry was with the standard model at TeV range of energy. I thought this was very strange at first.

      The low energy or low mass particle SUSY appears likely to be incorrect. The whole minimal supersymmetric standard model idea is comatose and on life support. A part of the call for the next collider is that it might recover there. However, people have to strain things hard to get the SUSY Higgs to work on a phenomenological level. It appears plausible none of that will be there in the 50 or 100 TeV energy range.

      SUSY may then be an aspect only of quantum gravitation. Experimental support for this will obviously not be easy.

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    7. Lawrence Crowell wrote: "It appears that supersymmetry is the easy whipping boy here." and "I think it is a hypothesis that one should keep in their toolbox." That is an astute observation ! Perhaps, readers would be surprised to learn of its application to laser arrays: Supersymmetric Laser Arrays (arXiv:1812.10690). Read: "Even though the full ramification of SUSY in high-energy physics is still a matter of debate that awaits experimental validation, supersymmetric techniques have already found their way into low-energy physics, condensed matter physics, statistical mechanics, nonlinear dynamics, and soliton theory, as well as stochastic processes and Bardeen-Cooper-Schrieffer–type theories." (Science, Feb 2019, Vol. 363, Issue 6427, pp. 623-626). Others might even look into an earlier textbook publication: "Supersymmetry in Quantum Mechanics" (2001, Cooper, Khare and Sukhatme). Earlier than that are the pedagogic expositions in the European Journal of Physics: Simple Supersymmetry I & II (Stedman, Vol. 6, N.4, pp.217-231).



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    8. This paper looks interesting. It is the case that SUSY potentials of superfields can model many things. SUSY is one way to model a transition between a system with topological order to one with symmetry protected states.

      This paper though seems to be flawed in the format of the pdf, for it is nothing but blanks after 6 pages or so.

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    9. Lawrence Crowell,

      Super theory has nothing to do with quantum superposition or entanglement! See: https://en.wikipedia.org/wiki/Supergeometry

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  20. Dr. Hossenfelder,

    You write:
    "I blame this confusion on the many philosophers, notably Popper and Lakatos, who have gone one about the importance of predictions, but never clearly said that it’s not a scientific criterion.
    ...
    A closely related confusion is the idea that scientists should not update a theory when new data comes in. This can also be traced back to Popper & Co who proclaimed that it is bad scientific practice. But of course a good scientist updates their theory when they get new data. That, after all, is the essence of the scientific method! You update your theory so that it has the highest explanatory power. In practice, this usually means recalibrating free parameters if new information is available.


    I don't think you're giving a fair reading to Lakatos if that is how you interpret him. Either that, or you're unfairly lumping him in with others. Lakatos himself would characterize the position you are rightly criticizing as "naive falsificationism."

    Lakatos wrote the following about his methodology of scientific research programmes, in his eponymous text on page 51:

    A 'model' is a set of initial conditions (possibly together with some of the observational theories) which one knows is bound to be replaced during the further development of the programme, and one even knows, more or less, how. This shows once more how irrelevant 'refutations' of any specific variant are in a research programme: their existence is fully expected.
    (bolding mine)

    There is a lot more of course, but I strongly suggest you take another look at Lakatos. From what I've read of him and what I've read of what you've written in this blog and your book, you seem to be in agreement. Obviously you'd know better than I about the extent to which your views diverge, but I don't think you're giving Lakatos a charitable read if what you wrote above is your summary of his position.

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    1. I am not talking about falsification, on what Lakatos, for all I can tell, had a reasonable position. My biggest problem with his approach is the imo confusing and superfluous notion of "research programs". I am here talking about the need to make a prediction for something that has not yet been observed.

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  21. Quick typo. Please remove this comment when you fix the article!

    Now: "who have gone one about"
    Fix: "who have gone on about"

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  22. The world, it seems, is filled with people who mistakenly think that a theory which is less complex than other theories is always the more preferable theory. That may be true if both theories being compared are incorrect, and if the comparer prefers less complex theories. If one of the theories being compared is correct and the others are incorrect, their relative complexity is immaterial, as is the comparer's preference for Occam's razor.

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  23. You means that you know what the good science is. Well, the problem is to express this knowledge formally. It used to refer to as a demarcation problem. However, no one was able to do it so far. Say, in your current proposal, I guess, it is impossible to formalize "good explanation". At the end, there is no agreement between physicists to this end.

    We can say whether science was good or bad when we look back into the history, then it is clear for us who was right and who gone mad. The real problem is to take the current state of the science and to say what a theory will be counted as a good theory say in fifty years. I am afraid that there is no method to achieve this goal. At least no one so far has found such a method.

    P.S. I have recently read Hilbert's address to the Society of German Natural Scientists and Physicians (1930):

    Wir müssen wissen,
    Wir werden wissen.

    By the way, there is 4 minutes radio address available where one can hear Hilbert today

    https://www.maa.org/press/periodicals/convergence/david-hilberts-radio-address-introduction

    The question is however what does it mean "Wir werden wissen". It seems that there is no answer either.

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    1. No, I do not claim to know what good science is. I instead propose a scientifically reasonable definition for a good explanation: Fit a lot of data with few assumptions. No, it is not impossible to formalize it or quantify it. This is well possible, we are just not doing it.

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    2. Well, I should say it is well possible in fields that rely on mathematical modelling.

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  24. "Naive falsificationism takes it for granted that the laws of nature are manifest and not hidden beneath disturbances of considerable magnitude. Empiricism takes it for granted that sense experience is a better mirror of the world than pure thought. Praise of argument takes it for granted that the artifices of Reason give better results than the unchecked play of our emotions. Such assumptions may be perfectly plausible and even true. Still, one should occasionally put them to a test. Putting them to a test means that we stop using the methodology associated with them, start doing science in a different way and see what happens."
    https://en.wikiquote.org/wiki/Paul_Karl_Feyerabend

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  25. This may in part depend upon what is meant by prediction. Prediction mean to say something, dictus, about a state of affairs before they happen. Now the classical case is Halley’s comet. Halley predicted the occurrence of this comet by his namesake in 1705 to occur in 1758 within a day and in a certain region of sky. He was very close to the mark, and this event sort of caps the so-called age of enlightenment. This was a prediction of an event based on Newtonian mechanics that supplanted the prophetic claims of religion. Prophesies are vague and murky with no clear time sense, whereas Halley stated a certain event would occur within a narrow window of time in an explicit way.

    Interestingly Darwin noted a species of orchid that had a long neck and wrote there must be some insect of bird with a long proboscis or beak that can reach the nectar and are then selected to pollenate this orchid. In the 1980s a continuous monitoring of this flower by a camera revealed that a moth indeed served this role. This was not a prediction of a specific event in the future, but rather that an observed state of affairs with some system implied there was some other component as yet not found. This is not quite the same as a prediction.

    Lamb showed there is a resonance in the microwave frequency with an electron in an atom. This is a correction to the g-factor and renormalization of energy. This might be compared to a prediction, but it is more of a statement, “if you do A then you will observe or measure B.” This is then again different and a different meaning to the word prediction. Halley predicted a specific event, which is true to the meaning of the word. Darwin said a state of affairs already exists and Lamb said that if one tweaks a system in a certain way that it will respond in a calculated manner.

    In what sense does a theory predict versus explain? In general, the two are coupled. I see no clear division between the two. Halley predicted the appearance of a comet according to an orbit understood by Newtonian mechanics. In the case of Darwin and Lamb again they both claimed a researcher will observe some state of affairs, with Darwin it already existed and with Lamb it occurs when the experimenter makes a tweak, and these are explained by a theory, With Darwin that is natural selection and with Lamb it is QED.

    Pure prediction of course is insufficient. In the case of the stock values, for those who were given the right guess a repeat of this will select an ever narrower set of those given the right prediction. With science this would not happen. That might be one way to separate what is meant by pure prediction and an explanatory system that may have some prediction.

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  26. Scientists are losing the argument for climate change because it has become a hugely political issue and unlike the current pandemic we're going through, a chronic one.

    If they won the argument it would have huge ramifications for the global economy which perhaps is one reason why people are lining up along political faultlines. Given that the issue isn't going to go away it suggests that scientists may have to learn political and media fighting skills which might be a little uncomfortable for those of us that prefer sitting on fences or studying change rather creating change.

    What is it with physicists and philosophers - I mean is it part of physicists etiquette to mock philosophers? Is it studied in graduate school? Feynman, Susskind, Hawking were at it as well, and I'm sure there are many more. Why not pick on archaeologists for a change? When many physicists don't understand mathematicians, and when many mathematicians don't understand physicists, I'm not surprised philosophers (and many other people besides) kind of move onto other more intelligible topics, which aren't (in respectable cases), any the less intellectually demanding.





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  27. Predictions may be like democracy as Churchill said, the worst system except for the other ones. Every time there is research that falls flat on its face they start knocking predictions and calling critics the Popperazzi. Perhaps they are more like the Pooperazzi as party poopers. You were at that workshop in Germany, it seemed to be more like an intervention with physicists about string theory and the multiverse.Since then there is nothing to show from their time of probation by the Popperazzi. Would another workshop be kinder today?

    If there are successful scientific achievements that didn't use testable predictions then perhaps you can name them. I didn't see any in your book, just things that didn't work like looking for beauty. It just seems that those ideas that didn't follow a testable path end up as nothing. Even if they weren't strictly made with tests they still need to be tested at the end, otherwise they are not distinguishable from fiction at all. Dirac was said to have jumped to the right relativistic equation in quantum mechanics, but then it passed the tests. It starts to sound like one of those courses that doesn't have exams at the end, so as not to make the students feel bad.

    Popper covered these kinds of situations, he said that people were free to work on wild goose chases as long as they don't call it science. Sometimes they do catch geese after all, blind luck can always happen but why claim it is some kind of method after the fact?

    I can see why people at the workshop you were in, like Sean Carroll, don't like falsification. It might cut off interesting areas of research prematurely. But no matter how many sow's ears they work on they never seem to come up with the silk purses, if I can use an old expression. When they get the last laugh on Popper I'll believe it then.

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  28. In James Geick's biography "Newton" he says that Newton tested his orbital mechanics methods against thousands of astronomical observations from many observatories. I gather from this post that from a strict etymological point of view those were not predictions, but I tend to lump them with predictions in this way: Newton was, at least in his own mind, predicting that his theories were going to explain each set of data (and those predictions were fulfilled).

    Retrodictions have the advantage that the calculations will be more thoroughly error-checked. I have read that Einstein made some errors in his calculation of the precession of Mercury before getting the correct result. So predictions are harder, especially about the future.

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  29. Perhaps it would be good to describe what prediction is meant.

    Examples of "predictions":

    1. The weekly astrological column in many newspapers.
    2. The trajectory of the Pioneer spacecraft.
    3. The evolutionary path that led from dinosaurs to birds.
    4. Who is going to win the November elections based on public opinion polls.
    5. What is the weather tomorrow?
    6. What is the average global temperature anomaly in 2040?
    7. What is the growing season in Monmouth County, New Jersey, in 2040?
    8. Superpartners of known particles will not be seen even in the next-generation collider.

    etc., etc.

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  30. I think I disagree with you that predictions are overrated. However, I agree with you that one way of judging a theory is by its ability to explain observations. However, if you confront me with the binary choice of judging a theory by what it explains or by what it predicts, then I would beg to do this on a case by case basis. Likewise, if I have to judge a person (or philosopher) on what they believe about a theory, then I would be in a similar position. Wikipedia indicates that there are a large number of phenomena that have yet to be explained ("List of unsolved problems in physics"). These indicate that our theories are not complete and are in need of improvement. How should we go about improving our theories so that they are more complete and can explain more of these unexplained phenomena? One way is to identify testable predictions and then look for them. This approach seems to have guided the building of the LHC to look for the Higgs boson (standard model); the launching of COBE, WMAP & Planck satellites to study the fluctuations in the CMB (inflation); the building of LIGO to look for gravitational waves (general relativity), and so on. Fortunately, these experiments were successful in confirming their predictions. Before confirmation, the predictions were extremely important to the theories, and possibly overrated. After confirmation, the predictions became underrated and merely something else the theories explained.

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    1. It does not matter if you "disagree" if you have no argument against mine. I have explained why relying on predictions is nonsense. You cannot just say "I disagree" and hope that my examples for how it can badly go wrong will magically disappear. What is it with you people that you are so utterly unable to lead an argument?

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    2. Precisely the hallmark of stagnation in fundamental Science(what is happening now) is the lack of empirically validated predictions, and that reason is the underlying topic in Stacy McGaugh article(Predictive power in science isn’t everything. It’s the only thing.)and that had been the recurrent topic of many of Sabine Hossenfelder articles. Shifting the emphasis to "explanation power" kind of belittle the damaging effects of the lack of empirically validated predictions in fundamental Physics.
      That is why now more than in any other time "a priori predictions must necessarily remain the gold standard in science".

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  31. Are predictions any different than betting on a horse race? To me they are the same thing. If you know something about it then maybe your bet will pay off. I you are like most people that horses are pretty much stranger beasts that people ride to bet on. Then the bet is a waste of money. When I think about a scientific theory, and its predictions. I remind my self that after every race the wining horses are tested to see if any cheating is going on.

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  32. Seems to me you need some new theory, akin to Information Theory, so you can compute the ratio of Information content required by the Theory to the Information content of what is explained.

    Kind of like, we can take N points of a function and fit an Nth degree polynomial to them, but the equation takes as much information as the original data. (Maybe More).

    But that would be more difficult to quantify with some theories, like Darwin's original evolution or psychological theories. How do we quantify the informational content of "Survival of the Fittest"?

    In another way, I'd say a successful theory is like a compression algorithm: Representing a LOT of information in far fewer bits than the raw data. The theory of gravity takes a few measurements and explains all the positions of an orbit. Or a missile trajectory.

    Darwin's theory has "explanatory power" because the information content of his book, which we can measure, is microscopic in comparison to the information it explains.


    In another way,

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    1. Dr Castaldo,

      Information theory is already a theory, so, sorry, I don't get the point. Why should physicists reinvent the wheel?

      "But that would be more difficult to quantify with some theories, like Darwin's original evolution or psychological theories. How do we quantify the informational content of "Survival of the Fittest"?"

      Yes, as I said above in response to someone else, of course you can only quantify the explanatory power of a theory that is quantitative to begin with. For Darwinian evolution you'd first have to go and develop a mathematical model for it and then measure its ability to explain observation. I do not see any reason why this should not be possible, but arguably no one has done it.

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    2. Dr Hossenfelder; yes, I understand Information Theory.

      As the second part of your answer details, it is inadequate to the task of quantifying the information content of MOST scientific theories; Darwinian Evolution being one I admire and believe is quantitatively scientific but based on difficult to quantify principles.

      For that reason, I say we need something akin (similar) to Information Theory, or an extension of it, to be able to quantify such things.

      Such an extension would be necessary to quantify what you are terming "Explanatory Power". Currently, your use of "Explanatory Power" is more qualitative than quantitative; you pick on the obviously correct idea that more variables or constants to explain the exact same thing will necessarily have less Explanatory Power.

      Implicitly (IMO) you are computing a ratio, the Information Content of the explained, divided by the Information Content of the Theory (of assumptions, constants and formulas involved).

      That approach can succeed when only one of the numerator or denominator are changed; obviously if the denominator grows, the fraction shrinks so Explanatory Power is diminished.

      Obviously if the numerator grows (e.g. Quantum Theory predicts the Higgs and then discovers it), Explanatory Power is increased.

      Likewise for eliminating superfluous elements of the theory, obviously the Information content of the denominator is lower, so the fraction is higher, and Explanatory Power is increased.

      That is numberless, we don't have to know how big the changes are, just the sign suffices. But this numberless approach might fail if both numerator and denominator are changed: Say we explain more by adding an additional assumption. Then it is difficult to compute whether the Explanatory Power has increased or not, because the magnitude of the changes in Information Content matter a lot.

      (It isn't always difficult: The incorporation of Genetics into Darwinian Evolution obviously (IMO) exploded the Explanatory Power by several orders of magnitude, even though it was a lot of new information in the denominator.)

      Information Theory, as it stands, is not up to the task. We need something like it, or an extension of it, to turn “Explanatory Power” into a quantifiable and measurable metric.

      One approach I have mentioned is Compression; in theory there is a maximum lossless compression factor for any given document based on its inherent Information Content. We obviously cannot losslessly compress a paper to one bit. (decoding dictionaries count as part of the lossless compression.)

      We could use that as a proxy to compare the information content of written theories, by comparing the sizes of the lossless compressions of the minimal written length of each theory.

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    3. I'm not particularly familiar with information theory, but the Akaike information criterion is a result in information theory that allows one to estimate the quality of a model taking into account how well the model matches the data *and* the number of free parameters in the model. Sabine talks about assumptions rather than free parameters, so this isn't precisely what she has in mind, but similar.

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  33. Surely it's close to, if not absolutely, impossible for a theory to not make some predictions about nature that have not previously been observed, for various reasons. With GR that you mentioned, gravitational waves couldn't have been observed because we didn't have the means; bending of light because nobody had thought to look; black holes because you'd have been laughed at for suggesting it. Mercury's anomalous orbital motion was only known about because it was obvious.

    If you have an arbitrary number of data points on a graph you can always formulate some curve to fit those points, and that curve necessarily extends beyond the known data points. It's a test of how good your curve is, when new data becomes available, how well it fits your formula. As our past observations are finite, surely a new theory must similarly make predictions, and only a good theory makes accurate ones.

    Can you think of a good theory that doesn't make predictions?

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    1. Gussss,

      "Surely it's close to, if not absolutely, impossible for a theory to not make some predictions about nature that have not previously been observed"

      I have no idea why you would say something like that. It's trivial to come up with theories that make no predictions. All you have to do, as I have mentioned in my examples, is to have assumptions that were superfluous to begin with.

      "Can you think of a good theory that doesn't make predictions?"

      Any theories that were developed in the past whose predictions have meanwhile been confirmed would no longer make "predictions" today because the measurements have already been done. If you insist on predictions you must therefore be comfortable with accepting that all theories we use today could accidentally be "not good" just because by some quirk of history no one did the relevant calculation in time. Is this what you want to argue for?

      "If you have an arbitrary number of data points on a graph you can always formulate some curve to fit those points, and that curve necessarily extends beyond the known data points. It's a test of how good your curve is, when new data becomes available, how well it fits your formula. As our past observations are finite, surely a new theory must similarly make predictions, and only a good theory makes accurate ones."

      Whether the theory does or does not provide a good fit to a set of data does not depend on whether it correctly predicted parts of it. The "prediction" part is utterly unnecessary.

      Can I think of a good model that doesn't make predictions? Yes, I named one in my blogpost, epidemic models. That's because their predictive ability depends on input that itself is unpredictable, namely which lockdown measures were taken.

      It's the same for the predictions of climate models which depend on volcanic eruptions.

      People who mistakenly insist on predictability will conclude from this that the models are not scientific. Which is rubbish of course. Just because you cannot predict a volcano eruption does not mean you cannot explain its effect on climate trends. Alas, you will only be able to do that after the fact.


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    2. Thank you for your response. First of all, the reason I would "say something like that" is that I'm interested enough first to read your articles, and then to respond when I think I might have something to offer which might even add to the debate.

      You said:

      "Any theories that were developed in the past whose predictions have meanwhile been confirmed would no longer make "predictions" today because the measurements have already been done."

      Until we have total and absolute knowledge of every particle in the universe, there must at least be some measurement that hasn't been made. Surely a good theory goes beyond what we already know and illuminates the unknown.

      There's also the question of what you think a prediction is. Did GR predict the anomaly of Mercury's orbit, given that we already knew the fact but not the cause? And some predictions, such as frame dragging, only emerged from the original theory as a result of other scientists exploring its implications. Other consequences may yet still become apparent. All I'm trying to say (perhaps not clearly enough) is that any good theory must necessarily make these unforseen predictions, because we can never have absolute knowledge of the universe. Alternatively, can a theory that ONLY describes what is already known, but which has no implications about any other phenomena, even be called a theory at all? Surely you're in theistic or "turtles all the way" territory there.

      I disagree that climate and epidemic models don't make predictions. They do, but as you say, "their predictive ability depends on input that itself is unpredictable", in other words chaotic behaviour of physical systems is often too complicated to provide exact predictions. In the same way, planetary orbits are chaotic, and you can't solve the 3 body problem mathematically anyway, so in that regard GR fails too. But it still predicts planetary orbits and other stuff quite well. I'd say the theory of evolution falls into the same category. Makes good general predictions, but fails at the level of fine detail.

      Anyway, this is a very interesting subject.

      Regards

      Andrew Guthrie
      BSc Astronomy (1984)

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  34. I really enjoy these essays. I sometimes have to read them three times but come away having felt that I have gained something for my effort.

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  35. (Confused lay person speaking) - where does the ‘1919 eclipse data support general relativity’ argument fit in ? The data *weren’t* available before the theory, so...?

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  36. Sabine,

    as another criterion for the quality of a theory I am missing in your list the point of reductionism. Because a reductionist theory also covers the next lower level in the physical system and so yields an additional understanding for physics as a whole.

    Example astronomy: with Kepler’s law we could describe the motion of the planets. But with Copernicus and Newton’s we have understood WHY these rules are as they are. So, even if both theories would have had the same level of precision at the end (we know that Copernicus was in the beginning less precise than Kepler), we surely agree that the Copernicus / Newton provided at the end the better theory. Kepler did not contain any physical understanding but provided only a pure description.

    You have addressed the question of reductionism yourself several time and that was truly justified; so we should not forget this as a criterion if judging about a theory.

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    1. Hi antooneo,

      Yes, I think you are absolutely correct. However, I think that a reductionist theory is only scientifically justfied if it provides either a simpler explanation of existing data, or explains more data. In both cases it would be superior in terms of explanatory power. Again, though, a prediction is not actually necessary for this.

      Newton's insight fits very well here because the great benefit of it was that he could explain several seemingly disparate observations with the same idea.

      I don't know what you mean by "pure description", the term makes no sense to me. It seems to me that all scientific theories of nature should be "pure description". That's the purpose of science after all, to describe nature.

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    2. Hi Sabine,

      Thank you. But when you say: “That's the purpose of science after all, to describe nature”, then I clearly disagree. Description is not enough.

      Personally, I have studied physics not to describe the physical world but to understand it. But, apart from my personal feelings, there are real arguments.

      One is the technical aspect that we want to use our physical knowledge to design technical devices. To be able to do this (as an engineer) we have not only to see how something functions but to understand, why it functions in the way it does.

      For the physics itself it has had a historical development. Some time ago philosophers – the epistemologists - have argued that it does not make sense to say: we want to find the ‘truth’. Their arguments were not so bad. This was then reflected by a certain direction of positivism which says that a theory must not have invisible parameters, so any use of models is strictly rejected. And for the followers of these considerations every activity in physics was restricted to the description of processes, any attempt of understanding was seen as waste of effort.

      Werner Heisenberg followed this direction for his whole life, Einstein in the beginning of his physicals work, but later he rejected this way as erroneous. Heisenberg’s position was reflected by his way in quantum mechanics, Einstein’s in his way of relativity. For Heisenberg there was no reason to rework QM, for Einstein there would have been good reasons to rework relativity, but he didn’t.

      The bad thing with positivism (as a pure description of phenomena) is that it is not open for a continued and deeper understanding of physics. This is in (not only) my view the main reason that the development of physics is in a deadlock. Even if it should be philosophically senseless to find any deeper ‘truth’, it has turned out to be needed in a successful search for solutions.

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    3. The orbits in the Copernican model were circular, that is, in no agreement with the experiments, which means wrong. A beautiful mathematical framework, yet wrong. Kepler got it right with his elliptic orbits. Much uglier, but apparently less wrong. Then came Newton wth his differential eqations and destroyed even that picture: the orbits have no particular shape, they merely reflect the superpositions of the gravity fields at a particular moment in time.

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    4. Antoneo,

      it is a common misconception that one of the purposes of physics has always been its application in engineering. This is a pretty recent approach, but most of the ground-breaking developments in the XX century have been made with no direct relation to physics and sometimes against it. Two quick examples: vacuum tube and transistor. Three smart guys at IBM were trying to build a MOSFET device based on an old Lilenfeld patent and failed. But the failed experimental device indeed had exhibited some gain and hence a bipolar juntion transistor was discovered. The guys had been smart and quickly learned how to bend physics to match their setup and subsequently won a Nobel prize.

      The role of physics is to optimize existing inventions once the principles are better understood, not to push the leading edge of engineering forward. I dare to think that the next ground-breaking invention will be made by engineers, not by scientists. And physics? Physics will surely adapt.

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    5. piotrw: Circular orbits are not "wrong", they are simpler and thus far more explanatory than epicycles. (The epicycles were not wrong, either, it is perfectly valid to consider the Earth a fixed point and devise equations for everything out there. Since the orbits are obviously calculable using the Sun as the center, the epicycles are just a translation of that: We could make epicycles just as accurate as any other method.)

      Kepler was not wrong with ellipses, but he matched the data considerably better, and the theory also matches cometary orbits.

      Newton matched the data even better, but not perfectly; he couldn't get the orbit of Mercury right, for one.

      Einstein solved that problem, but there is no ironclad reason to believe Einstein's equations are the final word, either. There are obvious problems with Einstein's assumptions about space being infinitely divisible, resulting in many infinities that make no practical sense.

      I believe it is a mistake to assume any scientific discipline is more than an increasingly accurate series of approximations.

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    6. Dear Dr Castaldo,

      My view indeed is that natural sciences are increasingly accurate series of approximations. The more facts we collect, the more we need to explain, and the more precise the explanation ultimately becomes. "Approximation" is not a derogatory word in my vocabulary; neither is the incredibly useful bunch of incompatible frameworks we collectively call physics. As it is in regular life, you have a certain budget and select the approximation you can afford. If nothing else, the required computational power is the currency.

      But if a theory predicts X and Nature prefers Y, then the theory is... wrong; sorry for being blunt. There most likely are no circular orbits in this universe, but this fact does not render Newtonian physics useless. One simply can be more wrong and usually the acceptable price for being more wrong is the inherent simplicity of the approach, which cannot be underrated. In principle, it is possible to use Special Relativity successfully for analysing car traffic. Still, the gain in accuracy can be neglected for all practical purposes, so this practice is generally avoided. And the falsified theory wins and often even outlives its successors.

      There is nothing wrong in being wrong, especially if one is able to predict how wrong one can be.

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    7. piotrw,

      I think that you are right that the relation between physical understanding and technical development also goes into the other direction. It is a mutual influence. Technical detections can be made incidentally. But as the development of the transistor shows, there was a lot of physical knowledge needed to develop transistors to the performance which they have today.

      Similar is my experience with development of radar antennas - here of phase controlled antennas. To achieve a good focal precision for them, the engineers needed physical understanding. And those engineers, who only knew the formal theory and did not have a good physical understanding behind it, in general did not find solutions and created incorrect results.

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    8. Dr. A.M. Castaldo,

      I think that progress in science is indeed more than increasingly accurate series of approximations. With Newton we have learned what the physical cause of planetary motion is. And with this we can also take the mutual gravitational influence of stars into account, which also applies for the motion of comets. This would have never been possible by the use of an increasing number of approximations. Which approximation would explain the motion of a comet?

      Einstein has then added relativistic effects to it – unfortunately in an unnecessarily complicated matter.

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    9. piotrw: I find it useless to employ a definition of "right" and "wrong" such that no theory is ever "right" and all theories are "wrong" because they are, for all we know, "just approximations".

      That renders the words "right" and "wrong" useless designations incapable of providing any distinction.

      Then to say there is nothing wrong in being wrong is just sophistry; a fallacy, it is saying 1 != 1.

      Instead of torturing the language, I will stick with the language that actually makes sense. Circular orbits is "right", it captures the essence of what planets are actually doing, in a way that epicycles do not; they are not retrograding, backing up and moving in loops, The best epicycles could do is predict position, but the paths were extremely convoluted.

      Circular orbits for Earth and the planets is sufficient to dramatically reduce the error of what stars and planets we observe in the night sky at any given time, and where we observe it in the night sky.

      Elliptical orbits reduce the error further, but that doesn't make Circular orbits "wrong".

      It is like saying every scale of weight is "wrong" because it cannot measure the weight of something down to the mass of an electron.

      That's just silly. Scales are "right" or "wrong" within their design resolution; if they only show "kilos" then they are either right or wrong when weighing various known weights.

      Theories are like that. Epicycles were "right" if all one was trying to do was predict the trace position of a handful of lights in the sky.



      Delete
    10. antooneo: Which approximation would explain the motion of a comet?

      You are kidding, right? An ellipse! Just like the planetary orbits! See Halley's Comet Orbit.

      antooneo: Einstein has then added relativistic effects to it – unfortunately in an unnecessarily complicated matter.

      If you can get identical relativistic results to Einstein equations with simpler equations, I imagine physicists might be interested in that. You should publish.

      That aside, the relativistic effects, particularly measurable on the orbit of Mercury, prove that elliptical orbits and parabolic trajectories are just very good approximations. I'm not an astronomer and have not seen any calculations of the gravitational effects of other stars on our planetary orbits; but obviously our planetary orbits might be perturbed by mutual gravitational interaction; and the comets can be initiated by collision of objects in the Kuiper Belt or Oort cloud, and terminated by intersection with a planet (sometimes violently, e.g. Comet Shoemaker-Levy 9 ended its cometary career when it bonded permanently with Jupiter in 1994).

      Delete
    11. Dr. A.M. Castaldo:

      Regarding comets: there is the class of aperiodic comets. Their path is either not elliptic or so extended that the ellipse is not observable for us. Here it does not make any sense to treat them as ellipses (approximated or not). But as soon as they are observable and their parameters can be measured, their motion can be determined by Newton’s mechanics (with additionally Einstein’s relativistic corrections).

      Yes, we you can get identical relativistic results to Einstein with simpler equations. This version is called the Lorentzian interpretation and there exists literature about it, in discussion since decades. The major simplification at Lorentz’ way is that it uses Euclidean metric rather than Minkowski’s and Riemann’s. Two names are connected to this way: Simon J. Prokhovnik and Franco Selleri, who have published a lot of books and papers about this topic.

      The two versions base originally on a different interpretation of the Michelson Morley experiment. Lorentz has shown that the null result of the experiment was caused by a contraction of the apparatus in motion. This followed from the contraction of fields in motion, known at that time as a property of Maxwell’s theory. Starting from this – and the meanwhile known oscillation in elementary particles – also objects like the MM apparatus contract at motion and the dilation of periodic processes follow. The mathematical treatment is classical and simple. Einstein on the other hand insisted in the assumption that the speed of light is constant in any frame independent of its motion. In order to solve now the summation problem, Einstein was forced to invent his known space-time using the metrics mentioned above.

      Why is Lorentz not accepted by the physical majority? This is to my knowledge a cultural phenomenon.

      Delete
  37. You write: "If I have a scientific theory, it is either a good description of nature, or it is not." Gleason's Theorem implies that there is no quantum reality!

    ReplyDelete
  38. We read above: "Many non-physicists ridicule hypotheses like supersymmetry...The problem with these models is that they have assumptions that were entirely unnecessary to explain any data to begin with." That is an interesting sentence, as I have yet to encounter 'ridicule' when 'describing' Supersymmetry to a non-physicist. Going back to 1985, we read: "the standard concepts of quantum field theory allow for Supersymmetry without any further assumptions" and "the no-go theorems imply that supersymmetry and supergravity are the only possibilities for unification within the framework of quantum field theory (page 47, Sohnius, Introducing Supersymmetry, Physics Reports). In the rare instance when I have been called upon to describe Supersymmetry to a layman, it is best to follow an historical path which allows one to understand why the "theory" was developed in the first place.

    ReplyDelete
  39. This is a beautiful article, I mean the argument is excellent.
    Thanks Sabine, for your wonderful blog! ;-)

    ReplyDelete
  40. Predictions are part of a good theory, but not the only thing. Luck, hard work, enthusiasm, connections, money, good science are also parts of a good theory.

    ReplyDelete
    Replies
    1. I just explained that predictions are not a necessary part of a good theory. What about my explanation is it that you did not understand?

      Delete
  41. Popper has not said the last thing about what science is, and you are making excellent distinctions. But somehow I think you are fighting the wrong war here. In a situation where string theory is dominant and the history of that theory (among their things) is
    A. hoping to find evidence fore super symmetry in CERN (and having not done so, demand a CERN 2 and then a CERN 3 and it is to be foreseen the claim will at the end be that you need the energy present at the Big Bang to see the super symmetry.
    B. The next claim is that black holes can explained by string theory.
    C. And ultimately some string theorists claim that the assumption of several dimension can only be explained by the multiverse, the safe place, where you cannot be proven wrong. This place is, I think, is also outside science. This is the real war to be fought now.

    Paul Steinhardt, one of the founders of inflation, now calls inflation a fixer and claims that this theory is not scientific, because it can prove everything and therefore nothing. And also is this theory driven to the multiverse, not science.

    Hugh Everetts Many World theory from 1957 is now having a revival with (among others) Sean Carroll. Based on QM everything is in a superposition including the observer. I like Sean Carroll’s attempt to somehow getting rid of the problem with the measurement, but there is no possibility for the many worlds to communicate - also protected against being proven wrong.

    I wonder, if it’s because we are living in a partly post factual time, that the audience to such unscientific theories is that big.

    ReplyDelete
    Replies
    1. You seem to be saying that I should not say what I think is correct because it could be exploited by people who you dislike. I do not think this is a good way of arguing.

      Delete
    2. This is not about people I dislike. My main argument is that theories, which ultimately end up in multiverse/many worlds, are not scientific, because they cannot be proven wrong. Do you agree with this argument?

      Delete
    3. The Many World Interpretation can easily be falsified. All you need to do is demonstrate decoherence in a well isolated system that happens faster than what standard unitary quantum mechanics predicts. If there is a fundamental collapse and not just an effective collapse due to entanglement with environmental degrees of freedom that we're not monitoring, then that disproves the MWI. However this would not disprove that a multiverse exists. So, while one cannot prove wrong the idea that a multiverse of some sort exists, the MWI is a proper scientific theory that can be falsified.

      Delete
    4. These theories, as I said, are unscientific because they contain unnecessary assumptions. The the unnecessary assumptions have the *consequence* that (some aspects of) the theories cannot be proved wrong.

      You didn't ask that but because people constantly misunderstand that, so let me add that the unnecessary assumption is that the unobservable worlds exist.

      Delete
    5. Count,

      What you say is that standard quantum mechanics can be falsified, which is correct. What you say has nothing to do with many worlds in particular. Many worlds has a superfluous assumption which is that "unobservable measurement outcomes exist". This assumption is untestable and unfalsifiable. It is also unnecessary, which is what makes it unscientific.

      Delete
    6. Thank you for your clear answer, Sabine.

      Delete
    7. "the unnecessary assumption is that the unobservable worlds exist"

      Surely it's a very necessary assumption of the 'Many Worlds Hypothesis' that they actually exist. Then you say "Many worlds has a superfluous assumption which is that unobservable measurement outcomes exist". If they do exist then they must be directly observable somewhere, the question is whether they will have an indirectly observable consequence in our universe, such as for example the idea that the CMB can hold the imprint of events in parallel universes.

      Regards

      Andrew

      Delete
    8. > Many worlds has a superfluous assumption which is that "unobservable measurement outcomes
      > exist". This assumption is untestable and unfalsifiable. It is also unnecessary, which is what
      > makes it unscientific.

      OMG. You repeat your thesis of:
      http://backreaction.blogspot.com/2019/07/why-multiverse-is-religion-not-science.html

      In the comment section first I in reasonable and then Mitchell in a very short but really striking comment told why you are wrong. And then Jaques Distler took his time to explain with really absolutely brilliant arguments why your argument is clearly absurd.
      I can understand that it is difficult for you to admit that you have been writing nonsense in the heat of the discussion at the time. But that you never reconsidered in the 10 months that elapsed since you wrote your blog is really sad. You do not have to write "I was wrong"! Just do not repeat this nonsense again and again. PLEASE reread the comments and think about them.

      Delete
    9. Gusss,

      "If they do exist then they must be directly observable somewhere, the question is whether they will have an indirectly observable consequence in our universe, such as for example the idea that the CMB can hold the imprint of events in parallel universes."

      You are confusing many worlds with eternal inflation. The other worlds in many worlds are by construction what we do not observe, hence assuming they "exist" is superfluous to explain anything we do observe.

      Delete
    10. Franzi,

      Yes, I remember very well that some people are unable to comphrehend a very simple and of course entirely correct argument that demonstrates what they believe in is scientific rubbish. If you still do not understand it, then maybe can you tell us what you think is wrong about it? Do you still not understand that it is superfluous to assume that something "exists" if you cannot observe it, because that seems to be Distler's difficulty.

      Delete
    11. What's wrong about your blog post in July is that you did not undertand that unobservable consequences of a scientic theory are still scientific, and
      clearly not "religous".
      Jacque pointed out that proton number violation is a necessary consequence of the standard model, but that it
      proceeds at an utterly (in principle) unobservable rate within the SM.
      Please take at least a day to think about his point and
      then tell me: did he make a religous statement?

      Delete
    12. Franzi,

      "What's wrong about your blog post in July is that you did not undertand that unobservable consequences of a scientic theory are still scientific, and
      clearly not "religous"."


      Seriously? You come here to complain I am supposedly "wrong" and did not even understand what I said in the first place? After I explained it extensively in my blogpost, in my video, and repeated it half a dozen times in response to Distler? After all that, you still did not understand it?

      But happy to repeat it once again: It is unscientific to make superfluous assumptions. The assumption in question is the existence of something that cannot be observed, which is always unnecessary to explain what can be observed. I am not talking about "consequences" of anything, I am talking about assumptions. Assumptions, not consequences. Assuming the existence of worlds/universes other than our own is unscientific because it is unnecessary to explain anything we observed. It is unnecessary and therefore unscientific exactly in the same way that postulating the existence of god is.

      Delete
    13. But removing unobserved outcomes from the theory would violate unitary time evolution. So, if we consider a closed system of observer plus the system the observer is measuring then the physical state of that system evolves in a way such that it contains all the information about all the possible measurement outcomes.

      If no real collapse happens, so the collapse we observe in practice is only an effective collapse due to decoherence, then you can in principle verify the existence of different measurement outcomes for another observer who is locked up in an isolated box, who is going measurements that are totally contained in that box.

      So, if the experimenter in the box measures the z-component of a spin that was initially polarized in the x-direction, then the state of the box and its contents will be a pure state describing the superposition of the two measurement outcomes and not a mixed state.

      That in practice we cannot see the difference doesn't mean that the difference doesn't exist. For the difference to not exist, would require a violation of unitary time evolution of completely closed systems.

      Delete
    14. >It is unscientific to make superfluous assumptions. The assumption in question is the existence >of something that cannot be observed, which is always unnecessary to explain what can be >observed.

      Yes your blog entry last July started with this thesis. I (and I believe al reasonable physicists) agree on this thesis!

      > I am not talking about "consequences" of anything,

      You were in your July posting! When you noticed that most of the times (e.g. in QM and eternal inflation)
      the multiverse is not an assumption but claimed to be a consequence of the theory, instead of correcting the first thesis, in order to uphold it you formulated the following wrong thesis, quote:

      >Third. They’ll claim the existence of the multiverse is a prediction of their theory.
      >It’s not. That’s just wrong. Just because you can write down a theory for something, doesn’t mean >it exists*. We determine that something exists, in the scientific sense, if it is useful to >describe observation. That’s exactly what the multiverse is not.

      THIS is the thesis that I, Mitchell and Jacques vehemently opposed.

      I replace "multiverse" with "proton decay in the SM":
      >They’ll claim the existence of [proton decay in the SM] is a prediction of their theory [the SM].
      >It’s not. That’s just wrong. Just because you can write down a theory for something, doesn’t mean >it exists*. We determine that something exists, in the scientific sense, if it is useful to >describe observation. That’s exactly what the [proton decay in the SM] is not.

      Your thesis in this form, (the one Jacques objected to) is wrong, exactly because the last sentence is correct. Proton decay might well not exist at all, but it's predicted existence in the SM obviously is a scientific and not a religous statement.

      I ask again: is Jacques' effective statement: "the existence of [proton decay in the SM] is a prediction of ... [the SM]" a religous or scientific statement?

      Delete
    15. Franzi,

      "You were in your July posting! When you noticed that most of the times (e.g. in QM and eternal inflation)
      the multiverse is not an assumption but claimed to be a consequence of the theory, instead of correcting the first thesis, in order to uphold it you formulated the following wrong thesis, quote:


      Uh, let me see. I supposedly did not "notice" that most physicists who believe in the existence of the multiverse claim that it is a consequence of their theory until someone on my blog educated me about it. Except that I wrote a whole chapter in my book explaining exactly this already in 2015. So much for your idiotic, hostile, condescending and wrong claim that this was news to me. I think you owe me an apology.

      ">Third. They’ll claim the existence of the multiverse is a prediction of their theory.
      >It’s not. That’s just wrong. Just because you can write down a theory for something, doesn’t mean >it exists*. We determine that something exists, in the scientific sense, if it is useful to >describe observation. That’s exactly what the multiverse is not.

      THIS is the thesis that I, Mitchell and Jacques vehemently opposed."


      Yes, I know that you are "opposed" to it. But that doesn't make it wrong. It just means that you dislike what is a trivial conclusion from a logically entirely correct argument.

      As to proton decay. To say the obvious, proton decay is a process. It is observable only during limited periods of time. That's why yo one in their right mind says "it exists". Normal people say "it happens" which you can read to mean "exists during a certain period of time". Without this information added, speaking of the "existence" of a process makes no sense. In short, Distler's word game simply produces a meaningless statement. This should be obvious upon reading it. I challenge anyone to make sense of this garble.

      Having said that, the reason that many physicists would say proton decay is a scientific prediction is that it may one day become observable. I am sure that some philosophers would quibble with that because one can question whether at the time it happens there will be anything or anyone around to do the observing. However, let us leave this subtlety aside.

      You then seem to want to claim that the "existence of the multiverse" is a scientific prediction because it might one day lead to observable consequences, just like proton decay, you see. I am afraid I have to inform you that this just is not so.

      Hope this clarifies it.

      Delete
    16. @Sabine
      >I supposedly did not "notice" that most physicists who believe in the existence of the multiverse >claim that it is a consequence of their theory

      No! I wrote you DID notice, quote:
      >> When you noticed that most of the times (e.g. in QM and eternal inflation)
      >> the multiverse is not an assumption but claimed to be a consequence of the theory

      > I think you owe me an apology.

      I think it is the opposite. I did not insult you, but you did, calling me an "idiot", just because you did not read carefully what I wrote.

      > That's why yo one in their right mind says "it exists". Normal people say "it happens" which you > can read to mean "exists during a certain period of time". Without this information added,
      > speaking of the "existence" of a process makes no sense.

      Oh come on, you wrote "exists in a scientific sense": "proton decay in the standard model" exists in a scientific, all right! You "added the information" to make sense of Jacques' counter example with no problem.

      > the reason that many physicists would say proton decay is a scientific prediction is that it may > one day become observable.

      Jacques did not use the example of "proton decay" but "proton decay with the rate predcited by the SM"! And the latter will NEVER be observed directly, i.e. with the protons that are around us at room temperature. THIS was his point.

      Different point. Doesn't your thesis:

      >It is unscientific to make superfluous assumptions. The assumption in question is the existence >of something that cannot be observed, which is always unnecessary to explain what can be >observed.

      the one I agree with, apply to the multiverse of string theory?

      Delete
    17. Franzi,

      You claimed that I supposedly only "noticed" physicists claim that the multiverse is a consequence of their mathematics after commenters on my last year's blogpost alerted me to it. This is wrong and this is easy to prove. I did not call you an idiot, I called your comment idiotic and that's what it is.

      Look "Franzi". I make a lot of effort by formulating clear and correct arguments. What I write about on this blog are usually (though not always, of course) topics that I have worked on and thought about for years. Then I have do endure commenters, more often pseudonymous cowards who won't put their name behind their nonsense, who think I should care that they dislike my conclusions and therefore insist the argument must be wrong. It's pathetic and it's tiresome and it's wasting my time.

      "You "added the information" to make sense of Jacques' counter example with no problem."

      Yes, I was, very very generous in trying to make some sense of complete rubbish. But you missed the point. It is trivially possible to make any statement meaningless by randomly replacing words, which is why Distler's "argument" is not an argument, it's just the last resort of someone who hopefully realized he is wrong.

      In case you still did not understand this. Take the statement "A person whose height exceeds 6 feet is tall." Now replace "person" with "birthday". You get nonsense because "tall" is not an attribute that makes sense in this case.

      I have been exceedingly clear in defining my terms. You have not, and neither has Distler, yet that is apparently my fault.

      "Jacques did not use the example of "proton decay" but "proton decay with the rate predcited by the SM"! And the latter will NEVER be observed directly, i.e. with the protons that are around us at room temperature. THIS was his point."

      He clearly thought that what he wrote has something to do with my demonstratation that assuming the existence of the multiverse is unscientific. I just explained that this is not so.

      ">It is unscientific to make superfluous assumptions. The assumption in question is the existence >of something that cannot be observed, which is always unnecessary to explain what can be >observed.

      the one I agree with, apply to the multiverse of string theory?"


      This statement is only meaningful if you define what it means for something to "exist" in the scientific way, which I have done above. It follows that any type of multiverse currently considered is unscientific. You can't have your cake and eat it too. Just in case that was too complicated: Yes, of course it applies to the multiverse of string theory.

      Delete
    18. >You claimed that I supposedly only "noticed" physicists claim that the multiverse is a >consequence of their mathematics after commenters on my last year's blogpost alerted me to it.

      No, I clearly did not imply that you only noticed only when commenters alerted you but rather that you noticed when you wrote the original post.
      I wrote, quote:

      >>When you noticed that most of the times (e.g. in QM and eternal inflation)
      >>the multiverse is not an assumption but claimed to be a consequence of the theory, instead of >>correcting the first thesis, in order to uphold it you formulated the following wrong thesis, >>quote:

      and then follows a quote from your original blog post. This implies that you noticed when you were still writing the post and not only when the comments came in.

      "What you are saying is idiotic" is an insult. Instead of an excuse I get another insult "pseudonymous coward".

      My pseudonym does not give me any right to treat you any different than if we would talk face to face, i.e. with respectfully formulated arguments. But this cuts both ways. And Jacques even used his clear name, but this
      did not keep you from calling his arguments "complete rubbish". Do you find this respectful?

      Delete
    19. Franzi,

      "No, I clearly did not imply that you only noticed only when commenters alerted you but rather that you noticed when you wrote the original post.
      I wrote,"


      My apologies, then, I misunderstood this. You did not claim that commenters on my blog alerted me in July 2019 that physicists think the multiverse is a consequence of the mathematics of their theory, but merely that it occurred to me when I was writing the blogpost.

      Both is equally idiotic, as you hopefully understood by now. I explained this in a book I wrote in 2015. The whole fucken reason the damned book is called "Lost in Math" is because of people like Distler who are mathematical Platonist and do not even realize that this is a belief.

      You get exactly the respect you deserve. Now excuse me, I have better things to do.

      Delete
  42. Dr. Hossenfelder,

    The discussions that occur after one of your blogs is really a great learning experience for so many of us late in life physics bloomers, thank you. I have a question and an observation; first the question but it is somewhat rhetorical, do you put little pieces of subtle humor into your blogs to see if we are really reading them? I though the reference to Occam’s Razor was very good.

    Now for the observation, Physics, in particular Theoretical Physics is a significantly different discipline than Philosophy. Therefore it seems to me that one should not be dictating process or conclusions in the other. If the point in time comes, or has come, where these two diverse disciplines are overlapping that would be a problem.

    Dark Matter and Dark Energy, yes my favorite topic, how can any possible theory make any prediction when all we know is what Dark Matter and Dark Energy does, not what they are? Standard Model, QT made some predictions that turned out to be correct, but what about all of the open questions associated with the standard model? Where are the predictions for these questions? Under a Philosophical evaluation If a theory is valid, could we not predict that this valid theory will or should predict all possible answers?

    (forgive me, I could not resist that one)

    To be perfectly honest, when I am looking at something physics related that I am trying to find an answer for, philosophical mandates are the last thing I am thinking about.

    ReplyDelete
    Replies
    1. Steve,

      Yes, I frequently make jokes, but the remark about Occam's razor wasn't one, so not sure what went wrong here.

      I don't think you can do science without philosophy. Without philosophy we wouldn't even know what science is.

      Also, it isn't my intention to "dictate conclusions" to philosophers, I am just pointing out that predictability is not a philosophical argument, it's a sociological argument. It's an argument about what humans do (or fail to do), not about the properties of scientific theories. This doesn't mean it's irrelevant or useless, but it does mean that it necessarily only a rule-of-thumb.

      As to dark energy and dark matter, how can these theories make predictions? Well, why don't you read some papers on the topic to see how it works? If you want to make a prediction with a theory, all you need to have a definition for the behavior of the elements of the theory. The question "what" they are doesn't even make sense to me. They "are" whatever is the description that fits best with observation.

      You are probably, as many people, asking if they are composed of other things, eg if they are emergent, rather than fundamental. That's what most physicist think is the case with dark matter. It may or may not be the case. And be that as it may, there is presently no observation that tells us one way or the other, so we just don't know. With dark energy there isn't even a good argument for why it should be made of something else. It might well just be a constant of nature like, say, Newton's constant, or the fine-structure constant.

      Delete
    2. "how can any possible theory make any prediction when all we know is what Dark Matter and Dark Energy does, not what they are?"

      I think because if your hypothesis is based on solid foundations of what is already known, it's unavoidable. Inventing a new particle will lead to a potential new measurement or product in a particle collider for example.

      As Professor Feynman said, "First we guess, then we compute the consequences and see what it would imply".

      https://youtu.be/b240PGCMwV0

      Regards

      Andrew

      Delete
    3. Dr. Hossenfelder,

      You did not go wrong with your Occam's Razor remark. I just found it enlightening to use a philosophical statement in a piece about philosophy going to far in physics. I should have been more clear as I do not believe that you or most physicist dictate conclusions to philosophers. Part of my understanding of your piece and the subsequent discussion is that some philosophers may be going a little too far WRT physics involvement. I was trying not to be offensive to some opinions and remarks.

      I also agree that physics needs some philosophy at times in order to keep it going in the right direction. Maybe I am wrong, but it seems to me the a large value of philosophy WRT to physics would be to help physicists understand and define the direction they are trying to go in with their work.

      Thanks Dr. Hossenfelder, I am always learning and for me that helps keep me young and moving forward.

      Delete
  43. I think there's some confusion about what "good scientific theory" means, specifically the "good" part. Is it good in the sense of explaining data (objective)? Or is it good in the sense of being worth for scientists to work on it (sociological)?

    Let's take an example of GR being invented today, so that it explains all the past observations but doesn't give any predictions. And there's an alternative theory that also explains all the past observations but also makes predictions at the cost of introducing some assumptions. In objective sense, the two theories are about the same, the GR may be even better if the assumptions introduced in the alternative are too extensive. But in the sociological sense, scientists will work on the alternative theory to make more predictions and verify the existing ones. Once the predictions are verified, the alternative theory becomes strictly better than GR because it accounts for more data (like GR vs. Newton's theory). Of course, once the new data is in, scientists may go back to GR and modify it so that it also accounts for new data and this modified GR may even have more explanatory power than the alternative theory. But it is the alternative theory that forced people to push research forward and develop new science. So, from sociological perspective, we want theories with predictions to ensure scientific progress.

    ReplyDelete
    Replies
    1. Toegut,

      In your example it is once again unnecessary that the alternative theory actually makes *predictions* for observations yet to come. The theory might also turn out to be better by explaining more already existing data. And, as I have said, just because it makes predictions and accounts for more data does not mean it is a better theory. This is only the case if it does so in a simpler way.

      "But in the sociological sense, scientists will work on the alternative theory to make more predictions and verify the existing ones. "

      Sometimes, sometimes not. This is a very sweeping claiming and it's clearly not generally correct. Scientists quite frequently work on theories to explain already existing data. Think of the lithium abundance, eg.

      Delete
  44. In 2008 psychic Sylvia Browne predicted:

    https://www.thehour.com/news/article/No-a-self-proclaimed-psychic-did-not-predict-15137409.php

    "In around 2020, a severe pneumonia-like illness will spread throughout the globe, attacking the lungs and the bronchial tubes and resisting all known treatments..."

    ReplyDelete
  45. So, in essence, science doesn't work well if theories are introduced that make too many unconfirmed predictions. Slow and steady, incremental progress using what's currently known works best.

    Other examples are Weyl's flawed gauge invariance for classical electrodynamics that had to wait for quantum mechanics where it could truly flower. And Gell Mann's Eight Fold Way that was initially successful, but was superseded by quantum chromodynamics.

    Note also that SUSY was independently discovered by different groups at around the same time. Perhaps SUSY, like Weyl's gauge invariance, is waiting to be correctly applied to some part of physical reality not yet known?

    ReplyDelete
  46. The required explanatory power needs to have certain quality and it might be hard to define it satisfactorily. To give you an example, the following "explains" EVERYTHING: In the beginning God created the heavens and the earth. Now the earth was formless and void, and darkness was over the surface of the deep. And the Spirit of God was hovering over the surface of the waters. And God said, “Let there be light,” and there was light.

    ReplyDelete
    Replies
    1. You cannot calculate the outcome of a single measurement from this, so the explanatory power is zero. I don't know what you think the difficulty is. As has been noticed before "God" is a superfluous hypothesis. That doesn't mean it's wrong, but it's unscientific.

      Delete
    2. I think this is an example of a theory that is ONLY explanatory, but makes no predictions at all. After all, how could it? You are relying on the whim of a deity for the next move. And therefore, as you say, it is unscientific.

      Stay safe

      Regards

      Andrew

      Delete
    3. Sabine Hossenfelder7:19 AM, May 07, 2020

      "That doesn't mean it's wrong, but it's unscientific. "

      As I have pointed out to you before, Dr. H., the actual claims of actual human religions are scientific and are wrong e.g.

      The universe was created - this implies the universe had a beginning, for starters, which is a scientific claim unsupported by any evidence so this belief is untenable.

      There was a human child in Bronze Age Palestine with a human mother and non-human father - this is false as well as insane. It is an empirical fact that humans in the Bronze Age had 1 human mother and 1 human father.

      etc., etc.

      The main tenets of all human religions, including belief in "God", are insane nonsense. "God" is not a superfluous hypothesis but empirically refuted insane nonsense.

      Delete
    4. @Gusssss: this is exactly my point. A theory that is completely deprived of predictive power, explains everything (or even anything, if you wish) and is nonetheless believed by many to be the ultimate truth. So, no, explanatory power is not the only important ingredient. To call it science we do need testable predictions, even wrong ones.

      Delete
  47. I beg to disagree. The explanatory power of "God" is infinite (and infinitely useless). The answer to any possible question is "That's because God wanted so" and there is no way to challenge it. Math does not have to be the language to answer the ultimate questions, this is one more hidden assumption. Moreover, the "theory" is believed to be correct by at least four orders of magnitude more people than "believe" in QFT. The only way to fight with this way of thinking is to demand testable predictions. And, as you correctly point out, there are none. I think this reductio ad absurdum shows that this time you went one step too far with relaxing the requirements.

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    1. I don't think we disagree except semantically on the God issue, but I don't consider it an explanation myself. To me it is an a pretend-explanation. A god that is omniscent and omnipotent is not understandable, and an explanation that is not understandable is not a real explanation.

      I think I agree with you, but again with a different slant, on this post about predictions. I like predictions myself (non-random, successful ones), so reading the post was like reading a bad review of a movie which I enjoyed. One can agree that they are not stictly necessary for a good theory, and are not infallible in verifying theories, without agreeing that they are over-rated, it seems to me.

      In practice, applied science and engineering, e.g. NASA putting a satellite in orbit, is largely a matter of predicting what it will take to accomplish something (so many dynes of thrust, so much tensile strength, etc.). Isn't the evolutionary purpose of intelligence to make good choices for survival, which requires predicting consequences? So I personally rate the predictive value of science very highly.

      As with a movie review, though, I can't really argue with someone else's opinion, except to say my perspective is different. (And we may be talking about different aspects of the issue.)

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    2. piotrw: The explanatory power of God is zero; to say everything happens because of X does not distinguish in any way why one thing happens and another does not not, or cannot. "Because God wanted it so" has zero information content for explaining the order we see.

      You don't need testable predictions if you have specific testable consequences; which QFT theory has. It allows some things to happen and prohibits others from happening; it matches the specific observations without matching every imaginable outcome (which the God hypothesis does.)

      Is the study of dinosaurs via fossils "testable"? No, there are no dinosaurs to test theories against. But it remains a science; there are theories that match our observations thus far, and because those theories do not match every imaginable discovery they can be refuted by newly discovered evidence that does not fit the theory.

      Astronomy in in the same boat; all we can do is observe celestial objects and devise organizing theories that match those observations without matching all possible future observations.

      You have to consider the specificity of theories, not in how much they can predict but in how much leeway they allow for additional data to fit into the theory.

      If it is infinite leeway (as in the God hypothesis) then the theory has zero explanatory value. Part of the way to judge that is to consider the evidence we already have that the theory purports to explain: How different could it be and still match the theory?

      Again, in the God hypothesis, it could be infinitely different, because God could may anything happen. Thus it tells us the amount explained is actually zero.

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  48. At the end of things is the fact as we understand it. Predictions do not prove a theory, as has be exhaustively demonstrated. In regard to dark energy and dark matter the facts as they have been measured demonstrate conclusively that there are physics phenomena we do not yet understand.
    Based on prior experience in physical measurements, calculations in several different fields suggest that there are fields. labeled dark, which if they exist have such and such characteristic. Similarly, dark matter is a name give to undetectable baryonic(perhaps) matter which would explain anomalies in observations.
    Theoretical predictions have the value of telling us what we might be looking for. Dr. Higgs and coworkers made calculations that suggested that there is a Higgs particle that should show up in a broad range of energies. It was just prediction based upon calculations consistent with measurements in quantum field theory.
    Does this prove the theory? No, but it sure supports the standard model. Proof of a physical theory may be forever beyond reach. Proof in mathematics is possible but often takes centuries effort to accomplish.

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  49. Sabine Hossenfelder is a great voice for physics. She is an outlier, but we could use many outliers.

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  50. Somebody has been in quarantine too long....Hannes Alfven had a cosmological theory that explained observations but had “zero” predictive power.

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  51. Initially, when I saw the title of this blog essay "Predictions are Overrated" I recalled a 2018 prediction: "...that loop quantum gravity predicts that spacetime continues across the center of the black hole into a new region that exists in the future and has the geometry of the interior of a white hole..." (Quantum Transfiguration of Kruskal Black Holes, Ashtekar, Olmedo and Singh, Phys. Rev. Lett. 121, 241301). Ashtekar states: “ In loop quantum gravity, the fabric of space-time has a tile-like structure, which cannot be divided beyond the smallest tile. We have shown that this is the case inside black holes and therefore there is no singularity.”

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  52. @Sabine
    > [You claimed] merely that it occurred to me when I was writing the blogpost.

    Yes. But I did NOT claim (nor did I intend to make such a ludicrous insinuation) that it occured to you FOR THE FIRST TIME when you were writing the blogpost. Therefore your insults and use of strong language have no basis in what I wrote.

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    1. Franzi,

      Oh, I see, my bad. You did not bombastically proclaim that the little dumb German only recently understood the entirely obvious point that physicists believe in the multiverse because they mistakenly think its existence follows from their mathematics. Because that would have been entirely idiotic indeed, seeing that she wrote a book about this that was published years ago. You merely mentioned for no particular reason that it occurred to me again and not for the first time when I wrote a blogpost last year. I am glad we clarified this. I am deeply sorry for this misunderstanding and apologize for having called your comment idiotic.

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  53. Taking epidemiology as an example - when the report of first death from covid-19 in California got pushed up by a month - the models that assumed the prevailing R0 and mortality rate are still assumed correct.

    If they had been held to falsifiability and prediction they wouldn't have the wiggle room. If you assume a model and rate of spread and mortality rate then you can't get away from predicting earliest cases.

    Making excuses now and holding on to same R0 and CFR is like trying to invent inflation to account for spread of universe while not being able to explain the temperature uniformity.

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  54. Amusing to read words by Physicist Leon Brillouin (1970):
    "The value of a scientific theory lies in its ability to predict." (Relativity Reexamined, Introduction, Page One, Line One). I say amusing because the book is evidence that even a great physicist such as Brillouin can be misled by holding on to certain beliefs (read the book). Brillouin writes: "an isotropic Euclidean space with a variable light-velocity should be the model closest to physical experimental physical conditions."
    (Schwarzschild solution, page 95).

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  55. You criticize philosophers (of sciecne)
    but the irony is you wrote and posted a philosophy of science essay.

    https://medium.com/science-and-philosophy/no-predictions-are-not-overrated-on-some-scientists-strange-attitude-toward-philosophy-60dfd5c2cb83

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    1. I do not criticize philosophers of science. I criticize those who apply their methods incorrectly. Of course this blogpost is about the philosophy of science.

      Massimo's piece is very disappointing. I'll write to him.

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  56. That’s quite a strawperson.

    If you blame the fact that people mistakenly think that a theory that makes correct predictions is a good theory on Popper and Lakatos, you need to reread Popper and Lakatos.

    Popper held that it was impossible to show that a theory was good or probable based on the theory being confirmed by evidence. He cited Hume’s critique of inductive logic that disputed evidentiary support as grounds for the truth of theories. For Popper, correct predictions was more of a vice than a virtue. Non-falsification of bold theories might be a better summary of Popper’s criterion.

    Popper admired bold predictions (falsifiable on that basis, not merely trivially falsifiable) for all the reasons that philosophical Bayesians do; without the theory the prediction should be utterly surprising. Eddington’s experiment was his exemplar for this. Of course science seeks good explanations, but with no element of refutability, theory choice based on explanatory power descends into relativism.

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    1. "If you blame the fact that people mistakenly think that a theory that makes correct predictions is a good theory on Popper and Lakatos, you need to reread Popper and Lakatos.

      Sure, must be my fault because I got it right and not the fault of the people who get it wrong. I just love it how you guys are all so pissed of at me for saying the obvious.

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  57. Wasn't popper only talking about demarcation and science vs pseudoscience.

    In contrast you are talking about comparing two scientific theories.

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    1. That is correct. As I explain, they were trying to address a different problem. What about what I wrote is it that you did not understand?

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  58. Surely these problems of comparing scientific theories, and the demarcation between science/pseudoscience cannot be easily disentangled.

    From what I can see, falsifiability is relevant to both problems.

    When theories contain explanations that rule out things, it is this falsifiability in the sense of knowing what you should not see that adds to explanatory power.
    Evolution: you should not see modern rabbits fossilized in the gut of a tyrannosaur, a type of prediction that you cannot test.

    Evolution works as an explanation because it also tells us why we won't see particular things.

    Many-worlds: An explanation that isn't and explanation at all. It rides on the coat-tails of the success of QM by stating at the outset the alternate universes always come into existence in just the right way to always reproduce the results predicted by QM.
    Thereafter proponents wax on as to its explanatory power as all prediction 'hits' produced by QM are also attributed to MWI.
    At its core MWI is not explanatory because its founding assumption (like a religion) is that something magically occurs in 'just the right way' to always match what we see.

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  59. First of all I’m sorry if this comment reaches you twice, I had some problems with Blogger.

    Not gonna lie, I had a hard time understanding this blog post. After first reading it, I thought you meant that predictions alone were not enough, and explanatory power was needed additionally. Then you tweeted “a scientific model does not need to make predictions”, which made me reread the post.
    I think the confusion came from how I understood the word “prediction”, I thought of it as “calculating an observable that matches experiment”. What you mean, is “calculating an observable that matches an experiment first performed after the calculation”, right? And you are saying that the latter is not necessary and the former is important, right? I know that your definition makes more sense language wise, but I’m not sure if it’s always used in that sense only.

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  60. Dear Dr. Hossenfelder,

    I began reading this post expecting to disagree with you. As an industrial physicist working in product research, development, and manufacturing I live and breathe the need to develop predictive understanding of the science I use. When you wrote the statement, "The fewer assumptions and the better the fit to data, the higher the scientific value of the model," I strongly agreed with you and started thinking of your arguments being more semantic in nature since fitting data and predictions are not all that different.

    This dialogue about predicting the past, however, convinced me of your point. A theory with few assumptions that is only valid for a certain set of data reveals that something important differs between the two sets.

    Thank you for writing that is able to change people's minds.

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    1. rosie,

      Thanks so much for your comment, which really made my day! All too often it seems so pointless to even think of an argument if people just ignore it and reiterate their beliefs, so it makes me super-happy to see evidence that this isn't the only way it can be.

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  61. As a non-physicist who has cared all his life [age 73 now]about the all the questions that arise from the question, 'what is reality?', what I have found frustrating, all my life, is the habit of physicists to write and talk as if their pet beliefs are a given [the Big Bang being the biggest example].

    Arguments would be easier to follow if scientists would admit when they don't know something. No one can tell me what a quark is, but no one admits this.

    That is what drew me Lost in Math, which I thoroughly enjoyed. You obviously enjoy pointing out things that are not known. The only other physicist/mathematician/cosmologist that I know of who does this is John Barrow ['New Theories of Everything, or 'Book of Universes'] but I don't think I've seen you mention him. What do you think of Barrow?

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    1. @ Alan,

      In quantum theory there are no objects; only phenomena and theories! So, there are no "Quarks"; only quark phenomena and quark theories. Furthermore, the Standard Model-which includes "quark matter fields"-is still not mathematically well-defined. (Though its classical limit is well-defined!)

      See my website for more!

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  62. I don't see a fundamental difference between a theory matching existing data and matching data that will be retrieved in the future, a.k.a. predictions. If someone says one day "I believe the Romans set foot on America 2000 years ago" and 50 years later he is proven right, was that not a kind of prediction? Is it fundamentally different from saying "I predict that one day it will be proven the Romans set foot on America 2000 years ago"? Or from "I predict that my brand new theory will match this age old set of data better than any other"?

    The stock market example doesn't reflect the nature of predictions. It's like saying "If you shoot in all directions, you'll always hit a target. So good aiming mechanisms aren't a selling point for guns."

    "What, then, is the scientific answer for the climate change deniers? It’s that climate models explain loads of data with few assumptions. The simplest explanation for our observations is that the trends are caused by human carbon dioxide emission. It’s the hypothesis that has the highest explanatory power."

    You have to tell this to the so called political experts who maintain that "simple answers" are typical for right-wing populists whose intelligence is too low to understand the complexity of the world and to cope with diversity.

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  63. I am in agreement with this article.
    For a long time I have questioned the value placed on "probability" (= "educated guesses"). To illustrate:
    If I buy a ticket in a lottery with 1 million tickets, the supposed "probability" of me winning is 1 in 1 million (0.0001%), right? However, I will either win, or not win. Hence, my chance of winning is either 100% or zero, and the "probability" of 1 in 1 million is meaningless.

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