2. A paradigm case -- old quantum theory

3. Brown's paraconsistent approach

4. Smith's objection

5. analysis

6. Probability account

7. Conclusion

Notes

References

In the history of science, we find many cases in which scientists seem to commit to inconsistent sets of beliefs.(note 1) Moreover, many of these cases occured as part of a development we usually regard as successful. In this paper I will examine the case of old quantum theory and two interpretations of the case -- Brown's (1990 and 1993) and Smith's (1988). I also propose my own probability analysis.

2. A paradigm case -- old quantum theory

Old quantum theory is rather frequently used as a paradigm case where an inconsistent set of beliefs could succeed as a scientific theory. To discuss the details of the theory is, however, beyond the scope of this paper, so we will see only the general feature of the cases following Smith's (1988) description.

Joel Smith characterizes the inference of Planck and other physicists as follows and names "Schema A" (Smith 1988, 433).

Schema A

{H}, {C} |= B

{H}, {Q} |= D

{H}, {C} | D

{H}, {C} | B

{H}, B | ~D

{H}, B, D |= E

In the above schema, {C} stands for classical electrodynamics, {Q} stands for quantum postulates, {H} stands for uncontroversial auxiliary hypotheses. {C} and {Q} are mutually inconsistent, because {C} says that radiations are continuous, while {Q} says radiations are not continuous. B and D are intermediate consequences of these proposals.(note 2) B and D are not mutually inconsistent. E is a consequence when we use both B and D with {H}.

Planck used this sort of inference to derive his black-body radiation law (Smith 1988, 434). He used two inconsistent assumptions: one is that oscillators radiate electromagnetic energy continuously; and the other is that oscillators exhibit only certain modes of vibration.(note 3) The resulting law was accurate, but Einstein criticized the derivation because of its inconsistent assumptions and tried to derive the law without using classical electrodynamics (436), though his derivation also exploited some basic phenomena in electrodynamics (absorption, spontaneous emission and so on). This Einstein's version was accepted from other physicists as the first self consistent derivation of Planck's law (436). We will discuss Smith's explanation of the difference between Einstein and Planck later.

Another example is Bohr's correspondence principle (Smith 1988, 439-441; see also Brown 1993, 4002-404). In his model of the atom, Bohr carefully distinguished two contexts and kept classical electrodynamics and quantum postulates isolated (Brown 1993, 399). But his correspondence principle postulated isomorphism between the frequency of the electron defined in terms of quantum postulates and the frequency in the classical electrodynamical sense (Smith 1988, 440). The result he obtained from the principle was accurate. So it is true that he isolated the two inconsistent proposals, but it is also true that he used the result of classical electrodynamics in the context of quantum postulates. In a sense this is only an analogy between classical electrodynamics and quantum postulates (Brown 1993, 403).

In short, Planck, Bohr and other physicists recognized the inconsistency between the quantum postulates and classical electrodynamics, and BohrÕs solution for the situation was basically to isolate these commitments. Nevertheless they used consequences of classical electrodynamics in the context of quantum postulates. Now, the question is how we should understand their behaviors, and how we can justify them (or, maybe, whether these behaviors are justifiable at all).

3. Brown's paraconsistent approach

The answer Brown (1990, 1993) gives is that the logic the physicists used was not classical.

Most philosophers of science assume that consistency is a necessary condition for a good reasoning. There is a good reason for it. According to the classical logic, if we admit to accept A and ~A at the same time, we can derive any well formed proposition from them.(note 4) Therefore, as Popper says, "[o]nce a contradiction were admitted, all science would collapse" (Popper 1940, 410). But, of course, this conclusion is relative to the classical logic.

Schotch and Jennings (1980) devised a system of logic in which this collapse does not result even if we admit inconsistent set of sentences. This system and other similar systems are called "paraconsistent logics" (Schotch 1993). Schotch and Jennings's system is rather conservative among these alternative logics, because this system retains the classical logic as a special case. First, they introduce the notion of degree (level) of incoherence (Schotch 1993, 424; Schotch and Jennings 1980, 329). When we have a set of sentences, there are many ways to divide the set into subsets so that in each subset all sentences are mutually consistent. the degree of incoherence is the minimal necessary number of subsets in such a division. If the original set itself is already consistent, the degree of incoherence is 1 (or, when it contains only logical truths, 0). If the set includes a sentence like "A & not A," since any decomposition of the set cannot remove this contradiction, the degree of incoherence is postulated as infinite. Second, they introduce the notion of *forcing* in place of derivability in the classical sense (Schotch and Jennings 1980, 329-330). A set of sentences G forces a if and only if for every n-fold decomposition (n is the degree of incoherence) of G, a1, a2, ..., an, there is some i such that a is derivable from ai in the classical sense (330). For example, suppose a set of sentences contains one inconsistent pair of sentences ("A" and "not A"). Then the degree of incoherence is 2, and there are many ways to divide the set into two consistent subsets. We are allowed to use classical logic in each subset. Now, suppose a is derivable from one or the other subset no matter what division we choose. Then, the set *forces * a. If the set is consistent, forcing is the same as derivability in the classical sense. But, since "A" and "not A" always belong to different subsets, we can derive no conclusion from this pair of sentences. In general, forcing preserves the degree of incoherence (Schotch 1993, 424). Thus anarchy is avoided.

Brown applies this system to historical cases, especially to old quantum theory (Brown 1993). According to him, we can explain the behaviors of Bohr and other physicists if we assume that they used a paraconsistent logic of Schotch and Jennings's form. Bohr's distinction of two contexts corresponds to the decomposition of a set of sentences into two consistent subsets. Bohr's correspondence principle seems to trespass the boundary of the two contexts. Brown claims that such a move can be explained by forcing. Under forcing, a conjunction introduction (inference from ÒAÓ and ÒBÓ to ÒA & BÓ) is not a logical rule, but an empirical matter. We are not prohibited to use consequences in different contexts together, as far as the conjunction introduction preserves the degree of incoherence. We should choose, however, which conjunction to accept by ourselves. In Brown's words, "[c]onjunction introduction is not a trivial inference, but a substantial step with both risk and reward" (Brown 1933, 408). He thinks that the correspondence principle is a case of such an empirical conjunction introduction.

Smith's paper (1988) is not a direct answer to Brown (actually Smith's paper is published before Brown's papers), but he objects to the paraconsistent approach in general. He tries to show how we can understand historical cases without such a revision of logic itself.

He points out Planck's derivation was not accepted as a satisfactory one, while Einstein's is judged as "the first self-consistent derivation of Planck's law" (Smith 1988, 436). According to Smith, the difference comes from independent supports to the intermediate classical results ("B" in schema A). Einstein borrowed results from classical electrodynamics, but the results are on the existence of some phenomena, and they were supported by evidence. Smith also points out that Einstein and physicists thought that such an inconsistent theory may contain the elements of truth ( 432, 435). According to Smith, Einstein's derivation is accepted because his intermediate results seem to be a part of the "element of truth" (437), because of the independent supports. From these considerations he proceeds to make a more general claim on the nature of these seemingly inconsistent commitment. When scientists accept two inconsistent proposals (x) Mx and (Ex) ~Mx, actually they commit the existence of an inconsistency resolving theory (438-439):

(x)(Yx->Mx) & (x)(~Yx->~Mx) .

This theory is incomplete because the scientists have no idea what Yx and ~Yx stands for at that time, but at least this theory is consistent. Einstein's derivation is accepted because it is more likely to be a part of this incomplete theory than Planck's. Smith argues this consideration is also applicable to Bohr's correspondence principle (439-444). Therefore, if Smith is right, we do not have to change the logic itself.

Brown and Smith agree in most part of the historical descriptions of (seemingly) inconsistent commitments in old quantum theory. Thus the difference is mainly in the interpretation of scientists' behaviors. Each interpretation has its own strength. Brown's interpretation can explain why these scientists did not use conjunction introduction as a matter of logical rule. Smith can explain why Einstein wanted independent supports to the intermediate results. But in these points their opponent's arguments seem to work as well. As for conjunction introduction, Smith would say that even if they seem to accept A and ~A, actually they accept Y->A and ~Y->~A, and we cannot use conjunction introduction to the latter pair. As for independent support, Brown would say that conjunction introduction is an empirical matter, and this means that if we want to use two results in different contexts together, we need empirical supports to do so.

But some historical evidence seems to go against Brown's account. First, Brown may face a difficulty in explaining why these scientists talked about the "element of truth," because this evidence suggests that the scientists believed in the existence of an incomplete but consistent theory. But in this point Brown's claim is moderate one and compatible with the belief in the existence of such a theory. He is not claiming that the scientists accepted the inconsistent theory as a true theory of the world (Brown 1990, 292). Rather he claims that "[a]t a given time, the state of our scientific enterprise may be such that we can best realize our epistemic goals (explanatory power, empirical adequacy, unity, and so forth) by accepting (...) an inconsistent theory" (Brown 1990, 292). Suppose our epistemic goal is to represent a part of "element of truth." Even with this goal, it is possible that the best way to realize it at the given time is to accept an inconsistent theory. Therefore, Brown could answer as follows: "yes, the scientists' remarks show their ontological commitments to the existence of a true consistent theory. But their epistemic commitments are still paraconsistent, because it was the best way to realize a part of the true theory at that time." I am not sure whether this answer sounds plausible, but at least Brown can avoid the difficulty by this answer. Secondly, as we can see in Einstein's effort, when scientists accept an inconsistent set of proposals, they try to remove the inconsistency (Smith 1988, 436). This is unintelligible if they obey a paraconsistent logic Brown describes, because the paraconsistent logic requires them to preserve the degree of incoherence, but does not require them to *reduce *it. Thus scientists have no reason to try to remove inconsistency if they have already accepted an inconsistent theory. It seems to me this is a genuine problem for Brown's approach.(note 5) Maybe he (or Schotch and Jennings) can rework the system so that they can explain this motivation, but before they show that it is possible, we should conclude that Smith's account is a better description of scientists' way of thinking.

However, Smith's account also seems to have a difficulty. His reconstruction of the inconsistency resolving theory does not answer the original question, namely the question why scientists could use a consequence of electrodynamics in the context of quantum postulates. The inconsistency resolving theory he proposes is (x)(Yx->Mx) & (x)(~Yx->~Mx). B in schema A is derived from Mx, and D is from ~Mx. Then, if Yx is true we get B but we have no reason to assume D. If Yx is not true then we get D but we have no reason to assume B. So even in this consistent theory we are not justified to use both D and B at the same time. Smith thinks that if B has independent supports we can bridge this gap. But such a support to B will confirm Mx and Yx, and disconfirm ~Mx and ~Yx. Therefore, if B has a strong support, this means just that we lose reason to assume D.

I think it is rather easy to revise the expression of the inconsistency resolving theory to avoid the difficulty, so Smith's approach is still viable, and has advantage to Brown's. But I would rather give another account of the same situation. This is the task of the next section.

It seems to me that these historical cases allow another reading -- a probability account. In this section I will show how we can explain the behaviors of the scientists by way of subjective probability, namely probability as a degree of belief. (note 6)

First, especially when we are constructing a new theory, we cannot be sure which proposals we have now are correct, and which are not. This may result in giving low probabilities to all alternatives, but it is also possible that we give two incompatible proposals rather high probability, when we already have evidence in favor of each proposal. The only requirement they should meet is that the sum of these probabilities should not exceed unity. This means that if we give quantum postulates probability 0.3, then the probability of classical electrodynamics is equal to or less than 0.7. (This analysis shows us an interesting problem about the relationship between ÒbelievingÓ and probability. I will return this problem later.)

Do these assignments lead us to any undesirable conclusions? First, as Campbell (1981) points out, these probability statements cannot lead us to anarchy. As I mentioned before, in the classical logic, we can derive anything from an inconsistent set of premises, such as "A" and "not A," because of the conjunction introduction rule. But in probability calculus conjunction introduction is not warranted. In general, even if we know the probabilities of "A" and "B", we cannot say anything about the probability of "A & B," because it depends on the correlation of two propositions. Especially in the case of "A" and "not A" these two propositions have the strongest negative correlations and naturally "A & not A" is assigned probability zero. Therefore, the undesirable anarchy is avoided without any special device like paraconsistent logic.

Second, let us see if this probability calculus can justify the schema A, the inference used in old quantum theory.(note 7) If we posit pr(Q)=p and pr(C)=q, they are mutually inconsistent, so p+q ² 1. {H} is a well established hypothesis, so assume pr(H)=1. Then we can derive D from {Q}, thus pr(D) is equal to or larger than pr(Q) (D holds if {Q} holds, and D can hold even if {Q} does not hold). The same relation holds between {C} and B. This relation can be expressed as pr(D)= p+a , pr(B)= q+b (0²a²1-p, 0²b²1-q). If D and B have no independent supports, a and b should be very small. Now, since p and q are probabilities of mutually exclusive events, pr(D & B) is small, and by calculation, we can show pr(D & B)²a+b.(note 8) Since we assume pr(H)=1, again E is derivable from B and D. So if we posit E=pr(D & B)+c, then c²pr(E)²a+b+c.

What does this result mean in the real case? In all cases above discussed, E had independent supports (Planck's law and Bohr's results proved to be accurate), so we can assume c is not so small. This may explain why their results are not neglected (other scientists thought that these results have a part of the "element of truth"), but as we can see in Planck's case, this was not enough to accept the result. Einstein required independent supports for B, and this means to require to increase b and, in turn, the upper limit of pr(E). We can also explain why they were not satisfied with the inconsistent set of proposals. They could derive E from {Q} and {C}, but the resulting probability of E is not affected by p or q, but by a, b and c. This means that {Q} and {C} do not give support to E. The reason is obviously because {Q} and {C} are mutually exclusive.(note 9) Therefore, it was natural that physicists thought of the situation as problematic and tried to solve the inconsistency.

An advantage of this probability approach is that there is no distinction between contexts, neither in Brown's way (contexts as consistent subsets) nor Smith's way (postulated Yx and ~Yx). In this way we do not need further explanations why they could use B and D together (and this is the point I argued as a difficulty of Smith's account). At the same time we can explain why the scientists isolated {C} and {Q}. If we use {C} and {Q} together, we get pr(C &Q)=0. This result shows that we cannot accept the conjunction (for the degree of belief is 0). This is a sufficient reason to make a practical distinction of contexts. In these points, probability account seems to give a better account than either Brown's or Smith's.

There is a point, however, the paraconsistent approach can make against this probability account (Brown 1993, 397). This account leave the question of what is accepting a belief unanswered. We assumed Bohr accepted both quantum postulate and the classical electrodynamics. On the other hand, in my account, at least one of them have the probability less than 0.5 (because the sum of these values is less than unity). But can we accept something when we think it is less likely to be true than not?(note 10) Let us imagine we could ask Bohr what probability he assigned to quantum postulates and classical electrodynamics. He might give both of them high probability -- higher than 0.5. If this is the way scientists think, the probability account needs to be revised. Rather, we would need "paraconsistent probability theory" to account for scientists' way of thinking. Anyway, this needs further investigations. Another related objection to the probability account is that it is hard to assign a concrete value to each of our degrees of beliefs so that all values are consistent with one another. Can we believe that scientists' degrees of beliefs obey such a strict requirement? In my argument here, I tried to avoid assigning a concrete value to each probability, and made only qualitative (not quantitative) arguments. I hope this removes most difficulties in assigning values.

I examined the case of old quantum theory and two interpretations of it. In many aspects these two accounts explain the behaviors of the scientists well, but in some points Smith's more conservative account seems to give a better explanation. I proposed a probability account as a third option, and compared it with other accounts. I think that it is at least as plausible as Smith's and Brown's, and in some points probability account do better than these alternatives. (note 11)

(1) I will concentrate on the case of old quantum theory in this paper. For another case of inconsistency, see Norton (1993). He discusses the case of inconsistency in Newtonian gravitation theory. He argues against the paraconsistent approach.

(2) Smith uses the word "proposal" to denote a collection of statements, and uses the word "theory" for the deductive closure of statements (Smith 1988, 429 n). I will follow Smith's usages in this paper.

(3) Kuhn (1984) has a different interpretation on the way Planck understood his results. According to Kuhn, "[i]n order to derive his black-body law Planck had to subdivided the energy continuum into cells or elements of size e" (Kuhn 1984, 232). And the discontinuity was understood as the restriction on the cell size. In this interpretation there was no inconsistency in his view. If Kuhn is right, this case becomes irrelevant to the argument, though we can still use other physicists (especially Einstein and Bohr) as our paradigm cases.

(4) For example, Popper (1940) proved it using two inference rules: (1) from "p" we can deduce "p v q." (2) from "p v q" and "not p" we can deduce "q." If we admit these two rules, we can deduce any "q" from "p" and "not p." The conjunction introduction rule discussed in the following is used to derive the rule (2).

(5) Prof. Brush suggested that the justification for paraconsistent logic might be that it legitimates certain kinds of temporary working hypotheses while assuming that the final (successful) theory will be consistent.But if Brown admits such a commitment to the final consistent theory, the difference between Smith and Brown seems to become a matter of expression. And this conclusion is disadvantageous to Brown, because if we can say the same thing in more conservative (Smith's) way, we have no reason to introduce such a radical revision of logic as Brown suggests. I think that if someone seriously proposes paraconsistent logic as a way of scientific reasoning, he also should refuse the general availability of consisntent theory, and admit the possibility that a paraconsistent theory can be the final theory in the field. This seems to be the only way to refuse Smith's suggestion.

(6) Campbell (1981) gives a similar probability account for another case of inconsistency. Campbell's case is the belief that at least one of the beliefs I accept (except for this one) is not true. Even though we give high probabilities to each of our beliefs, the probability that all of the beliefs are true (in other words the probability of the conjunction of the all beliefs) is pretty low, so we can also accept that at least one of the beliefs is not true. Now, the conjunction of all other beliefs and this last belief is a plain contradiction. Campbell thinks that such an conjunction introduction does not apply to this kind of probability thinking. Lehrer (1975) also argues the same problem, though his position is against the probability account.

(7) Usually Baysians use concrete values for this kind of proof to help reader's understanding. But this strategy seems to cause objections that we cannot assign such concrete values in real life situations, and that thus Bayesianism is useless. I try to use only letters to avoid such a misunderstanding.

(8)There are three cases in which B&D holds: (1) {Q} and B hold, (2) {C} and D hold, (3) neither {Q} nor {C} holds and B and D hold. Now (2) + (3) ²a and (1)+(3)²b, thus (1)+(2)+(3)²a+b.

(9) If {Q} and {C} are not mutually exclusive, pr(D and B) can be larger than a+b. Formally speaking, when pr(Q and C)=r, it can be easily shown that pr(D and B)³r, and pr(E)³r.

(10) There is an interesting argument on this point by Kaplan (1995).

(11) I am very thankful to the discussion in Prof.Brush's seminar on this topic. I am also thankful to his suggestions to the first version of this paper.

Brown, B. (1990). How to be realistic about inconsistency in science. *Studies in the History and the Philosophy of Science 21*, 281-294.

--- (1993). Old quantum theory: a paraconsistent approach. *PSA1992 vol.2*, 397-441.

Campbell, R. (1981). Can inconsistency be reasonable? *Canadian Journal of Philosophy 11*, 245-270.

Kaplan, M. (1995). Believing the improbable.* Philosophical Studies 77*, 117-146.

Kuhn, T. S. (1984). Revisiting Planck. *Historical Studies in the Physical Sciences 14*, 231-252.

Lehrer, K. (1975). Reason and consistency. in *Analysis and Metaphysics*, K Lehrer (ed.), Dordrecht: Reidel. 57-74.

Popper, K. (1940). What is dialectic? *Mind 49*, 403-426.

Schotch, P. K. (1994). Paraconsistent logic: the view from the right. * PSA1992 vol.2*, 421-429.

Schotch, P. K. and Jennings, R. E. (1980). Inference and necessity. *Journal of Philosophical Logic 9*, 327-340.

Smith, J. M. (1988) Inconsistency and scientific reasoning. *Studies in the History and the Philosophy of Science 19*, 429-445.

Norton, J. D. (1993). A paradox in Newtonian gravitation theory. *PSA1992 vol.2*, 412-420.

Back to Recent Works

Back to Tetsuji Iseda Homepage

To INFORM Homepage

To WAM Homepage

If you have any comments, questions or anything else, please mail to tetsuji@wam.umd.edu .

<http://www.wam.umd.edu/~tetsuji/works/consistency.html> Last modified: July 13, 1996