Edited excerpts from letters to David J. McAdoo, Texas
Februar 1987, May 1988
... I am honestly worried about the way mass spectrometrists communicate and about the reputation that this has given us. In the 'sixties and 'seventies there was an anything goes attitude in mass spec papers. Unsubstantiated mechanisms appeared right and left, and the marks of standards and rigor that characterize most of physical organic chemistry were often absent. Things have improved somewhat, but the liberties some people take from ion-molecule complexes (IMCs in the following) threaten to put us back in the muddle.
The term 'Ion-Molecule Complex' ('ion-neutral complex') may well have become counter-productive when used in relation to unimolecular fragmentation reactions, in the sense that it has added confusion to complicated situations (and to a few simple ones, too) rather than understanding. The IMC has shown itself to be all too successful as a vehicle for what I see as unwarranted speculation.
The concept is not yet well-defined, which for one thing makes it difficult to disprove a proposed IMC mechanism. A multitude of meanings have been assigned to the term complex in the literature, and it has become a very vague term indeed. You know what you mean by complex, I think I know what I mean by it, but I am not certain that we mean the same thing. When we try to impart precise information to our readers, the word complex may not serve us well. In fact, the term threatens to become a disguise for hand-waving when the course of a reaction is not obvious; the semantic problem, that complex means different things to different people, becomes camouflage (on purpose, sometimes, I fear).
For the term to have any meaning it must apply to situations where the interaction between two well-defined, separate species (one of them ionic) is attractive through primarily electrostatic forces. Such situations can indeed readily be imagined, if one is not too quarrelsome with regard to when valence forces become essentially Coulombic.
The real problem is then if and how one can establish evidence for the existence of such an undissociated pair of 'independent' species - and let us leave aside the question of minimum lifetime for an IMC and for the moment just satisfy ourselves that it must be long enough to make it meaningful to speak of reasonably well-defined molecules (ions) rather than some transient species.
Before proceeding with this let me borrow a bit from other people. Occam argued - heretically in some people's view at the time - that we should not adopt a complicated description if a simple one suffices to account for what we know. The full truth may be more complex, but we introduce misconceptions by multiplying observation by speculation, we don't advance understanding. Popper six centuries later taught that any explanation we put forth must lend itself to be falsified. A theory must be testable, and a valid test is one that could show the theory to be wrong; to find such a test is much is more important than searching for supporting evidence. Hence Popper's insistence on the risky prediction, eventhough he may have had grander things in mind than organic reaction mechanisms. An explanation that cannot be disproved, or one that does not even lead to testable predictions, is of very little value. Our problem is that intermediate IMCs can easily be postulated in such a vague fashion as to become untestable. Of course, we would never get anywhere if we required every new model to be conclusively proven valid before it was even suggested, but when evidence is hard to come by we must make an extra effort to avoid irrelevant and unwarranted speculation. It is not satisfactory to propose a particular model just because it might be true.
It is particularly important to place relatively stringent requirements on models that are qualitative in nature, on models that do not lead to numerical predictions. When radical cations are considered we are clearly on the warning track when we encounter situations where simple valence-bond pictures do not readily allow us to describe the process under consideration. This happens often since, after all, bonding in open-shell species is not necessarily well-described in terms developed for even-electron systems, particularly not when transitory species are considered. Here, it seems to me, we must take pains to avoid massaging the problem in order to fit the models, and to avoid circumventing the problem by resorting to woolly concepts. Vague terminology often reduces to sheer unsupported conjecture.
Such considerations apply in particular when models (mechanisms) are employed in a suspiciously post hoc fashion - and judging from the literature usage of the term, IMCs seem to be there except when they aren't. Worse, you will have seen authors carefully specifying that their complexes may be either intermediates or transition states or perhaps something else again. One would have thought that a transition state was the last thing a complex could ever be, if the word were to have any meaning. It is when I encounter usage such as this that I fear that the IMC concept may have become counter-productive as a framework for understanding. Loose terms must be used with care and caution. If not they are better abandoned.
A slight digression: it seems futile to attempt a strict distinction between concerted, (strongly) asynchronous, and non-concerted reactions. We have in most cases no way of knowing if one thing has begun before the other is quite finished. Perhaps the rejection of other than essentially completely stepwise processes rests on an insistence on the still picture. It may be that chemical equations depicting multi-step reactions are deceptive in this respect, being essentially series of still pictures. They lead us to confuse image with fact, which is rather like climbing the signpost instead of following the road (Alan Watts). My point is that in some cases an IMC description is only meaningful if it can be ascertained that there is a temporal distinction between one step and the next.
Let me illustrate some of this by an example which is often used to demonstrate the validity of the IMC approach: consider the dissociation of CH3CH2CH2CO+, claimed to proceed via a [C3H7...CO]+ complex. Where is the evidence that propyl does not become isopropyl simply as the C-CO bond is stretched? Even if one presumes that the kinetic energy release observed confirms isomerization, what permits us to conclude that an attempted C-CO stretch leads us to a complex where we may placidly await carbonium ion rearrangement, only then to resume the C-CO stretching motion?
I'm not saying that the model is incorrect, but I am issuing a warrant for the evidence. Certainly, the incipient fragments are relatively free to do their thing as the C-C bond stretching approaches the dissociation limit, but this does not constitute an ion-molecule complex!
I am here not concerned with semantics, but with Occam's razor. What seems to have been overlooked when reactions of this kind have been considered is that the C-C stretch has not become a dissociation at some 3 Ångströms or thereabout, as will be the case for the comparable neutral species. We need to get out to perhaps twice or thrice that distance, given a reasonable dipole moment for the departing neutral. Approaching dissociation, the incipient fragments will be moving in a predominantly electrostatic potential, and, for the above examples, the covalent bonding to the departing neutral that kept propyl from becoming isopropyl is no longer present and rearrangement can ensue. But there is no complex. Or perhaps better, there is no need to postulate a complex.
Perhaps this is the still-picture problem? C3H7 isomerizes as the CO moves away, that's all. The interaction between CO and a point charge is rather small (less than 3 kcal/mol at 3.5 Å distance, polarization interactions almost all of it), while the propyl-to-isopropyl isomerization yields some 16 kcal/mol; it would seem that the bond to the departing CO could not stretch very far before the system woke up to the fact that the primary carbonium ion isn't even in a potential energy minimum. For CH3CH2CH2OCH2+ and related systems Williams and Bowen's results provide good indications that electrostatic interactions are behind the differences in the detailed behavior. But, and this is another big but, there's a long way from electrostatic interactions to complex.
This description may seem reasonably compatible with that in the original papers, if the unfortunate term, IMC, had not been used. So why worry? The reason is that in some cases the term is actually appropriate. Using it when it isn't robs us of the opportunity to employ it when it is. Mass spectrometry has quite enough imprecise terminology as it is.
If the above seemed to be rather a fine point, or perhaps just a disagreement with regard to interpretation, let me try to illustrate my position in a somewhat different way. It may seem to be useful, in a didactic sense, to describe the dissociating species as a pair of distinct entities that are still bound to one another, in order to illustrate the various transformations one after another while the two fragments-to-be are in some waiting position. But we are considering the term IMC as a vehicle for scientific communication, not for second year organic chemistry. When attempting to describe the actual course of the reaction it is dangerous to give some model priority over testable fact, and it is unreasonable if the deus-ex-machina, the ion-molecule complex, is invoked only to exculpate the didactic maneuver.
Above I voiced the opinion that models involving IMCs may lead to unsubstantiated and unwarranted speculation. However, far would it be from me to reject a model only because it had yet to be rigorously proven to be valid, if it led to useful predictions. But it should at least be clear when the model is applicable. Take the reactions of metastable immonium ions: two processes leading to alkene loss, one by cleavage of a C-C bond, one by cleavage of a C-N bond. For the latter an ion-molecule complex has been postulated, for the former not. Why? Because, it seems, the former involves a specific H-transfer and that is easy to draw, with arrows and all. The H-transfer in the latter reaction is not specific and that is difficult to explain. Kazam!! In comes the ion-molecule complex, shining armor, and the problem goes away. Be that ever so much THE TRUTH, how is one to decide a priori which reaction(s) will occur via IMCs?
So what I think is, basically, that it is often (usually?) unnecessary to invoke IMCs, that it seems difficult to decide when to expect them to intervene, that misuse of the concept may too easily lead to unsatisfactory hand-waving, and that the difficulties inherent in establishing experimental evidence for the existence of 'something' with the necessary lifetime should make us wary of postulating this 'something' in lieu of explanation. The words remain falsifiability, be the model ever so pleasing, and evidence, be that ever so hard to get.
The reason, it seems to me, that complexes have caught many people's attention is that the in(ter)vention of complexes can provide an easy (and today fashionable, as you will have noticed) rationalization of apparently inexplicable observations. It seems not to be an obstacle if the rationalization is not testable. When a sufficiently large number of papers have claimed that complexes intervene, then the complex is elevated, automatically, from intriguing possibility to proven fact. Regardless of whether any hard evidence was ever presented. And that is worrisome.
This sitation arises because the focus, for many people, is the explanation, something that can account for the outcome actually observed. To explore the matter further, one approach is to find other reactions that also appear to require the intervention of complexes. These reactions can be studied in great and careful detail, providing valuable evidence that can be interpreted elegantly on the assumption that complexes intervene. But, and this is a magnum BUT, this approach will provide mainly circumstantial evidence, since the selection of the system ensures that the results will not be in disagreement with the intermediacy of complexes.
My own attitude is that instead of worrying about the reactions and rejoicing in the explanations, we should worry about the complexes, if in fact the complexes are what we're really interested in. Forget about the explanations they afford. If a complex between X and Y exists, what will be the properties of this complex? How long could it live, what range of energies might it possess, when might it be formed, how might it react? And then, how are we going to demonstrate that it possesses these properties? When we approach this aspect we must avoid begging the question; the significant properties are those that are not related to the explanation, to the reason why we suspect that a complex might be present.
A useful definition of what a complex is will be difficult to put together if lifetime is not a criterion, since I suggest that we restrict the definition to include complexes we can study. Otherwise it becomes metaphysical. You and I disagree because (correct me if I interpret you wrongly) you aim to characterize reactions that proceed by a particular mechanism, and your 'complex' can be but some transition state, while I concern myself with something that exists long enough to be looked at and talked about. Frankly, I don't think that your approach will be productive; it will never allow you to be sure that you have a situation with no complex. This is why it has been difficult for you to find good "identifying characteristics"; a proper criterion requires that you can draw conclusions when the conditions specified are not met.
Science doesn't just happen, scientific method is not what happens to feel good. To consider how one goes about examining theories does not require mastership of mumbo-jumbo. It only looks that way. Personally, I am a simpleminded organic chemist who believes in evidence. When evidence is absent or circumstantial I prefer the simplest possible account of the results (that's the Occam bit), and I reserve and exercise the right to conclude that I don't understand what's going on. I even suggest that it is questionable science to do otherwise. It is fine to propose a particular explanation, once or perhaps twice, even if the evidence is not at first compelling. It is not fine to insist on the explanation time and time again, when evidence continues to be elusive. Ten years passed between the first suggestion that ion-neutral complexes might intervene in some reactions and the first hard evidence that they really did.