The beryllium dimer (Be2) is my favorite molecule. With two identical atoms and just four valence electrons (2CTg2CT2) it is not exactly pretty. However, for many years it resisted discovery, and much theoretical work indicated that this situation would not change. I was astonished when my DF calculations showed that the binding energy should be substantially greater than in its group 12 neighbors in the periodic table (He2, Mg2). Either I had an unexpected prediction that could be checked by other methods, or I had a case where the DF method led to a qualitatively incorrect result. An interesting situation, or so it seemed.
My interest in group 12 dimers arose from discussions with a colleague in the Institut für Chemie in Jülich, Chung Wu. He had used a Knudsen source to evaporate metals and study the concentration of clusters of different sizes as a function of temperature. If one makes assumptions about the bond length and the vibration frequency, it is possible to estimate the dissociation energy of the ground state. Chung had performed measurements on Mg2 and Ca2, for which other spectroscopic data were available, but his estimates of the binding energies were significantly larger than earlier results of infrared spectroscopy. I decided to carry out calculations on all group 12 dimers.
The results for Mg2 were consistent with measured values of the bond length, but the vibration frequency and the well depth were both overestimated, a feature we now know follows from the local density (LD) approximation used in these calculations. Absorption spectra had also been measured for the calcium dimer, and the results of the calculations showed similar parallels. I was confident enough in the DF description of the binding in these molecules to extend the calculations to the heavier dimers (Sr2, Ba2, and Ra2), even to the lightest, He2. I did not expect a good description of the last of these, a prototype van der Waals molecule with a minimum in the binding energy curve that is so shallow that it does not support vibrations (this means that the minimum energy associated with vibrations - the "zero point energy" - is above that of two separated atoms). The DF calculations led, as expected, to a minimum that was too deep.
There were good reasons why I came last to the beryllium dimer. The opinions of many eminent theoretical chemists were overwhelmingly against its existence, and our first applications of the DF formalism to "first-row" molecules  omitted Be2 for precisely this reason! Here are quotes from some of the most cited theoretical chemists of the past decades:
One would expect that two normal beryllium atoms would behave towards each other as do two normal helium atoms. This expectation is given support by our calculations, which show that the resulting molecular state is repulsive.
There is no evidence from this calculation that the ground state of Be-Be is bound ... The CI results are just as repulsive as the SCF results
.. the van der Waals bound molecule Be2, which should have a dissociation energy less than 1.2 kcal/mol, the experimental for Mg2 .. To obtain a realistic result, say 0.7 kcal/mol, for the dissociation energy ...
Of course, the ground states of analogous diatomics (Mg2, Hg2, Cd2) are bound due to the much larger dispersion interaction which occurs in these much more polarizable species. ... The second order perturbation theory calculations indicate that the ground state potential curve of Be2 is indeed repulsive.
Because the ground state of Be2 has not been detected experimentally, it appears that the van der Waals minimum is very shallow (. 1 kcal/mol), it may even be too shallow to support vibrational levels.
Since a system of two Be atoms, each with closed shell (1s22s2) electronic configurations, does not show appreciable bonding, substantial changes must occur in the nature of bonding if beryllium metal is to be formed. ... At the highest level of theory used, RMP4(SDQ)/6-31G*, the bond length is 3.999 A and the binding is 0.3 kcal/mol.
R.A. Whiteside, R. Krishnan, J.A. Pople, M.-B. Krogh-Jespersen, P. von R. Schleyer, G. Wenke 
These articles paint a clear picture: The beryllium dimer has an equal occupancy of bonding and antibonding orbitals and will be unbound in the absence of long ranged "van der Waals forces." These forces are proportional to the atomic polarizability, which lies in Be between the values of He and Mg. As noted in , this implies that the bonding in larger Be clusters must be substantially different from that in the dimer, or beryllium metal would not form.
I carried out the calculations in the last quarter of 1978, completing the last (Be2) in early December. The results were quite disconcerting: Not only should Be2 exist, but its equilibrium separation (2.57 A) would be shorter than in Mg2 and about half of the anticipated minimum of the binding energy curve. Moreover, the binding energy should be significantly greater than that of Mg2. The results are shown in Fig. 1.4, where DF calculations of the cohesive energies of the bulk elements and experimental values are shown where available. The obvious similarities between the two curves suggest that binding in the diatomic molecules and the bulk has the same origin. A shorter bond length in Be2 than in Mg2 would be consistent with the measured lattice constants in the bulk materials.
I planned to submit the results for publication, but I was uncertain enough to seek the reaction of theoretical chemists before doing so. Just before Christmas (21 December 1978) I wrote to Prof. Werner Kutzelnigg in Bochum, who headed one of the leading theoretical groups in Germany. Bochum is just 100 km from Jülich, and I had given a seminar in this group in February 1978. We arranged
(solid line, left scale ) and Experimental values (crosses)
a second seminar on 7 February 1979. In the meantime I began analyzing and writing up the results. I also tried several times to convince Chung Wu to perform measurements on Be2, but that is another story.
I have vivid memories of my second Bochum seminar. It was obvious that nobody believed my results, and the discussion after my presentation focused solely on which mistake I must have made, not on whether or not there was one. I asked what I had done wrong in Be2 that had apparently been right in Mg2, but there were ready answers. Herbert Kollmar agreed to perform additional calculations on Be2, and I returned to Jülich. Prof. Kutzelnigg wrote to me shortly afterwards (19 February 1979) with the results of these calculations for an interatomic separation of 5.0 a.u. (2.65 A) (a little longer than the minimum in my binding energy curve), informing me that2:
The molecule is certainly not bound at this separation, but (by ca. 0.5 kcal/mol) repulsive. The minimum is then at greater distances and is obviously much weaker than you imagine, but in agreement with the pseudopotential calculations that Herr Schwartmann has shown you, where Mg2 has a clearly deeper minimum.
In the following 2 weeks I completed the manuscript. The calculations indicated that sp-polarization is the origin of binding in these molecules, and I showed that the spatial overlap between the valence s- and p-orbitals was greatest in beryllium. I sent the manuscript to the Journal of Chemical Physics at the University of Chicago on 13 March 1979, and I left for Australia with my family shortly afterwards. I included several minor improvements suggested by the referee, and the manuscript was accepted on 2 May 1979 and published on 1 August 1979 .
The absence of experimental evidence for the existence of the beryllium dimer was very frustrating, of course, and I tried again to convince Chung Wu of the interest that the identification of the molecule would cause. I had no success, and I understood his reluctance to work with a metal whose vapor is highly toxic. Shortly afterwards, Olle Gunnarsson returned from the 46th Nobel Symposium in Aspenasgarden (near Göteborg, Sweden from 11 to 16 June 1979). Rod Bartlett had told him there that correlated wave function calculations on Be2 by Bowen Liu (IBM San Jose) had led to a minimum between 4 and 5 a.u. with a binding energy of several kcal/mol. On 26 June 1979 I sent copies of my manuscript to Bowen Liu, with a request for more information, and to Walter Balfour (University of Victoria, BC, Canada), who had observed Mg2 while at the National Research Council laboratories in Ottawa. I asked whether he could do similar measurements on Be2.
2W. Kutzelnigg to ROJ (19 February 1979)
"Herr Kollmar hat inzwischen Be2 bei 5 a.u. (2.65 A) gerechnet. Das Molekül ist bei diesem Abstand sicher nicht bindend, sondern (mit ca. 0.5 kcal/mol) abstoßend. Das Minimum liegt wohl bei größeren Abstanden und ist offenbar viel schwacher als Sie vermuten, aber in Einklang mit den Pseudopotentialrechnungen, die Ihnen Herr Schwartmann gezeigt hat, wonach Mg2 ein deutlich tieferes Minimum hat"
Balfour responded on 4 July 1979 with more information on Mg2 and Ca2 and the news of unsuccessful attempts by Reginald Colin at NRC to find the beryllium dimer. Colin (who had moved to the Universite Libre in Brussels) provided me subsequently with more details of a difficult experiment (18 July 1979). Bowen Liu did not answer my letter and he was not particularly forthcoming when I phoned him, so I wrote on 7 August 1979 to his collaborator Douglas McLean. Doug came originally from Western Australia, and he had spent a year (1962) in the Chemistry Department of the University of Western Australia in Perth when I was an Honours student in Physics there. He responded at length (27 August 1979) with full details of the calculations and the results. Liu and McLean had found a minimum at 4.75 a.u. and a well depth of 810 cm-1, but the calculation (ICF, interacting correlated fragments) left several questions open.
I had not received the promised details of Herbert Kollmar's calculations, and I wrote to him on 30 July. He responded (1 August) that he found no minimum in CEPA (coupled electron pair approximation) calculations for a Be-Be separation near 5 a.u. On 7 August Prof. Kutzelnigg wrote a letter with an unambiguous message3:
Herr Kollmar has shown me your letter and his response. In order to avoid misunderstanding, I should like to add the following remarks. ( ) This indicates that the CEPA-curve should be very similar to the exact curve - even if you like the IEPA-curve better, because it is similar to yours. Perhaps you neglect exactly those inter-intra correlation effects that are ignored by IEPA.
Several weeks later (21 September), however, Herbert Kollmar informed me of a presentation by Paul Bagus from IBM San Jose at a meeting held in Bad Neuenahr (18 September), where the results of Liu and McLean were presented (Be2: re = 2.49 A, De = 814 cm-1, v1 = 202 cm-1, v2 = 132 cm-1). He wrote:
The results confirm your calculations; the discrepancy to our calculations is unclear.4
The results of Liu and McLean were submitted to Journal of Chemical Physics as a Note on 10 December 1979 and published on 1 March 1980 . This article referred to my JCP publication.
3W. Kutzelnigg to ROJ (7 August 1979)
"Herr Kollmar hat mir Ihren Brief und seine Antwort gezeigt. Damit keine Mißverständnisse auftreten, möchte ich noch folgende ergänzende Bemerkungen machen. ( ) Dies spricht schon dafür, dass die CEPA-Kurve der exakten Kurve sehr ahnlich sein muss - auch wenn Ihnen die IEPA-Kurve sympatischer sein sollte, weil sie Ihrer ahnlich ist. Vielleicht vernachlassigen Sie auch genau jene inter-intra Korrelationseffekte, die man bei IEPA vernachlässigt."
4H. Kollmar to ROJ (21 September 1979)
"Die Ergebnisse bestatigen Ihre Rechnungen; unklar ist die Diskrepanz zu unseren Rechnungen."
The density functional results for Be2 were so different from all preceding work that they were greeted with much scepticism. This was also true to some extent for the work of Liu and McLean. A notable exception was Volker Heine, the adviser of my Ph.D. work, who told me:
It is perfectly obvious to any solid-state physicist that Be2 must be more strongly bound than Mg2.
He knew immediately that this was a consequence of the relative compactness of the 2p-orbitals in the first-row elements, but few other condensed matter physicists were interested.
It was by no means obvious that the beryllium dimer could be identified using the mass-spectrometric methods in use at the time. The melting and boiling points of Be are far higher than Mg, and - even if one could develop an appropriate furnace -such high temperatures lead to very unstable clusters. Other DF calculations led to similar results to mine, and Lengsfield et al.  extended the correlated wave function work of Liu and McLean to larger basis sets and more extensive methods of including correlation effects. The location of the minimum of the Be2 binding energy curve changed very little (the revised best estimate was re = 4.73 ± 0.03 a.u, De = 2.04 ± 0.21 kcalmol"1), and the work was published on 4 May 1983.
I was surprised that this paper did not refer to my JCP article 4 years earlier, and I thought that a "Comment" to the journal was appropriate. I added some newer results on Be2, as well as those of Painter and Averill . The Editor sent it to Bowen Liu, who noted the lack of new results and suggested asking the opinion of a neutral referee. Liu added, however:
In the event that you decide to publish the comment, we would like an opportunity to reply to the claim that 'density functional calculations are simpler to interpret than CI calculations'.
The "neutral" referee wrote:
No new results or analyses are presented here. This contribution is mainly in the nature of a polemic in favor of more serious consideration of density functional results in studies of chemical binding. All the data and arguments on this point are already in the literature, and no useful purpose is served by publishing this discussion.
While I agree that it would have been appropriate for Lengsfield et al. to mention the density functional results, their omission is not a sufficient reason for the publication of this comment. In any case, the ab initio calculation is a definitive calculation which establishes a standard of accuracy. I do not think that any density functional calculation can be regarded in the same light.
It is interesting to read these remarks over 20 years later, when most theoretical chemists value density functional calculations for opening up the study of much larger systems than possible with more traditional (wave function based) methods and the single-particle picture that eases the interpretation of the results.
Nevertheless, it is not surprising that the Editor, John Light, rejected the article and equally unsurprising that I responded to these comments.5
I had heard so often about the difficulties facing the experimental identification of Be2 that it came as a real surprise when it was carried out  (published 31 August 1984). Vladimir Bondybey at Bell Laboratories used liquid N2 to cool Be vapor, after which laser-induced fluorescence from Be2 was measured. The 1 Xg ground state was found to be characterized by re = 2.45 A, De = 790 ± 30 cm-1, !e = 275.8 cm-1. I am sure that Liu and McLean were as pleased with this result as I was. The minimum in the binding energy curve is much shorter than in all work prior to 1979, and I had no doubt that my picture of the nature of the bond was right.
The experimental confirmation of the DF prediction that the bond is stronger in Be2 than in Mg2, so that the binding trends were similar to those in the solids, might have helped the acceptance of density functional methods by chemists. It did not. I met many who remained convinced by the weight of literature favoring a very weak bond, and others focused on the overbinding that resulted from our use of the local density approximation in the DF calculations. A representative view came from John Light, Editor of the Journal of Chemical Physics and ex officio a member of the chemical establishment. During the refereeing process of a paper I
5ROJ to J. C. Light, Editor, Journal of Chemical Physics (29 November 1983) Thank you for the author's and referee's response to the above comment. Given the content of these remarks, I would probably have acted as you did. Nevertheless, it would be surprising if I had nothing further to say on the matter.
I think that you should make it quite clear in your Announcement that you are less interested in "discussion and comments" than in controversy. The first draft of my comment would have been much closer to your requirements, and I shall bear your change of policy in mind for future occasions.
Over the past few years, I have had numerous opportunities to discuss the density functional method and its applications with quantum chemists. I have found that most chemists of a particular generation are incapable of giving the method serious consideration. My visit to San Jose in August indicated that Dr. Liu is no exception and his letter comes as no surprise. The last sentence of the referee's remarks indicates that he, too, subscribes to the prevailing view of the CI fraternity.
For some years, I have been attempting to convince chemists that density functional calculations are very useful in certain contexts and solid state physicists that the approximations they use in DF calculations can lead to unreliable results. I have not yet had much success in either direction. Quantum chemists and solid state physicists can learn a lot from each other, but the communication is poor and is not helped by editorial decisions to throttle scientific discussion. Given the amount of rubbish generated by earlier CI calculations on Be2, it would have been interesting to hear Dr. Liu's arguments for the relative simplicity of their interpretation. Making such a comparison would also have provided him and his colleagues with the opportunity to discover what the density functional formalism is.
submitted on the carbon trimer C3, I asked him about his view of the DF method and its appropriateness for his journal. His response is given below.6
I had spent the first 4 months of 1984 at the Max-Planck-Institut fur Festkorperforschung in Stuttgart, after which Olle Gunnarsson and I had a clear picture of a major source of error in DF calculations using the local density approximation . There is no doubt that LD calculations for Be2 will lead to overbinding, and the experimental result for Be2 told us by how much. It comes as no surprise that other efforts were made to improve on the initial calculations of Liu and McLean. One of the most extensive was that of Petersson and Shirley , who studied the convergence of wave function-based calculations for Be2. After extrapolation to the complete basis set and full CI limits, they found good agreement with measured values. My 1979 paper was not cited.
The DF calculation and the prediction that Be2 should be more stable than Mg2 were pieces in the mosaic that led to the breakthrough of DF calculations in chemistry. As noted by Nicholas Handy and coworkers, it was one of the first successes in DF applications to small molecules :
Jones was indeed the first theoretician to suggest that Be2 has a potential minimum near 2.45 A, and although his well depth at 8 kcal/mol was too deep, his frequency was good at 300 cm-1. All other ab initio calculations to that date (1979) had predicted a minimum near 4.5 A , principally because of deficient basis sets. Jones result was one of the first successes of DFT to the study of small molecules.
I still like my JCP article of 1979, where my tone was appropriately cautious, and I am pleased that I did not yield to the weight of opinion of the chemical establishment concerning binding in the beryllium dimer. Chemistry is a conservative field, and I cannot help but wonder whether established opinion is as wrong in other areas as it was in this one.
One postscript might also be interesting: I have not been to the Theoretical Chemistry group in Bochum since 1979. However, my colleague John Harris gave a seminar at the 29th Symposium for Theoretical Chemistry, held at Oberwiesenthal
6J.C. Light, Editor, Journal of Chemical Physics to ROJ (16 November 1984)
"Thank you for your letter of 2 November 1984 concerning the above manuscript. In order to try to evaluate the problem better, I have read through your manuscript. The problem, as I see it, is that despite the large number of manuscripts published in the Journal of Chemical Physics on this method, many chemists remain to be convinced of its value.
There appear to be two reasons for this. First, the local density approximation introduces an uncertainty about the reliability of the results which is compounded by the use of muffin-tin orbitals. Second, many chemists prefer the more rigorous and familiar approaches even if they be computationally more computer intensive. It is also clear, from looking at some of the published papers listed, that the approach has continued to evolve (i.e., different parameterizations of Exc).
This leaves me, and probably the reviewer, with an unhappily ambiguous feeling toward this manuscript. it does not treat the methodology problem (clearly stated in JCP 79, 1874, part
IV. D) but gives only one example where the method apparently works well, whereas for the NH3 inversion barrier it doesn't.
I'm not sure that I have answered your questions as to criteria, which are probably decided empirically by averaging over referees."
(Erzgebirge) from 27 September to 1 October 1993. In the discussion following the talk, which considered the role of density functional calculations in chemistry, Prof. Kutzelnigg said to John that he acknowledged our "triumph." He had noticed, after all.
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