Decoherence Spectroscopy for Atom Interferometry

Round  1

Reviewer 1 Report

Trubko and Cronin present an interesting experiment on how to use decoherence for spectroscopy in atom interferometry. They provide a short introduction, clear motivation, compare model and experiment to extract useful data on the tune out wavelength with a comparison to alternative methods. In total this is a paper is serious science that can clearly be published.

I would however suggest some minor additions and considerations to be included in the final manuscript:

The "tune-out-wavelength" is established in the community but not a standard notion in larger circles. I suggest to explain it in a half sentence where it appears for the first time.

The references 1-6 are summarized under the heading atom interferometers.
2 of them refer to molecule interferometry. It might be useful to either summarize that
under "matter-wave" interferometers or to make the distinction between atoms and molecules

As a theorist one would expect to see references to decoherence theory in the first line (line 8), where the concept is introduced . Ref 31 and 32 are good, but earlier of more in depth references are cited below and could already be mentioned very early: Theory preceeded experiments by decades!

- Zurek, W. H. Environment-Induced Superselection Rules. Phys. Rev. D 26, 1862-1880 (1982).

- Zurek, W. H. Decoherence and the transition from quantum to classical. Phys. Today 44, 36-44 (1991).

- Zurek, W. H. Decoherence, Einselection, and the Quantum Origins of the Classical. Rev. Mod. Phys. 75, 715-775 (2003)

        - Joos, E. & Zeh, H. D. The emergence of classical properties through interaction with             the environment. Z. Phys. B. 59, 223-243 (1985).

        - Caldeira, A. O. & Leggett, A. J. Influence of damping on quantum interference: An             exactly soluble model. Phys. Rev. A 31, 1059 (1985).

4. The use of decoherence for advanced measurements in matter-wave interferometry has been implemented before in some other works which might be mentioned for reference.

    -  Eibenberger, S., Cheng, X., Cotter, J. P. & Arndt, M. Absolute absorption cross sections     from photon recoil in a matter-wave interferometer. Phys. Rev. Lett. 112, 250402 (2014).

5. I suggest to say "multi-pass cell" rather "optical cavity", since there is no resonant enhancement in this arrangement... even though it is a (on purpose strongly misaligned) plane-parallel optical cavity.

6. On line 31 they define 32 "s(v) is the atom wave packet separation".. I suppose it means "the maximum wave packet separation".. since it varies from 0 to s(v) up to the middle grating

7. Line 55:
"scattering even one photon per atom reduces the atom interference fringe contrast nearly to zero, provide that the components of each atom’s wave function are separated by a distance larger than the wavelength of light"
-> Should it read "half the wavelength of light?"

8. line 57

"In a related perspective, scattering entangles atoms with the environment."

might be clearer:

"In a related perspective, scattering entangles atoms with the scattered photons which are then dissipated by the environment."

9. Would it be better to clarify  that the Rabi frequency between different transitions is different? The detailed calculation is not entirely trivial with all Wigner, Racah etc.. coefficients

Author Response

Author Response File: Author Response.pdf

Reviewer 2 Report

The manuscript by Trubko et al. details how the authors use decoherence effects in an atom interferometer to calibrate a laser wavelength for tuneout spectroscopy. The decoherence is simply spontaneous emission, but due to the complicated beam geometry involved the effect requires careful analysis. Although this work is fairly specific to the authors’ particular apparatus, it does provide a useful explanation of their calibration technique and supports other results from the author’s lab. I think that publication in Atoms would make sense.

I have a few comments on the manuscript:

The most significant is in regards to some of the potential error effects that the authors discuss in Section 5. My impression is that these are all supposed to be small effects on the scale of the current precision, but that they would need to be considered if the precision is to be improved. However, the authors never actually give estimates for the size of these effects. I think that such estimates need to be provided if the stated accuracy is to be trusted. In other words, if the calibration error estimate is 0.22 ± 0.05 pm, a calculation should be provided to show that the estimated shifts due to finite mirror reflection, beam size variation, beam misalignment, and dephasing are all small compared to 0.05 pm.

In the introduction, references should probably be provided to other contrast interferometers. A notable example is S. Gupta et al, Phys. Rev. Lett. 89, 140401 (2002) but I guess there are others.

In section 2 paragraph 1, the authors mention α(iω ) but I don’t understand the presence of the i.

Also in that paragraph, it would be helpful to state clearly that the only decoherence mechanism being considered is spontaneous emission. As discussed later in the paper dephasing can also occur, it is not immediately obvious which is dominant.

In Figure 1(a), the blue curve seems to be more like ten times larger than the red curve, vs. the factor of five I would expect from the listed intensities.

In Figure 2 and the related discussion, the relative scales of the atom beam separation and the laser waist are not clear. The expression for the phase in Eq (1) suggests that the atom beam separation is small compared to the laser beam waist, so that using the derivative to quantify the intensity difference is appropriate. Is that the case? Providing values and describing how the lasers are aligned to the atom beam would be helpful. Perhaps in Fig 2, the laser spots on the cavity mirrors could be indicated in part (a), to illustrate their size an alignment. But perhaps the figure is not shown sufficiently to scale for this to be effective.

In Eq (6) I think there is a factor missing. I believe the excited state population should be

for the authors’ definitions of  and . If so then Eq (6) should feature Γ /2 rather than Γ .

I am confused by Eq (10) because I think that for a given laser polarization, the scattering rate depends on the  level of the atom. Shouldn’t the  term be defined as some type of average over m levels?

In Figure 4 and the related discussion, it is confusing how T and δ are being treated.  I guess that T here is meant as an average exposure time, since the atoms don’t all have the same velocity? Do the authors feel they know the velocity and beam waists well enough that it makes more sense to fix T in the model? But the value cited in the figure looks more like an estimate than a calculation. In the first paragraph of the section, it suggest that θ  is well known empirically but that T is a free parameter, how does that accord with the procedure described in the figure?

Also, the text says that only Ω  was adjusted in the fits, but surely δ  was as well. The second paragraph discusses varying θ , but that seems contrary to the discussion in the first paragraph.

Is there an explanation for why the blue curve has a different Doppler shift in Fig 4? Also what range of Ω  values were obtained from the fits? I would expect that the ratios of the beam intensities could be measured fairly accurately here, do they agree with the fit results?

In the paragraph before Section 5, the authors suggest that the measured Doppler shift can be directly applied as a correction term to the tuneout wavelength. This isn’t clear. The authors say that the contrast spectrum is shifted by -0.22 pm from what would be measured if δ  were zero, so it makes sense that the same shift would apply to the TOW spectrum. But it is not clear that δ =0 corresponds to zero velocity atoms. Here δ  is defined as the angle of the first laser pass, but the other laser passes are at different angles and it isn’t obvious that the Doppler shifts all cancel or average to zero if the first pass is perpendicular to the atom beam.

In the discussion of fluorescence detection, the authors suppose that each atom scatters one photon. Why is that a reasonable estimate?

The authors make a reasonable case that contrast measurements are the optimum approach in this apparatus. But it would be useful to discuss how small a change in contrast can be detected, on both a practical and perhaps fundamental level. The authors suggest that shifts as small as 50 kHz could be identified, but can they back that up with experimental results or theory calculations? It seems like this would require a very good sensitivity to small contrast changes.

I did not very well understand the relation between Figures 6 and 7. Figure 6 I think shows the laser beam walking off transversely due to misalignment, but Figure 7 seems to show an abrupt ‘jump’ in the beam position near the bottom of the mirror.

I do not expect that any of these issues will be too hard to address, and I think they will help improve the paper.

NB - I am not quite sure how the review submission process is going to handle my equations, my apologies if this causes confusion. I have attempted to attach a pdf version as well.

Comments for author File: Comments.pdf

Author Response

Author Response File: Author Response.pdf

Round  2

Reviewer 2 Report

The authors have revised the manuscript and addressed most of my comments. I do have a few further recommendations to consider.

First regarding some issues remaining from the initial review:

- Regarding the alpha(iw) at the start of section 2, I recommend using alpha(w). While alpha(iw) is indeed relevant to van der Waals calculations, the actual measurements of tuneout wavelength discussed in the present paper and most of the references deal with the polarizability alpha(w).

- I like the dimensions in Fig 2, but the distance causing me trouble was the atom beam separation in the interferometer, which is not shown. Perhaps it could simply be mentioned in the caption.

- The authors claim that for linear polarization, the polarizability (and scattering rate) is independent of the m_F level. That is true only in the limit that the excited state hyperfine splitting is negligible. The excited state splittings are not very small compared to the claimed precision here. I doubt this has any significant effect but it should probably be checked, and the paper should not claim that the polarizabilities are identical (cf first paragraph of 5.2) without further explanation.

- I think it would help the reader if, near Eq (8), it was noted that p =0 corresponds to the most perpendicular beam, and that p ranges symmetrically about that from –N to N.

A few additional issues noticed on re-reading:

- The authors obtain a net shift of 0.22 \pm 0.1 pm, which is surprisingly large given the estimated range of Doppler shifts in the cavity of \pm 0.26 pm. Would it be possible to comment on why the Doppler shifts do not average out better?

- At line 178 (pg 9) the superscripts on both detunings are typeset incorrectly.

Author Response

Author Response File: Author Response.pdf