It's typically much easier to overestimate than underestimate the loss angle with a ringdown measurement (eg, you underestimated clamping loss and thus are not dominated by material dissipation). So, it's a little surprising that you would find a higher loss angle than Penn et all. That said, I don't see a model uncertainty for their dilution factors, which can be tricky to model for thin films.

Yeah but this is the noise that we are seeing. I would have liked to see lower noise than this.

If you're assuming a flat prior for bulk loss, you might do the same for shear loss. Since you're measuring shear losses consistent with zero, I'd be interested to see how much if at all this changes your estimate.

Since I have only one number (the noise ASD) and two parameters (Bulk and Shear loss angle), I can't faithfully estimate both. The dependence of noise due to the two-loss angles is also similar to show any change in frequency dependence. I tried giving a uniform prior to Shear Loss Angle and the most likely outcome always hit the upper bound (decreasing the estimate of Bulk Loss Angle). For example, when uniform prior to shear was up to 1x 10^{-5}, the most likely result became = 8.8x10^{-4}, = 1 x 10^{-5}. So it doesn't make sense to have orders of magnitude disagreement with Penn et al. results on shear loss angle to have slightly more agreement on bulk loss angle. Hence I took their result for the shear loss angle as a prior distribution. I'll be interested in knowing if their are alternate ways to do this.

I'm also surprised that you aren't using the measurements just below 100Hz. These seem to have a spectrum consistent with brownian noise in the bucket between two broad peaks. Were these rejected in your cleaning procedure?

Yeah, they got rejected in the cleaning procedure because of too much fluctuations between neighboring points. But I wonder if that's because my empirically found threshold is good only for 100 Hz to 1kHz range because number of averaging is lesser in lower frequency bins. I'm using a modified version of welch to calculate the PSD (see the code here), which runs welch function with different npersegment for the different range of frequencies to get the maximum averaging possible with given data for each frequency bin.

Is your procedure for deriving a measured noise Gaussian well justified? Why assume Gaussian measurement noise at all, rather than a probability distribution given by the measured distribution of ASD?

The time-series data of the 60s for each measurement is about 1 Gb in size. Hence, we delete it after running the PSD estimation which gives out the median and the 15.865 percentile and 84.135 percentile points. I can try preserving the time series data for few measurements to see how the distribution is but I assumed it to be gaussian since they are 600 samples in the range 100 Hz to 1 kHz, so I expected the central limit theorem to kick-in by this point. Taking out the median is important as the median is agnostic to outliers and gives a better estimate of true mean in presence of glitches.

It's not clear to me where your estimated Gaussian is coming from. Are you making a statement like "given a choice of model parameters \phi_bulk and \phi_shear, the model predicts a measured ASD at frequency f_m will have mean \mu_m and standard deviation \sigma_m"?

Estimated Gaussian is coming out of a complex noise budget calculation code that uses the uncertainties package to propagate uncertainties in the known variables of the experiment and measurement uncertainties of some of the estimate curves to the final total noise estimate. I explained in the "other methods tried" section of the original post, the technically correct method of estimation of the observed sample mean and sample standard deviation would be using gaussian and distributions for them respectively. I tried doing this but my data is too noisy for the different frequency bins to agree with each other on an estimate resulting in zero likelihood in all of the parameter space I'm spanning. This suggests that the data is not well-shaped either according to the required frequency dependence for this method to work. So I'm not making this statement. The statement I'm making is, "given a choice of model parameters and , the model predicts a Gaussian distribution of total noise and the likelihood function calculates what is the overlap of this estimated probability distribution with the observed probability distribution.

I found taking a deep dive into Feldman Cousins method for constructing frequentist confidence intervals highly instructive for constructing an unbiased likelihood function when you want to exclude a nonphysical region of parameter space. I'll admit both a historical and philosophical bias here though :)

Thanks for the suggestion. I'll look into it.

Can this method ever reject the hypothesis that you're seeing Brownian noise? I don't see how you could get any distribution other than a half-gaussian peaked at the bulk loss required to explain your noise floor. I think you instead want to construct a likelihood function that tells you whether your noise floor has the frequency dependence of Brownian noise.

Yes, you are right. I don't think this method can ever reject the hypothesis that I'm seeing Brownian noise. I do not see any other alternative though as such as I could think of. The technically correct method, as I mentioned above, would favor the same frequency dependence which we are not seeing in the data :(. Hence, that likelihood estimation method rejected the hypothesis that we are seeing Brownian noise and gave zero likelihood for all of the parameter space. Follow up questions:

Does this mean that the measured noise is simply something else and the experiment is far from being finished?

Is there another method for calculating likelihood function which is somewhat in the midway between the two I have tried?

Is the strong condition in likelihood function that "if estimated noise is more than measured noise, return zero" not a good assumption?

I talked to Kevin and he suggested a simpler straight forward Bayesian Analysis for the result. Following is the gist:

Since Shear Loss Angle's contribution is so little to the coatings' brownian noise, there is no point in trying to estimate it from our experiment. It will be unconstrained in the search always and would simply result in the whatever prior distribution we will take.

So, I accepted defeat there and simply used Shear Loss Angle value estimated by Penn et al. which is 5.2 x 10^{-7}.

So now the Bayesian Analysis is just one dimensional for Bulk Loss Angle.

Kevin helped me inrealizing that error bars in the estimated noise are useless in bayesian analysis. The model is always supposed to be accurate.

So the log likelihood function would be -0.5*((data - model)/data_std)**2) for each frequency bin considered and we can add them all up.

Going to log space helped a lot as earlier probablitis were becoming zero on multiplication but addition of log likelihood is better between different frequencies.

I'm still using the hard condition that measured noise should never be lower than estimated noise at any frequency bin.

Finally, the estimated value is quoted as the most likely value with limits defined by the region covering 90% of the posterior probability distribution.

This gives us:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

Now this isn't a very good result as we would want, but this is the best we can report properly without garbage assumptions or tricks. I'm trying to see if we can get a lower noise readout in next few weeks, but otherwise, this is it, CTN lab will rest afterward.

I realized that using only the cleaned out frequencies and a condition that estimated power never goes above them at those places is double conditioning. In fact, we can just look at a wide frequency band, between 50 Hz to 600 Hz and use all data points with a hard ceiling condition that estimated noise never goes above the measured noise in any frequency bin in this region. Surprisingly, this method estimates a lower loss angle with more certainty. This happened because, 1) More data points are being used and 2) As Aaron pointed out, there were many useful data bins between 50 Hz and 100 Hz. I'm putting this result separately to understand the contrast in the results. Note that still we are using a uniform prior for Bulk Loss Angle and shear loss angle value from Penn et al.

The estimate of the bulk loss angle with this method is:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval. This result has an entire uncertain region from Penn et al. within it.

Which is a more fair technique: this post or CTN:2574 ?

Today we measured further low noise beatnote frequency noise. I reran the two notebooks and I'm attaching the results here:

Bayesian Analysis with frequency cleaning:

This method only selects a few frequency bins where the spectrum is relatively flat and estimates loss angle based on these bins only. This method rejects any loss angle vaue that results in estimated noise more than measured noise in the selected frequency bins.

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

Bayesian Analysis with Hard Ceiling:

This method uses all frequency bins between 50 H and 600 Hz and uses them to estimate loss angle value This method rejects any loss angle value that results in estimated noise more than measured noise in the selected frequency bins.

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

I'm listing first few comments from Jon that I implemented:

Data cleaning can not be done by looking at the data itself. Some outside knowledge can be used to clean data. So, I removed all the empirical cleaning procedures and instead just removed frequency bins of 60 Hz harmonics and their neighboring bins. With HEPA filters off, the latest data is much cleaner and the peaks are mostly around these harmonics only.

I removed the neighboring bins of 60 Hz harmonics as Jon pointed out that PSD data points are not independent variables and their correlation depends on the windowing used. For Hann window, immediate neighbors are 50% correlated and the next neighbors are 5%.

The Hard ceiling approach is not correct because the likelihood of a frequency bin data point gets changed due to some other far away frequency bin. Here I've plotted probability distributions with and without hard ceiling to see how it affects our results.

Bayesian Analysis (Normal):

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

Note that this allows estimated noise to be more than measured noise in some frequency bins.

Bayesian Analysis (If Hard Ceiling is used):

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

Remaining steps to be implemented:

There are more things that Jon suggested which I'm listing here:

I'm trying to catch next stable measurement with saving the time series data.

The PSD data points are not normal distributed since "PSD = ASD^2 = y1^2 + y2^2. So the PSD is the sum of squared Gaussian variables, which is also not Gaussian (i.e., if a random variable can only assume positive values, it's not Gaussian-distributed)."

So I'm going to take PSD for 1s segements of data from the measurement and create a distribution for PSD at each frequency bin of interest (50Hz to 600 Hz) at a resolution of 1 Hz.

This distribution would give a better measure of likelihood function than assuming them to be normal distributed.

As mentioned above, neighboring frequency bins are always correlated in PSD data. To get rid of this, Jon suggested following

"the easiest way to handle this is to average every 5 consecutive frequency bins.

This "rebins" the PSD to a slightly lower frequency resolution at which every data point is now independent. You can do this bin-averaging inside the Welch routine that is generating the sample distributions: For each individual PSD, take the average of every 5 bins across the band of interest, then save those bin-averages (instead of the full-resolution values) into the persistent array of PSD values. Doing this will allow the likelihoods to decouple as before, and will also reduce the computational burden of computing the sample distributions by a factor of 5."

I'll update the results once I do this analysis with some new measurements with time-series data.

I've implemented all the proper analysis norms that Jon suggested and are mentioned in the previous post. Following is the gist of the analysis:

All measurements taken to date are sifted through and the sum of PSD bins between 70 Hz to 600 Hz (excluding 60 Hz harmonics and region between 260 Hz to 290 Hz (Known bad region)) is summed. The least noise measurement is chosen then.

If time-series data is available (which at the moment is available for lowest noise measurement of May 29^{th} taken at 1 am), following is done:

Following steps are repeated for the frequency range 70 Hz to 100 Hz and 100 Hz to 600 Hz with timeSegement values 5s and 0.5s respectively.

The time series data is divided into pieces of length timeSegment with half overlap.

For each timeSegment welch function is run with npersegment equal to length of time series data. So each welch function returns PSD for corresponding timeSegement.

In each array of such PSD, rebining is done by taking median of 5 consecutive frequency bins. This makes the PSD data with bin widths of 1 Hz and 10 Hz respectively.

The PSD data for each segement is then reduced by using only the bins in the frequency range and removing 60 Hz harmonics and the above mentioned bad region.

Logarithm of this welch data is taken.

It was found that this logarithm of PSD data is close to Gaussian distributed with a skewness towards lower values. Since this is logarithm of PSD, it can take both positive and negative values and is a known practice to do to reach to normally distributed data.

A skew-normal distribution is fitted to each frequency bin across different timeSegments.

The fitted parameters of the skew-normal distribution are stored for each frequency bin in a list and passed for further analysis.

Prior distribution of Bulk Loss Angle is taken to be uniform. Shear loss angle is fixed to 5.2 x 10^{-7} from Penn et al..

The Log Likelihood function is calculated in the following manner:

For each frequency bin in the PSD distribution list, the estimated total noise is calculated for the given value of bulk loss angle.

Probability of this total estimated noise is calculated with the skew-normal function fitted for each frequency bin and logarithm is taken.

Each frequency bin is supposed to be independent now since we have rebinned, so the log-likelihood of each frequency bin is added to get total log-likelihood value for that bulk loss angle.

Bayesian probability distribution is calculated from sum of log-likelihood and log-prior distribution.

Maximum of the Bayesian probability distribution is taken as the most likely estimate.

The upper and lower limits are calculated by going away from most likely estimate in equal amounts on both sides until 90% of the Bayesian probability is covered.

Final result of CTN experiment as of now:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

The analysis is attached. This result will be displayed in upcoming DAMOP conference and would be updated in paper if any lower measurement is made.

Final result of CTN experiment as of June 4th 9 am:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

The analysis is attached. This result will be displayed in upcoming DAMOP conference and would be updated in paper if any lower measurement is made.

Adding Effecting Coating Loss Angle (Edit Fri Jun 5 18:23:32 2020 ):

If all layers have an effective coating loss angle, then using gwinc's calculation (Yam et al. Eq.1), we would have effective coating loss angle of:

This is worse than both Tantala (3.6e-4) and Silica (0.4e-4) currently in use at AdvLIGO.

Also, I'm unsure now if our definition of Bulk and Shear loss angle is truly same as the definitions of Penn et al. because they seem to get an order of magnitude lower coating loss angle from their bulk loss angle.

I realized that in my noise budget I was using higher incident power on the cavities which was the case earlier. I have made the code such that now it will update photothermal noise and pdhShot noise according to DC power measured during the experiment. The updated result for the best measurement yet brings down our estimate of the bulk loss angle a little bit.

Final result of CTN experiment as of June 11th 2 pm:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

The analysis is attached.

Adding Effecting Coating Loss Angle (Edit Fri Jun 5 18:23:32 2020 ):

If all layers have an effective coating loss angle, then using gwinc's calculation (Yam et al. Eq.1), we would have an effective coating loss angle of:

This is worse than both Tantala (3.6e-4) and Silica (0.4e-4) currently in use at AdvLIGO.

Also, I'm unsure now if our definition of Bulk and Shear loss angle is truly the same as the definitions of Penn et al. because they seem to get an order of magnitude lower coating loss angle from their bulk loss angle.

I figured out why folks befor eme had to use a different definition of effective coating coefficent of thermal expansion (CTE) as a simple weighted average of individual CTE of each layer instead of weighted average of modified CTE due to presence of substrate. The reason is that the modification factor is incorporated in another parameter gamma_1 and gama_2 in Farsi et al. Eq, A43. So they had to use a different definition of effective coating CTE since Farsi et al. treat it differently. That's my guess anyway since thermo-optic cancellation was demonstrated experimentally.

Quote:

Adding more specifics:

Discrepancy #1

Following points are in relation to previously used noisebudget.ipynb file.

One can see the two different values of effective coating coefficient of thermal expansion (CTE) at the outputs of cell 9 and cell 42.

For thermo-optic noise calculation, this variable is named as coatCTE and calculated using Evans et al. Eq. (A1) and Eq. (A2) and comes out to (1.96 +/- 0.25)*1e-5 1/K.

For the photothermal noise calculation, this variable is named as coatEffCTE and is simply the weighted average of CTE of all layers (not their effective CTE due to the presence of substrate). This comes out to (5.6 +/- 0.4)*1e-6 1/K.

The photothermal transfer function plot which has been used widely so far uses this second definition. The cancellation of photothermal TF due to coating TE and TR relies on this modified definition of effective coating CTE.

In my new code, I used the same definition everywhere which was the Evans et al. Eq. (A1) and Eq. (A2). So the direct noise contribution of coating thermo-optic noise matches but the photothermal TF do not.

To move on, I'll for now locally change the definition of effective coating CTE for the photothermal TF calculation to match with previous calculations. This is because the thermo-optic cancellation was "experimentally verified" as told to me by Rana.

The changes are done in noiseBudgetModule.py in calculatePhotoThermalNoise() function definition at line 590 at the time of writing this post.

Resolved this discrepancy for now.

Quote:

The new noise budget code is ready. However, there are few discrepancies which still need to be sorted.

Please look into How_to_use_noiseBudget_module.ipynb for a detailed description of all calculations and code structure and how to use this code.

Discrepancy #1

In the previous code, while doing calculations for Thermoelastic contribution to Photothermal noise, the code used a weighted average of coefficients of thermal expansion (CTE) of each layer weighted by their thickness. However, in the same code, while doing calculations for thermoelastic contribution to coating thermo-optic noise, the effective CTE of the coating is calculated using Evans et al. Eq. (A1) and Eq. (A2). These two values actually differ by about a factor of 4.

Currently, I have used the same effective CTE for coating (the one from Evans et al) and hence in new code, prediction of photothermal noise is higher. Every other parameter in the calculations matches between old and new code. But there is a problem with this too. The coating thermoelastic and coating thermorefractive contributions to photothermal noise are no more canceling each other out as was happening before.

So either there is an explanation to previous codes choice of using different effective CTE for coating, or something else is wrong in my code. I need more time to look into this. Suggestions are welcome.

Discrepancy #2

The effective coating CTR in the previous code was 7.9e-5 1/K and in the new code, it is 8.2e-5 1/K. Since this value is calculated after a lot of steps, it might be round off error as initial values are slightly off. I need to check this calculation as well to make sure everything is right. Problem is that it is hard to understand how it is done in the previous code as it used matrices for doing complex value calculations. In new code, I just used ucomplex class and followed the paper's calculations. I need more time to look into this too. Suggestions are welcome.

Final result of CTN experiment as of June 15th 5 pm:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

The analysis is attached.

Adding Effecting Coating Loss Angle (Edit Fri Jun 5 18:23:32 2020 ):

If all layers have an effective coating loss angle, then using gwinc's calculation (Yam et al. Eq.1), we would have an effective coating loss angle of:

This is worse than both Tantala (3.6e-4) and Silica (0.4e-4) currently in use at AdvLIGO.

Also, I'm unsure now if our definition of Bulk and Shear loss angle is truly the same as the definitions of Penn et al. because they seem to get an order of magnitude lower coating loss angle from their bulk loss angle.

Final result of CTN experiment as of June 23 5 pm:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

The analysis is attached.

Adding Effecting Coating Loss Angle (Edit Fri Jun 5 18:23:32 2020 ):

If all layers have an effective coating loss angle, then using gwinc's calculation (Yam et al. Eq.1), we would have an effective coating loss angle of:

This is worse than both Tantala (3.6e-4) and Silica (0.4e-4) currently in use at AdvLIGO.

Also, I'm unsure now if our definition of Bulk and Shear loss angle is truly the same as the definitions of Penn et al. because they seem to get an order of magnitude lower coating loss angle from their bulk loss angle.

Final result of CTN experiment as of June 24 9 pm:

with shear loss angle taken from Penn et al. which is 5.2 x 10^{-7}. The limits are 90% confidence interval.

The analysis is attached.

Adding Effecting Coating Loss Angle (Edit Fri Jun 5 18:23:32 2020 ):

If all layers have an effective coating loss angle, then using gwinc's calculation (Yam et al. Eq.1), we would have an effective coating loss angle of:

This is worse than both Tantala (3.6e-4) and Silica (0.4e-4) currently in use at AdvLIGO.

Also, I'm unsure now if our definition of Bulk and Shear loss angle is truly the same as the definitions of Penn et al. because they seem to get an order of magnitude lower coating loss angle from their bulk loss angle.

I added the possibility of having a power-law dependence of bulk loss angle on frequency. This model of course matches better with our experimental results but I am honestly not sure if this much slope makes any sense.

Auto-updating Best Measurement analyzed with allowing a power-law slope on Bulk Loss Angle:

RXA: I deleted this inline image since it seemed to be slowing down ELOG (2020-July-02)

Major Questions:

What are the known reasons for the frequency dependence of the loss angle?

Do we have any prior knowledge about such frequency dependence which we can put in the analysis as prior distribution?

Is this method just overfitting our measurement data?

I followed the analysis of this recently published paper Jan Meyer et al 2022 Class. Quantum Grav. 39 135001 to calculate the birefringence noise in the CTN experiment. Interestingly, the contribution from birefringence noise after my first attempt at this calculation looks very close to what we were calculating as coating thermo-refractive noise before. If this were true, our experiment would have seen it much before. In fact, we wouldn't have seen thermo-optic cancellation as Tara experimentally verified here. So something is missing

What is birefringence noise?

After going through some literature and reading properly Meyer et al, I have the following understanding of the birefringence noise (and why it is called so).

The temperature fluctuations cause length fluctuations in the coating layers (through the coefficient of thermal expansion)

The length fluctuations cause stress fluctuations in the coating layers (through Young's modulus Y).

The stress fluctuations get converted into refractive index fluctuations through the photoelastic effect (through photoelastic tensor)

This induces refractive index fluctuations that are different for the fast and slow axes. The difference between the two fluctuations causes a phase shift in reflected light from each layer. That's why this can be birefringence noise. In an unstressed isotropic material, this pathway should not exist.

Is this different from thermo-refractive noise?

This is a question I am still not sure how to answer. My understanding is that the common mode change in refractive indices of both axes drives the thermo-refractive noise. This means I should be able to derive the coefficient of thermo-refraction using the same formalism.

Calculation:

Both thermo-refractive noise and thermo-photoelastic noise show up as dn/dT terms in the thermo-optic noise summation, just through different physical processes. This could mean that experimentally measured coefficients of thermo-refraction already include birefringent contribution if any. In my calculations for the plots presented here, I got the following values of the two coefficients:

Coefficient of thermo-refraction (Effective for coating): 8.289e-05

Coefficient of thermo-photoelastic effect (Effective for coating, using Eq.11 of Meyer et al.): 8.290e-05

It was very surprising to me to see that both these coefficients came out to be within 1% of each other.

Because of this, when we add the noise sources coherently (since they are all driven by the same thermal fluctuations), the thermo-optic cancellation that we have experimentally proved does not work anymore. So something must be wrong with my calculation.

Possible explanations:

Calculaiton error in my code. I'll double check tomorrow.

Somehow the thermorefractive noise already takes into account the birefringent noise, through the coefficient of thermo-refraciton that we use as seed in our thermo-refractive noise calculation. This would explain how the witnessed themo-optic cancellation was achieved.

Meyer et al. is calculating birefringent noise for the substrate. Maybe the tensorial calculations are different for coatings.

I made a few changes in my calculations today, which changed the noise contribution of this photoelastic noise (coatTPE) to roughly half of the individual contribution from coating thermo-refractive (coatTR). If this was true, it would significantly affect thermo-optic optimization, although not totally destroying it. I admit there is an outcome bias in this statement, but this noise estimate fits very well with the noise floor measured by CTN lab.

Changes in the calculation:

I made two changes in total:

I'm using original coefficients of thermal expansion for each layer instead of the "effective" coefficients used in calculations of thermo-optic noise as per Evans et al. PRD 78, 102003 (2008)

I removed the use of young's modulus and the crystal's elasticity tensor.

So now, the noise calculation is as follows:

The temperature fluctuations cause isotropic strain fluctuations in the coating layers related through coefficient of thermal expansion

The strain fluctuations cause changes in the refractive index of the layers through photoelastic tensor

In the last step above, I assumed isotropic bulk strain in the layers (which is expected for this cubic lattice), thus

The product of the above two numbers give the coefficient of thermo-photoelastic effect as:

I averaged this coefficient over all coating layers weighted by their thicknesses.

The noise contribution comes same as coatTR term as they both are channels causing dn/dT.

Notes:

The above calculation does not take into account any birefringence in the layers that could be caused by this effect. In fact, the cubic crystal symmetry of GaAs does not allow for birefringence to occur in usual formalism and the only way it could happen is due to a large strain in one direction breaking the symmetries. Thus, I would not call this noise "birefringence noise", but it is a credible noise source in it's own right.

Note that the themo-optic cancellation is only partially happening now, but the thermo-optic noise is still much less than the simple quadrature sum of the noises. We can maybe check back our measurements in our previous paper if the measured photothermal transfer function allows this.

Maybe this noise source is not perfectly coherent with coatTE and coatTR and needs to be added a bit differently.

About the plot:

The trace marked "Coating Thermo-Optic" is a coherently summed noise of coatTR, coatTE, and coatTPE.

The trace marked "Coating Thermo-elastic + Thermo-refractive" is what we previously used to calculate as thermo-optic noise.

"Measured Beat" is the best measurement we made and is a median over 50 lowest noise measurements made in June of 2020.

"Coating Brownian" trace is calculated using bulk loss angle value of 4.878e-5 which was measured by Penn et al. in indirect measurement.

I think we need to regroup and discuss this further.

The obvious go to measurment here would be two-lasers-one-cavity to measure the residual between the two polarisaiton modes of one of the cavities. Is the experiment in a state where this could be done easily?

If I recall correctly Tara had this set up with an optical circulator on the input side which Antonio and I switched to linear polarisasion with Faraday isolator. The mode splitting of the AlGaAs coatings would take care of only selecting one polarisation mode, but is it posisble that the latter measurments sampled a different polarisation to the original thermo-optic measurment? Just a thought.

The photothermal transfer function measurement made back in 2014 showed some cancellation of thermo-optic noise, but there were some irregularities with the modelled transfer function even back then. Here in attachment 1, I have plotted the measured photothermal transfer function, along with the estimated transfer function with and without adding a term for thermal photoelastic (TPE) channel.

Notes:

The estimated transfer function without TPE (as was estimated back then) does match well with the measured transfer function on the south cavity below 200 Hz.

However, the north cavity measurement did not match well.

The estimated transfer function with TPE (green) is in between south and north measurements at least in magnitude above 200 Hz.

However, the phase of estimated transfer functions (with or without TPE) do not match well with any of the measurements. This phase discrepancy is worrisome.

Looking at these estimated transfer functions and measured transfer functions, which model do you think explains the measured data better?

Updated noise budget:

I was wondering if photothermal noise would get amplified due to the TPE effect. We were not using a measured photothermal transfer function in our noise budget for this noise contribution and relied on a theoretical model instead. For comparison, I added noise traces for three cases, Estimated photothermal noise with and without PTE, and photothermal noise using measured TF. In all these cases though, the ISS in the experiment suppressed RIN enough that photothermal noise did not matter to beatnote frequency noise.

The obvious go to measurment here would be two-lasers-one-cavity to measure the residual between the two polarisaiton modes of one of the cavities. Is the experiment in a state where this could be done easily?

Not easily, but it is doable if we resurrect the south path only. I estimate ~1 month of work for that if things go fine.

Quote:

If I recall correctly Tara had this set up with an optical circulator on the input side which Antonio and I switched to linear polarisasion with Faraday isolator. The mode splitting of the AlGaAs coatings would take care of only selecting one polarisation mode, but is it posisble that the latter measurments sampled a different polarisation to the original thermo-optic measurment? Just a thought.

With circularly polarized light, Tara could be addressing any of the two possible resonances, with only effect of suffering in modematching with the cavity. So it should be a 50/50 chance that they measured it in a different polarization. However, the nature of thermal photoelastic measurement is same in both polarizations. The photoelastic tensor for GaAs (cubic symmetry), in theroy, does not create birefringence, or afect different polarizations differently. The source of birefringence in these coatings is not known.

Martin Fejer recently gave two talks in a coatings workshop where he showed calculations regarding the thermal photoelastic channel. I have not been able to under the logic behind some of the calculations yet, nevertheless, I used his formulas for our coatings to get an alternative idea of this noise coupling.

Major difference

Fejer argues that free body thermal expansion does not generate any strain, and it is only when the substrate is present to counteract with it, that such strain is generated.

Hence, the calculation goes as: thermal expansion -> stress in presence of substrate -> strain -> photoelastic effect.

So instead of the simple contribution for photoelastic tensor and thermal expansion that I take, the term is:

This gives an effective (averaged with layer thickness weighting) coefficient of thermal photoelasticity of 1.45e-5 K^{-1} instead of 4.30e-5 K^{-1} from my calculations. That's a reduction by a factor of roughly 3.

Updates

Attached is the photothermal transfer function calculated with TPE contribution as calculated by Fejer. This makes the situation bit more messy on what to trust.

I updated the noise budget with two new noise traces, the thermo-photoelastic contribution as calculated by Fejer and the total thermo-optic noise as calculated by Fejer.

I just received more calculation notes of Fejer (through Yuta) which I'll study and try to make more sense of this calculation. It also contains the calculations of sough-after birefringence noise.. But in his presentation as well, he stated that birefringence noise is not sourced through termperature fluctuations and is not part of thermo-optic noise (something I didn't understand again).

I had some stuff to write up about modematching in the south path. But after looking in the far field I realised there was some clipping somewhere. It turns out that the Farday is mounted slightly too high for our standard 3" height. I will switch it out presently and continue matching the path with a FI with a slightly lower height.

We should probably look getting the mount machiened down by about 1 mm.

A couple of mode matching solutions for the north cavity that look promising have been found.
I'm thinking the following plan 2c to be implemented.

introduction

- We'll use the PMC in each path
- We also need to insert a FI in each path (to use the reflected light from the cavities)
- EOMs after the PMC will be inserted for the in-vacuum cavities PDH

These constrains the mode macthing to be done with the use of three lenses. One to focus the beam
into the BB EOM and the other two to mode match the North cavity.

Approach

Question1: Can we place the FI without changing the mode matching solution?

Answer: In Plan1 the profile caluclation is shown. As you can find there, considering that
the maximum distance from the waist of the PMC for the FI is ~ 1.32m (FI length ~ 10cm)
we have a diameter around ~2mm.

Question2: OK. We need to use some focusing lenses. How strong will they be?

Answer: In Plan2-a/b/c the profile caluclations with the sensitivity to the displacement of the lenses
are shown. As you can find there, we have at the FI a beam radius that is around ~750um at most.
However the three setups show a different sensitivity with Plan2a and 2c being lens sensitive to lens
displacement compared to 2b.

Conclusion

Along with the discussion above, I will use 2c. (or 2a looks applicable too)

For all the profiles the reference point is the waist at the PMCc (330um), zero point in the plots
and the cavity waist is located at 1.96m far from the PMC waist.

Plan 1: FI after the two MM lenses

Setup

In this case we have 3 lenses of focal "fi"(mm) located at "li"(m):

l1 = 0.16;

l2 = 0.762;

l3 = 1.107;

f1 = 0.1432;

f2 = 0.688;

f3 = 0.572;

Beam Profile

If we want to "risk" a 2 mm diameter beam into the FI.

The following plans 2(a,b,...) have all the FI in the between the two MM lenses. I just report

one figure with the setup:

Plan 2a:

Setup:

l1 = 0.183;

l2 = 0.773;

l3 = 1.32;

f1 = 0.229;

f2 = 0.143;

f3 = 0.229;

Beam Profile

We can place the FI around 1.2m or further than the North cavity. The further we go and the smaller is the beam

until we reach the waist at 0.9m.

Sensitivity of lenses displacement

Dipending on which directions we move the lenses we may have 20% mismatch with a displacement of ~4cm for lens 2

while for Lens 3 only few percent.

Plan 2b:

Setup:

l1 = 0.117;

l2 = 0.951;

l3 = 1.313;

f1 = 0.229;

f2 = 0.143;

f3 = 0.143;

Beam Profile

Sensitivity

Plan 2c:

Setup

l1 = 0.148;

l2 = 0.683;

l3 = 1.325;

f1 = 0.1432;

f2 = 0.1719;

f3 = 0.229;

Beam Profile

Sensitivity

This shows to be less sensitive to the lens displacement, compared to the others. Furthermore we notice that the two lenses are somehow indipendent as the curve are more circular;

There is something not ok with the Gouy phase, I need to cross check what is wrong there. I should fix this doubt later, for now it is not important.

I would propose plane 2c

Data:

Data are currently stored in a shared Box Inc folder, but we may wanto create an svn folder for all our data.

Motivation
I have realized that I made a mistake measuring the distance of the North cavity waist from the PMC (waist).
I have done the same analysis presented in ID 1660 and adjusted the plan.

Conclusion
A new set of lenses has been found respecting all the constraints given in ID 1660

Setup
The waist of the North cavity is located at 1.701m far from the PMC waist. The size is 210um.
The chosen lenses focal lens f"i" (m) located at l"i"(m) are:

I have put down and pulled up the first section of the south path a few times. I've developed a habbit of packing optics in at close range and we decided that this was not so great when we had plenty of space. Starting at the begining again I had another go at measuring the mode strait out of the laser. Data is attached below and z0 = 0 is referenced to the front of the laser head.

I changed the power at point 8 and there seems to be a distict change in slope there. There are two waveplates, a PBS (which I think is UV silica) and a W2 coated window that is definitly fused silica.

This data is much cleaner than earlier measurment and I'm not sure if the change in waist (for the measurment) is enought to be worried about. I will use these values for subsqutent modematching.

Horz. beam waist = 193.4873 um
Horz. beam waist position = 27.7636 mm
Vert. beam waist = 139.5525 um
Vert. beam waist position = 34.6003 mm

I've mapped out a path for the south laser beam (draft attached). I've left the final stages until I have placed and measured the final modulator to get the most accurate MM solution possible. z values are referenced to the laser head and quoted waists are the mean of the two axis. After placing the first lens I took another beam profile. Its not so great for the vertical nearer the waist. The fitted values are

Horz. beam waist = 250.5078 um
Horz. beam waist position = 1051.8195 mm
Vert. beam waist = 191.9869 um
Vert. beam waist position = 1069.7957 mm

Here I used a W2-PW1-1037-UV-1064-45P wedge and a 1" PBS-1064-100 (BK7 unfortually, but good enough for a quick measurment).

The second EOM (an amplitude modulator: Newfocus-4104) was placed at the next waist and optics installed were lambda/2->AEOM(4104)->PBS. Location of the AEOM (referenced to laser head) was 1012 mm.

The beam was reameasured after this point (as a check) with a AR coated window pickoff. Fit was:

Horz. beam waist = 183.5091 um
Horz. beam waist position = 957.1859 mm
Vert. beam waist = 226.7887 um
Vert. beam waist position = 856.7048 mm.

Accounting for the AEOM and PBS length and RI this is pretty much right for placement of the AEOM.

A PLCX-25.4-64.4-UV-1064 (f = 143.23 mm) lens was placed in the path at z = 1247 mm. The order of components after the AEOM was (Space for waveplate)->PBS->Steering Mirror->Lens->lambda/2->EOM2. The lens placement was very clost to the steering mirror, but it was difficult to find a choice of lens that would accommodate a suitably focused solution.

This final EOM (before the PMC) was placed at z = 1440 mm (ref. to laser head position).

The beam was profiled after the EOM2 to get better characteristics for MM to the PMC. The fit was:

Horz. beam waist = 246.0624 um
Horz. beam waist position = 1397.5481 mm
Vert. beam waist = 210.7356 um
Vert. beam waist position = 1252.1215 mm

The waist was set a little bigger to ease the MM placement sensitivity of the first lens for matching into the PMC. Data and plot attached.

Next MM to the PMC (although this wont be put in place until after we have gotten a first beat note).

I was concerned about some of the spacial features I was seeing after the second broadband EOM. On closer inspection there was a small fleck of what looked like plastic tape in the input aperture (pictured).

Fleck of plastic, now removed

I removed the fleck and it looks all clear now.

Also, I thought maybe the beam was just a the limit of size for one axis. I moved the lens (PLCX-25.4-64.4-UV-1064) forward to z = 1252 mm. The re measured beam had the fitted characteristics:

Horz. beam waist = 194.3474 um
Horz. beam waist position = 1472.415 mm
Vert. beam waist = 140.8421 um
Vert. beam waist position = 1418.9487 mm

I made some further alignment adjustments of the modulators and some changes to the polarization inputs and outputs. A lambda/2 wave plate was installed directly after the AEOM (for now) so that the PBS could be manually tuned to the 50% transmission point for s- polarisation into the AEOM. For now we will ignore the circular polarization generated by the AEOM and the small amount introduced by the previous EOM.

After checking the field after first EOM I determined that the residual polarization was 108 uW out of 83.4 mW or 0.13 %. Without the EOM installed the extinction was down to ~10 uW. For now this level of circular polarization should be tolerable. It is something we can optimize later.

I also realigned (again) the AEOM and 2nd EOM using Antonio's methods. This gave a satisfactory looking Gaussian beam. The profile was again remeasured. Its fitted values are:

Horz. beam waist = 259.6243 um
Horz. beam waist position = 1436.9167 mm
Vert. beam waist = 215.7146 um
Vert. beam waist position = 1319.3657 mm

I placed a pair of lenses and a cylindrical lens in the path after the final EOM before the PMC location to provide a MM solution close to that of the PMC when we eventurally impliment this. The goal was 330 um waist. The PMC base was bolted in position and with a quick alignment the cavity was scanned to see how well it will mode match when we install. Visablity was found to be 84.4 % (with 1.000 V off resonance and a dip down to 156 mV on reflection). All this is so that we have a fair idea of the MM solution and placement for later installation.

I took the PMC out today and took a proper beam profile referenced to the steering mirror just before the PMC. Data and plot of fit are attached the fitted profile values were:

Horz. beam waist = 256.7996 um
Horz. beam waist position = 2635.8799 mm
Vert. beam waist = 211.6388 um
Vert. beam waist position = 2538.9972 mm
--
Mean beam waist = 234.2192 um
Mean beam waist position = 2587.4386 mm

However, looking at the plot it looks like the fit overshoots the actual measurments close to the waist. It may be that the large distance measurments bias the measurment (and there are more of them). But the waist was definitly located closer to the reference point at which the PMC base was placed yesterday. I haven't modeled it but I find a visablity of 84 % for a waist of 234 um hard to belive if the PMC cavity is designed for a 330 um. For now it is probably ok to assume 330 um for this next modematching step.

Next final MM to the south cavity. We expect that this should take to the end of today.

Correction: Wrong plot (at least the x-scale is wrong). The updated one is attached.

Also the offset of the data from the laser head position is 2698 mm.

Quote:

I placed a pair of lenses and a cylindrical lens in the path after the final EOM before the PMC location to provide a MM solution close to that of the PMC when we eventurally impliment this. The goal was 330 um waist. The PMC base was bolted in position and with a quick alignment the cavity was scanned to see how well it will mode match when we install. Visablity was found to be 84.4 % (with 1.000 V off resonance and a dip down to 156 mV on reflection). All this is so that we have a fair idea of the MM solution and placement for later installation.

I took the PMC out today and took a proper beam profile referenced to the steering mirror just before the PMC. Data and plot of fit are attached the fitted profile values were:

Horz. beam waist = 256.7996 um
Horz. beam waist position = 2635.8799 mm
Vert. beam waist = 211.6388 um
Vert. beam waist position = 2538.9972 mm
--
Mean beam waist = 234.2192 um
Mean beam waist position = 2587.4386 mm

However, looking at the plot it looks like the fit overshoots the actual measurments close to the waist. It may be that the large distance measurments bias the measurment (and there are more of them). But the waist was definitly located closer to the reference point at which the PMC base was placed yesterday. I haven't modeled it but I find a visablity of 84 % for a waist of 234 um hard to belive if the PMC cavity is designed for a 330 um. For now it is probably ok to assume 330 um for this next modematching step.

Next final MM to the south cavity. We expect that this should take to the end of today.

I am missing the target here. The size is 330um, but I did not get the waist target location.

Quote:

I placed a pair of lenses and a cylindrical lens in the path after the final EOM before the PMC location to provide a MM solution close to that of the PMC when we eventurally impliment this. The goal was 330 um waist. The PMC base was bolted in position and with a quick alignment the cavity was scanned to see how well it will mode match when we install. Visablity was found to be 84.4 % (with 1.000 V off resonance and a dip down to 156 mV on reflection). All this is so that we have a fair idea of the MM solution and placement for later installation.

I took the PMC out today and took a proper beam profile referenced to the steering mirror just before the PMC. Data and plot of fit are attached the fitted profile values were:

Horz. beam waist = 256.7996 um
Horz. beam waist position = 2635.8799 mm
Vert. beam waist = 211.6388 um
Vert. beam waist position = 2538.9972 mm
--
Mean beam waist = 234.2192 um
Mean beam waist position = 2587.4386 mm

However, looking at the plot it looks like the fit overshoots the actual measurments close to the waist. It may be that the large distance measurments bias the measurment (and there are more of them). But the waist was definitly located closer to the reference point at which the PMC base was placed yesterday. I haven't modeled it but I find a visablity of 84 % for a waist of 234 um hard to belive if the PMC cavity is designed for a 330 um. For now it is probably ok to assume 330 um for this next modematching step.

Next final MM to the south cavity. We expect that this should take to the end of today.

I measured the beam as it would enter the third and final EOM after the PMC (note that the PMC was removed from the path for now). The first PLCX-25.4-64.4-UV-1064 (f = 143.23 mm) was placed at 2769.5 mm from the laser head (see attached updated map of south path). The beam profile measurements are attached as txt file along with plot. The z = 0 reference point is the first bolt on the second table or 2815 mm referenced from the laser head.

The fit of the data was:

Horz. beam waist = 112.7457 um
Horz. beam waist position = 2908.1548 mm
Vert. beam waist = 115.3321 um
Vert. beam waist position = 2940.4081 mm
--
Mean beam waist = 114.0389 um
Mean beam waist position = 2924.2815 mm

It appears that the actual beam waist is 150 um and 166 um in horizontal and vertical respectively for the data. (At least if we trust the D4σ fit).

NOTE ON D4σ METHOD:

It seems that the CCD measurements close to the waist don't fit well with the data at a large distance. I am using the D4σ definition of beam width. This should be the same as 1/e^2 clip method when dealing with Gaussian beams. However, it is possible that small beams have biased results from dark noise + offsets in pixels well outside the beam that weight the integral of the beam profile. This may be a deficiency in this method. At some stage I should check how to get the best possible pre calibration for the CCD baseline.

A mode matching solution was found for the beam to be coupled into the south cavity.

With lengths referenced to the first hole in the second table (2815 mm from the laser head)

f = 143.23 mm (PLCX-25.4-64.4-UV-1064) @ 0.148 m

f = 103.20 mm (PLCX-25.4-46.4-UV-1064) @ 0.589 m

f = 171.92 mm (PLCX-25.4-77.3-UV-1066) @ 0.974 m

A small alteration was made as we settled on the final solution, the first lens was shifted back to the 0.100 m mark with a commensurate shift in the other lenses. The effect of this move was move the first waist (and the position of the EOM back a couple of bolt holes. The change in size of the first waist was small so the solution remained the same with small tweaks to the second and third lens positions.

In order to fit the components into the vacuum tank and get a beat note as soon as possible we opted to route the beam along a different route to the north path. The path is shown with positions of components in the attached schematic. Lenses were mounted on linear translations stages for fine alignment and the Faraday isolator polarization axis was slightly altered to give a return path beam that was parallel to the table. The way the Thorlabs FI come from the manufacture is such that the input polarization is optimized for horizontal polarization input, rather than reflection in the plane of the beam.

With the changes to the end PBS rotation we re measured the through put power and reverse power attenuation. Out of 9.05 mW incident power the forward propagating output was 8.75 mW: this is a 3.3 % loss. The reverse power throughput was 3.062 uW out of 9.01 mW (we rotated through all input polarization and chose the maximum value): this is a 34.7 dB degree of isolation for back reflection.

A quick measurement of the return path efficiency (of back reflected light extracted from the first FI's first PBS port for PDH locking of the cavity) was 8.07 mW from a total of 9.01 mW or 10.4 % loss. This was a quick measurement, and maybe something we might like to confirm later.

---

All the components up the periscope have been aligned with their heights and centering checked. I did a quick walk of the lenses to see if I could find a waist of 220 um located at the expected point for the cavity (checked with a flipper mirror on the table). I ran out of range on the second lens (it needs to be moved back more). However, the solution is pretty close now.

Also, we need to check the beam waist fitting method (see note PSL_Lab/1680), it may be necessary to do a baseline subtraction of the dark CCD detector to be able to use the D4σ method with confidence. Otherwise double check the the 1/e^2 clipping option in the WinCamD software; you can get the software to display both at once. We should compare tight waists to beams much further out so see how the two methods scale.

Summary
Following the previous entry the South path construction was at the point where mode matching was needed for the South Cavity.
We also needed to install a resonant photodiode for the PDH lock and start to prepare the optic in transmission.

Coonclusions

The light is resonating into the South Cavity with a visibility = (Vmax-Vmin)/Vmax = ~ 0.75.

We also have the resonant PD for the light reflected from the cavity.

Camera and ISS PD in transmission of the South cavity have been aligned too.

All the cabeling are hooked, but they need to be tidied up.

Note:

Lenses have been adjusted and slightly changed compared to the previous entry.

The alignment of the cavity took me a while. The mounts for the steering mirrors on the
periscope are very sensitive, here the alignment requires a bit of more attention.

All power supply and cables are connected. I just need to verify the HV power supply settings.

Today I set up the North path to do some proper mode matching using the beam profiler.

awade has been fighting the RFAM hump we see jumping around at 2 kHz in our beatnote spectrum. To do this, he has been realigning the North path left and right. The last thing he did was replace the broadband 14.75 MHz EOM with a resonant one. After realigning, we were unable to recover the TEM00 mode of the North cavity.

Our North path mode matching should not be so fragile that we cannot do basic optics steering without destroying the mode. Also, with our PMC, we should be near 100% visibility on the North path, but the best number I was able to get was 39% last time we found it. Finally, when I look at the cavity shields when purposely severely misaligning the periscopes into the cavities, I see that the spot size for the South path is significantly smaller than the spot size for the North. This all points to abysmal mode matching on our North path (to say nothing of the South, which also needs improvement, but it okay at least for now).

I took out the second steering mirror after the new 14.75 MHz EOM, and placed the beam profiler just after it. (pics 2 and 3) This will give us our initial beam, and allow us to figure out what we are injecting into our North telescope. Then we can use alamode to find the optimal spots for our lenses given our cavity position. I don't anticipate huge changes in the telescope, maybe moves on the order of centimeters.

I also fought with the DELL computer with Windows and DataRay on it for about an hour and a half because it would not boot, eventually succeeding in getting it to boot by going into its BIOS and disabling booting from something called a "Diskette Drive" and instead booting from the hard disk drive (HDD).

I took a first data point, see picture 4. Beam looks very nice and Gaussian. I will get more tomorrow and fit it using alamode.

Today I took some measurements of the North path beam profile, calculated a beam waist using awade's GaussProFit.m, and used alamode to find our current overall beam profile up to the cavities.
This is a coarse estimate, I doubt it is completely correct. The main concern is the length of the path uncertainties. On some of the path lengths I had to take my best guess, particularly about where in the vaccum can the cavity is.
Our cavities target waist is 178.55 µm, but this beam profile puts our beam size at 2.5 mm in the cavity. This is obviously wrong. It's pointless to say anything more about this until we get this fixed, but I wanted to post my code here in a tarball. Green points on the plot are my beam profile measurements. Will continue working on this tomorrow.

Some facts:
Cavity target waist: 178.55 µm
Cavity length = 3.68 cm
Cavity mirrors RoC = 0.5 m
Lens 1 focal length = 103.1 mm
Lens 2 focal length = 154.7 mm
Pre EOM Lens focal length = 103.1 mm
Beam Intensity Profile GFit value = 98% (This is a measure of how Gaussian our beam is, apparently the PMC is doing its job very well.)

EDIT: awade and I fixed the beam waist measurements by dividing them by two. I failed to realize that alamode and GaussProFit assume beam waist radii, not full beam waist diameters.
Attached are our new North path mode matches.

So awade and I decided that the mode matching in the North path was so bad that we are redoing the entire thing from the PMC forward.
Our old mode-matching used short focal length lenses, which caused too tight of beam waists, short Rayleigh ranges, and was highly sensitive to lens position. The results were posted in the ELOG this is replying to. Based on measurements we took and propagated forward with alamode, we ended up with a beam width of about 1 mm at the cavity, with absolutely no waist there.

Now we are starting with the PMC beam waist as calculated by Evan in LittlePMC.ipynb, and mode matching that beam into our cavity. I just measured the PMC exit beam, to see if Evan's calculations were correct. They were.
Evan quotes a PMC beam waist of 332 µm located at the center of the triangle base. We ran the exit beam through a single lens with focal length = 343.63 mm placed 10.0 cm after the PMC, and measured the beam profile after the lens at 14 bolt holes each spaced one inch apart. We we get is plot 1.

In the plot, the first waist we see is the PMC waist, and the second is the waist for the EOM. I am in the process of adding the other mode matching lens to this new beam profile. With this more collimated beam, it will be a lot easier to place optics which are relatively insensitive to lens placement.

EDIT: Added in new beam profile measurements in dark blue after adding in PBS, HWP, QWP, EOM, and two steering mirrors, and measuring all of their path lengths. I assumed a 2 cm lithium niobate crystal in the EOM, with index of refraction of 2.23. Measurement still agrees very well with alamode fitting. Also took photo of new optical arrangement.

Just an update on North path mode matching. Today I found an optimized North path mode matching using alamode, installed the two new mode matching lenses, replaced the green light resonant EOM we accidentally installed with an IR broadband one again, and took some more beam profile measurements for sanity.

Tomorrow I want to align into the North cavity and lock this dang thing. There are still some post-Faraday isolator waveplates missing in the North path too.

This fragility of MM is one of those things we ought to develop a MCMC for. Jenne did something like this for the 40m input mode matching a long time ago, but that was before I understood what corner plots were for.

I wonder if JamMT or alaMode have the ability to be run to generate corner plots. If so, we could find out the sensitivity to lens positions and lens focal length errors in a visually useful way for each mode matching solution (generated from the discrete set of available focal lengths in the CVI catalog).

Might be a project to give to the CTN SURF this summer.

Today I altered beamPath.m in alamode to support gwmcmc.m, which is pretty much emcee for matlab. (The gw in gwmcmc stands for Goodman-Weare MCMC algorithm, not gravitational waves).

It's capabilities are pretty limited, all it can do is move around optics. It cannot set hard limits on where an optic can be placed yet, and it cannot vary a lens' focal length. It would be easy to add these capabilities for the future.

My log likelihood for the MCMC algorithm is -0.5 * [ weight1 * (1 - overlap)^2 + weight2 * positionSensitivity^2 ], where weight1 = 100 and weight2 = 1. The user can choose how much to weight each metric which quantifies the quality of the mode match. Overlap and positionSensitivity were already calculated for me by alamode.

I ran the MCMC on our North path mode matching, allowing two of our lens to move around by about 20 cm for our old lens focal lengths. Initially, Lens1 was 0.9625 m from the PMC and Lens2 was 1.3717 m.
I get two peaks of different mode matching, which I thought was pretty cool. My final results for the Lens2 position ended up pretty far away from where I started, which is not physically possible in our setup. Need to add hard limits to this.

Not sure how to distribute this. It's in the tar in this ELOG. Will also copy this to Git/labutils/alm. Once it's cleaned up, our future person could make a pull request on github/alm.

Quote:

This fragility of MM is one of those things we ought to develop a MCMC for. Jenne did something like this for the 40m input mode matching a long time ago, but that was before I understood what corner plots were for.

I wonder if JamMT or alaMode have the ability to be run to generate corner plots. If so, we could find out the sensitivity to lens positions and lens focal length errors in a visually useful way for each mode matching solution (generated from the discrete set of available focal lengths in the CVI catalog).

Might be a project to give to the CTN SURF this summer.

PMC mode overlap was found to be 68.77%. I realigned this to 91.99%. Here, the percentage is the percentage of power that went through the PMC.

Then I found that the alignment into Faraday isolator in the south path was also very poor with only about 75% of light going through. I aligned this also to 87.11%, but unfortunately, due to this exercise, the south cavity is misaligned now.

However, this will help in keeping the required power low at the PMC stages. So for some reason, the PDH error signals of PMC locks on both paths saturate to some value and do not increase further. This is right after the mixer so it is not the fault of the Servo Cards. As I tried a pristine different RFPD too, it is not the fault of the RFPDs either. I checked the modulation depth, and it is good as well. So only two things can happen here:

Either the photodiode's fast response diminishes as more light falls into it (which shouldn't happen as the rates max photocurrent is 100 mA)

Or the mixer saturates in its capability to drive IF higher (which shouldn't happen since the rated max IF current is 40 mA which is enough for 4 Vp-p )

This problem seems unsolvable, so I basically have to keep power low enough at the PMC stage. My goal is to send 3 mW power on the cavities. Then the FSS RFPDs will be shot noise limited.

p.s. I know this seems too elaborate exercise at this point when I know a much larger issue, the 50 Hz noise source. But to investigate that, I need rest of the table working and since I'm sort of rebooting everything, I want to optimize it as good as I can and I want to keep the record of all problems and efficiencies as well.

Today I aligned the south path completely with about 60% matching with the cavity. I guess I got lucky or I really know how to do this correctly now (see PSL:2253).

I have just one last weird thing remaining in South Path. The South Cavity Reflection RFPD doesn't behave well with its RF cage lid on. More specifically, the +5V voltage regulator LM309H stops working for some reason and +5Vrail becomes -0.6 V. But with lid off, everything works. I was even able to lock FSS nicely. So something is going on which I am trying to understand for a long time now. I have replaced MAX4107ES, LM309H and capacitor at the input of LM309H, but nothing works. The RF cage has a layer of electrical insulation tape from the inside, so there is no chance of it shorting any tall component (only tall component is an Inductor, see PSL:2241). I'll look a little bit more into this on Monday but otherwise, I'll just go ahead and install RFPD without this RF cage lid. Anyways the box itself should provide pretty good insulation from RF interference. If anyone has any clues about this -0.6V issue, please help me.

this morning the laser was off with the error "HT error". As the chiller was off too i think that means high temperature error, right?
So i checked everything and started the laser again. So far everything is fine and working. Any idea?

exchanged the old mirror (T330-HR, T331-AR) by a simple Y1-1025-45P to get more power.

measured laser power : 7.17W
downstream of the new output coupler : 134.6mW

added waveplates & pbs to make the power adjustable. current power through the EOM is 8mW which gives about 4.33V on the RF-PD (Thorlabs PDA10CS, 0dB-setting, 17MHz)

C3:PSL-RCAV_DIFFPWR : diffracted power (single pass) measured behind curved mirror
C3:PSL-126MOPA_PWRMON : laser output power monitor measured after PC