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?