i would like to make the following points in this regard:

1) in case there is heterogeneity of variance across different experimental settings forming the experimental design of the regression modeling framework, the problem is handled most efficiently through transformation of the response variable, e.g the BOX-COX family of transformations, and regression modeling be performed on this transformed variable w.r.t the original set of regression variables (input factors).

2) regression model of the form y=mx essentially implies the response at the zero point of the experimental space ( where all input variables takes value zero), the mean output should be zero, so for this type of model to be applied, blank correction ( or blank subtraction ) is essential for the response output, but there lies a problem, the experimental process blank solution is never ideally at zero concentration level for all individual input variables, but in the model the experimental setting associated with blank is 'assumed' to be the zero point, so the blank solution is not a proper correction for the response associated with the zero point in experimental space.

3) in my opinion, the regression model should be considered along with the intercept term, with response variable as it is without any blank correction, the model would give a reasonable prediction for output at points close to center of the experimental design space, than at the boundaries or at points not encompassed by the experimental design, at such points prediction uncertainty goes up significantly as design leverage increases as we move away from the center of the experimental design region.

4) for calibration purpose, inverse least squares is also an option, i suggest you look into K and P Matrix calibration methods in this regard.

some good text in this regard are the following:

1) Mathematical Analysis of Spectral Orthogonality (Practical Spectroscopy): John Kalivas (Author) )

2) Quantitative Spectroscopy: Theory and Practice: Brian C. Smith (Author)

Keith -

From what I have seen on ResearchGate, and in discussions with Chris Lee (though any misunderstanding on my part would not be due to Chris) it seems to me that unlike a similar sounding problem in statistics where I would say that you are not 'forcing' the origin as a solution, when it naturally is a solution, the problem here is that the 'curve' really isn't linear, but only approximately linear in a given range.  Therefore, the straight line being considered is not related to the intercept, which is outside of this range, but would only appear nonzero if you extended this line where it does not apply. 

Regarding heteroscedasticity, one would always expect this, just as in survey data ( https://www.researchgate.net/publication/320853387_Essential_Heteroscedasticity), due to the 'size' differences of the data points, but data quality can impact this ( https://www.researchgate.net/publication/324706010_Nonessential_Heteroscedasticity). 

Cheers - Jim

PS - BTW, FYI,   :-)

I think of heterogeneity of variance as in the case where you have two or more samples, and the unconditional variance for each is different.  I think of heteroscedasticity as a difference in the conditional variance of y for each given predicted y.  In the case of the simplest model, y = bx + e, where e is a product of a random and a nonrandom factor, due to heteroscedasticity, the conditional variance of y given predicted y, i.e., bx, is the same as y given x:

 y|x. 

So here, for this question, I would consider heteroscedasticity important, but since we are not talking about unconditional y variances (i.e., we are not talking about variances of sample data y, but instead we are looking at the variances of estimated residuals), I would not use the term 'heterogeneity of variance.'  However, because you could consider ranges of x here, even though we are still talking about estimated residuals, some might, I think, consider the different ranges and use that term, but you still have heteroscedasticity in each range. 

Anyway, I'd just say "heteroscedasticity" here. 

For more on this, please note the following:

 https://www.researchgate.net/post/How_does_heteroscedasticity_compare_to_heterogeneity_of_variance

PSS -

For a Sage Publications encyclopedia entry on heteroscedasticity, please see https://www.researchgate.net/publication/262972023_HETEROSCEDASTICITY_AND_HOMOSCEDASTICITY

Note comment number 7:

" Figure 1 may be misleading in that the last data point on the right might distract from the fact that the scatter of the points is vertical, not perpendicular to the line.  -  Also, we are assuming a linear relationship with a zero intercept in that figure.  Perhaps production is not related to workforce that way."

Hi James,

Thank you for your time. So you're making a distinction between non-heterogeneity of variance (I think I said 'heterogeneity of variance' in my post mistakenly) and heteroscedasticity? I am not used to hearing of them discussed as separate things, as many authors use the terms interchangeably and so was I. I am not sure how your distinction between sample data and residuals fits, because I would see differences in sample data as differences of residuals on the calibration line. Can you clarify? This is the case that I mean, and feel free to tell me which definition of yours this fits:

When I make a calibration curve over 1000x range in concentration, the individual levels of the curve (e.g. 100x) are usually not freshly prepared, so I don't see a large increase in the variance of the response (say area counts of an integrated peak on a chromatograph) as concentration increases. Even if I was to re-inject the same levels of the curve, my variance at each level is usually minute, although there is still a small difference in variance with concentration that we would expect with scaling, say 2-5% at each level for FID data. This has the typical drawbacks of a dilution series where each level is correlated as they are not independent.

Now what I'm talking about shows up when for each concentration that is independently sampled repeatedly, there's a clear increase in variance of the area counts when I look at all of the points on the same graph that even re-injecting the same level over and over again does not capture. There's more variance between curves than within, and that variance increases with concentration more so than the increase seen with replicate injections of any one prep of a curve. Randomly sampled versions of each level for each concentration on this set (which I can do because they were independent), can result in lines that are straight and polynomial just by chance, with clearly different nonzero intercepts and different slopes. The irony is that the analyst who encountered a polynomial fit here would often be required to re-prep and rerun until he/she got a curve that matched the ones in method validation (that were usually based on a non-independent dilution series). Also, if the slope differed markedly from any one calibration set, it would usually be overlooked since the analyst is generally just looking for a straight line and a high R^2 value to justify the curve.

Does this variance of Y across repeated and independently sampled levels of X fit in your definition of non-heterogeneity of variance or does it better fit with heteroscedasticity?

This question crystallises what I consider to be an unsatisfactory state of theory and practice regarding calibration in analytical chemistry, as presented in textbooks and regulatory ‘guidelines’.

I’ve written about a common situtation (1), where the calibration curve is prepared only to validate the use of single point calibration ‘on the day’, and the working range is narrow, perhaps within 20 or 30% of the nominal (expected) amount. A typical application is the assay of drugs during quality control. The procedure in uncomplicated in the sense that the standard and test portions are weighed out, dissolved, made up to a specified volume or mass, and then injected into the chromatograph. Other manipulations apart from filtration are avoided. A difference with respect to other analystical situations is that each measurement is independent, starting with a separate weighing. In other fields one may make a set of standards by diluting one or two stock solutions.

We generally operate near the upper limit of the range of the instrument, which may be of the order of 10^5, in order (among other reasons) to determine impurities during the same chromatographic run, using the main (drug substance) peak as internal standard. Methods are usually chromatographic and the detector response, which depends on some physical constant, is linear apart from small but inevitable aberrations.

There is often slight curvature withing the working range, so that a straight line extrapolated from the working range to zero amount does not go through the origin. During system suitability testing we ensure that blank injections give no significant response, but these runs are not part of the calibration. In this particular situation it is fairly obvious that the straight line should not be forced through the origin, even to evaluate what difference this makes to the calibration; we expect a non-zero intercept. Most of the validation reports I have seen (I retired a while ago) argue in one way or another that the intercept is not large enough to invalidate the use of single point calibration, which requires both a straight line and zero intercept. However, the arguments tend to be of the ‘checkbox’ kind and I haven’t seen a statistical approach to evaluating the impact of the non-zero intercept (and its uncertainty) on the confidence limits for the analytical result. In any case, such extrapolations are not allowed, though our regulatory authorities don’t seem to have noticed this anomaly in their official validation procedures.

The relevant criterion for a strictly linear fit is surely the constancy over the working range of the response factor = response/amount. There have been several proposals that the correct way to evaluate strict linearity is to plot response factor against amount, with no mention of the intercept. I don’t think anyone has published a statistical treatment, analogous to conventional inverse regression, that takes random errors into account.

Heteroscedasticity is an inevitable feature of chromatographic and many other kinds of analysis, because most of the error-prone operations are volumetric and therefore multiplicative. This applies to the injection process, and also to the effect of flow-rate fluctuations on the integration of chromatographic peaks, because we integrate with respect to time not volume. In some cases it is difficult to avoid or evaluate uncertainties associated with weighing the standard and test portions.

When formal analytical method validation procedures were introduced in pharmaceutical analysis about two decades ago, we were instructed to verify ‘homogeneity of variance’. Lack of homogeneity was treated almost as an anomaly. However, after reading Jim Knaub’s comments on the terminology, I envisage that the curve prepared for validation purposes was considered by the statisticians, in the first instance, as (typically) 5 independent clusters of 3 independent points, the amounts being for example 80, 90, 100, 110 and 120% of nominal. Only when you have evaluated homogeneity of variance are you allowed to proceed to the regression analysis. This makes no sense to an analyst, because the amount taken for a given point is allowed to deviate from the intended amount by +-10%; accurate weighing in this field is a matter of rapidity. In practice the best you can do is make sure to have 15 points reasonably distributed across the range, and then assign them to the clusters. Joel Tellinhuisen has discussed the assignment of the weighting function for calibration curves with replicate data (2). I’m no expert, but it seems reasonable to think in terms of heteroscedasticity here.

Heteroscedasticity needs to be taken into account in calculations in routine assays, because reference and test portions are run in duplicate. I posted an article about this on RG (1), but wish to emphasise that this was possible only with Jim Knaub’s help and I’m not competent to take the subject further. In particular, Jim is interested in essential or intrinsic heteroscedasticity and I don’t know how to connect this with analytical situations where it’s a known and and inevitable consequence of the experimental methodology.

Returning to the original question of calibration curves covering much of the available dynamic range, I remember reading in a textbook that such curves should be treated as a set of separate independent curves, each covering no more than an order of magnitude in the independent variable. The statistical properties of the signal and noise may vary throughout the range – spectrophotometric detection provides a good example. Logically, only the first segment of the curve might be forced through the origin, depending on knowledge of possible reasons for a non-zero intercept. Weighting should not enter into this evaluation, because it should always be applied if necessary.

Finally, I recommend the series of papers by Joel Tellinghuisen which brings the subject of analytical calibration up to date by providing a unified approach that covers all the usual eventualities including curvature, heteroscedasticity and errors in x. I understand that one of the key features is that the calibration data are reprocessed for each measurement on an unknown, with the analytical result considered as an additional parameter to be fitted.

(1) Calibration uncertainty in pharmaceutical analysis: replicate single-point calibration revisited. March 2013 Christopher R. Lee, ResearchGate

(2) Weighted least-squares in calibration: What difference does it make? Joel Tellinghuisen

Analyst, 2007, 132, 536–543 DOI: 10.1039/b701696d