My opinion is that these strategies are both inappropriate.

Panel A:

If you state that the treated values is proportional to the control value, then you very obviousely expect proportional effects, and you therefore should analyse proportional changes (not differences). The simplest way to analyze proportional changes is to analyse differences of the logarithms of the values. It's simple and straight forward here to log the dansity values and use a conventional paired t-test. Non-parametric methods have two problems: (i) they do not perform well with small sample sizes, and (ii) they probably test a hypothesis you did not intend to test. If you use a rank-based method (e.g. the MWU test as the "alternative" of a t-test), you do not get any interpretable information about the direction of the effect. You will get this only in very special cases in which the t-test would be (more!) appropriate as well.

Panel B:

Again, dividing values means that you expect proportional effects (see above). Additionally, this analysis ignores the pairing and assumed too many degrees of freedom ("pseudoreplication").

I agree with Jochen Wilhelm . The approach described is not the optimal one, but it is commonly employed in publications, likely due to its longstanding tradition. This conventional method becomes particularly problematic when considering the need to normalize the Western blot signal to a housekeeping or, preferably, total protein signal from the same sample, which may have a different scale. Typically, people achieve this by simply dividing the signal of the protein of interest by the total protein signal. However, it becomes evident that this can pose challenges when applying the previously mentioned approach.

A more suitable approach would involve treating the obtained signal as the dependent variable ina (linear) model and including the total protein or housekeeping signal as a covariate. If necessary, you can adjust the model's design to reduce noise and incorporate other significant covariates. For instance, when dealing with samples on multiple membranes, you can include membrane allocation as an additional covariate to account for experimental, non-biological variation.

By adopting a modeling approach, you gain the flexibility to include covariates, maintain higher statistical power, and facilitate tasks such as repeating the PAGE analysis, adding an identification variable, integrating the data into an existing dataset, and constructing a mixed model to handle repeated measurements.

I recognize that many basic scientists, whether consciously or unconsciously, often adhere to the famous Rutherford quote, "If your experiment needs statistics, you ought to have done a better experiment." As a result, they often prefer to stick with the "simple solutions" outlined by Curtis et al. in the referenced BJP guidelines (10.1111/bph.14153) - e.g. the non-parametric Mann Whitney Wilcoxon rank sum test. However, it is essential that we all make an effort to discover more effective and suitable approaches to minimize the uncertainty associated with our results and accurately convey any existing uncertainties. This endeavor will not only enhance the quality of our scientific findings but also reduce the requirement for animals, time, and financial resources in our experiments.

It would be interesting if the authors of the BJP guidelines participated in this conversation to gain insight into their perspective as well.

Best

jan

Thank you Jan Homolak for your nice elaboration. I just want to adress a possibly problematic or dagerous part in your post. You wrote that one may/should treat "the obtained signal as the dependent variable in a (linear) model and including the total protein or housekeeping signal as a covariate.". The problem here is that the linear model would fit the (average) differences between the signals, and expect the signals being normal distributes with equal variance. This is both problematic or wrong. Actually, ratios should be fitted, and it is more appropriate to assume a log normal distribution of the signals (with a variance constant on the log-scale).

So with the tiny but important modification, "the obtained log-signal as the dependent variable in a (linear) model and including the total protein or housekeeping signal as a covariate" is a statement I would be happy with and fully subscribe to.

An alternative was to use generalized linear models, e.g. of the gamma or quasi-Poisson family with log-link. But this is usually not required imo, unless the accurate estimation of concentrations and fold-changes on the "original" scale (i.e. "band intensity values") is not of utmost relevance (and why should that be? And even if this would be relevant, it is still posibble to correct the estimates from the standard linear model using the variance estimate).

Dear Jochen Wilhelm did I get it right that you would fit the log-values of protein of interest divided by its total protein value as the dependent variable and then (still) inculde the total protein as the independent variable?

Also what would you think about scaling in this scenario?

No, I just made the remark that density/intensity measures that are proporional to protein concentrations should be log-ed before any analysis based on linear models. Imo it is simpler to normalize the values by total protein content (or any other normalizer) and then continue (take logarithms, fit an appropriate linear model) than to do this normalization within the model by including the normalizer as a covariable in the model.

Dear Jochen Wilhelm ,

I concur with your perspective. Nevertheless, from my own experience, it is not prudent to make the assumption of a straightforward linear correlation between the signal associated with the protein of interest and that linked to total protein or a normalization factor like actin or GAPDH. Theoretically, one might expect a proportional connection between the concentration of our target protein and the total protein content. However, total protein signal is typically derived through different methods, such as Ponceau quantification, silver staining, or UV illumination signals from gels containing trihalo compounds. Even if we employ GAPDH or actin quantification as a normalization technique, based on similar principles used for the signal from the protein of interest (e.g., fluorescence or luminescence), the substantial abundance of these proteins compared to those we aim to measure can lead to deviations from the proportional relationship.

This can be conveniently validated by conducting PAGE with serial dilutions of a single sample. In my opinion, a simple division could introduce considerable bias when we incorrectly assume a straightforward proportional relationship. Conversely, I believe that incorporating total protein as a covariate provides a more nuanced correction that is also more adaptable, particularly when the relationship is not strictly linear. I acknowledge the possibility that I may have overlooked certain factors or that I might be mistaken, and I am eager to hear your thoughts on this matter.

P.S. I have conducted validations for my blots as internal controls but have not previously published them. However, I recently came across publications addressing this very issue. Take, for instance, this one (Misleading Westerns: Common Quantification Mistakes in Western Blot Densitometry and Proposed Corrective Measures): "We also confirm that when data to be normalised are not directly proportional to protein abundance, it is a mistake to use the normalisation technique of dividing densitometry data from the protein-of-interest with densitometry data from loading control protein(s), as this can cause the normalised data to be unusable for making comparisons." Article Misleading Westerns: Common Quantification Mistakes in Weste...

Dear Jan Homolak , I fully agree. Normalization is generally problematic when the relationships between signal and concentration are non-linear. I thought that was trivial :/

Regarding total protein content: to my experience, normalizers are often taken quite carelessly, often just for historical reasons. The normalizer should be something you like to refer your target signal to, and this reference should be meaningful. It is clearly not meaningful when the normalizer itself is regulated/impacted by the experimental conditions. When it is not known if a potential normalized if regulated, one my use several normalizes hoping that their possible regulations will cancel out. Of course, taking the whole protein to normalize is the ultimate end to this strategy, but this can bear its own risk. For instance, may viral infections lead to a transcriptional or translational shut-down considerably altering the abundance of most proteins and therewith the total protein content massively. Another argument against claiming the total protein as a generally best normalized is that one may wish to normalize a cell-type speficifally expressed protein against specifically the number of cells of this type. In this case I would use a normalizer that is also specifically expessed only in the target cells. This is relevant when tissue homogenates are analyzed, and when the cell contents in the tissue chenge do to the treatment (e.g. differet developmental stages, or by infiltration of immune cells, etc).

Take home: normalization is difficult, and there is not a "one-size fits it all" solution. Often it is done wrongly (at least sub-optimally) making bold assumptions that are typically unlikely to hold in practice.

Thanks, Jan Homolak and Jochen Wilhelm, for your answers.

Can I get your feedback on the following approach? Would it be reasonable to use the following model for analysis (assuming technical correctness):

dependent variable: log(protein of interest densitometry)

covariate: log (housekeeping or total protein)

fixed effect: experimental group (e.g. WT and KO)

random effect: blot ID, technical replicates

Unfortunately, I´m not familiar with LMM, and I would need to contact a statistician, but I would like to propose a reasonable model.

Further, I found the following recent publication, which, in my opinion, addresses the underlying problems quite well. What do you think about it?

Improving rigor and reproducibility in western blot experiments with the blotRig analysis software

https://doi.org/10.1101/2023.08.02.551674

The model setup looks reasonable to me. If you normalize or adjust for the loading control does not really matter much, I assume, as I think this should be comparable to what is known for qPCR (1).

Regarding the publication: I just had a short look.

a) it is not clearly stated in the methods what data is analyzed and hoe the model looked like. E.g. were the density values log-ed?

b) "standardized effect size was calculated": standardized effects are conflated measures and typically not interpretable. Dad practice.

c) "Observed power was calculated": this is uttet nonsense to do.

(not related to the topic: "R packages used included: shiny, tidyverse,...": Using tidyverse in a shiny app is typically blowing up everything (disk + memory requirements, reaction times, ...). Does not seem a very smart thing to do, imo)

d) "Counterbalancing": of course. Never design an experiment leading to counfounding with your experimental factor(s)!

e) "Technical Replication": I don't think that knowing details about the assay precision is of such great interest for biologists. Often, biological variation is orders of magnitude larger than technical variance, and comparing assays regarding their technical precision is rarely done (the cruical hurdle typically remains achieving a sufficiently large sample size). Many researchers I know measure tech. reps on the same run/gel, in whcih case the value could simpüly be averaged befor any further analysis. However, I think tech. reps could also be distributed across different runs/gels, in which case one has to deal with it using an appropriate model. The authors also recommend this.

f) "However, ratios may violate assumptions of common statistical test used to analyze qWB": yes, but concentrations measures do so as well. You have to take logs, and the log of a ratio equals the difference of the logs. So this is not an argument here.

g) "Replication and Subject as a random effect": sounds reasonable. However, it may also be possible to use fixed effects as well for some simpler designs.

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(1) Article Statistical analysis of real-time RT-PCR data