I want to investigate whether there is a significant upregulation of certain genes between cells from WT and KO mice without stimulation (negative control) and after stimulation with substances A, B and C.
The sample size consists of n=3 KO and n=3 WT mice. Primary cell lines are cultivated from each mouse. Cells from each mouse are used in all four conditions stated above (repeated measures).
Because of the small sample size, I presumed a non-parametric test was in order (correct me if I am wrong).
If I would only need to compare the differences in gene expression between control, A, B and C in one type of mouse, I would use something like the Friedman test (the non-parametric alternative to the Repeated-measures One-way ANOVA). However, I am interested in the difference in expression between KO and WT mice. Should I use something like a non-parametric equivalent of a repeated-measures two-way ANOVA? And if so, which test should I use?
Re your question about whether small sample sizes necessitate non-parametric tests, see this 2009 BMJ Statistics Note by Bland & Altman:
- https://www.bmj.com/content/338/bmj.a3166.full
But note that the first sentence of the article is mistaken where it says that the data are assumed to follow a normal distribution. It is the errors, not the data, that are assumed to be normally distributed. And the standard parametric methods are robust to non-normality of the errors, particularly as the sample size increases. See this set of slides based on Jeff Wooldridge's econometrics textbook, for example.
- https://sites.google.com/a/lakeheadu.ca/bweaver/Home/statistics/files/OLS_regression_assumptions_Wooldridge.pdf
HTH.
Nice link, Bruce. Bland and Altman have a great series about statistics in bmj. It's certainly worth reading their other articles, too.
Today I would add that we do have statistical modelling techniques available to everyone that allow using proper distributional assumptions. Transforming the response should be avoided. I had some references showing that but I don't recall where I put them :( Here is one paper I found in a haste:
Article Log-transformation and its implications for data analysis
Unfortunately, the authors alsow fall back on the ancient suggestion to use "non-parametric" approaches.
There are some papers I found saying that log-transformations of count data is inappropriate (e.g. Article Do not log‐transform count data
)The example given in the bmj artice should, as I see it, be analyzed using a gamma-GLM with log-link. The response should be the latencies (Tab1) or the concentrations (Tab2) and the baseline values should be used as covariate.
In the Tab.1 data set it is quite obvious that the 11th record is "outlying". The interesting question is: why that? Is that value trustworthy? If yes, we should take it seriously, and in this case we must admit that the variability in the data is so large that we should not confidenctly conclude that the treatment reduces the AB concentration (p=0.3). If the value is in fact problematic and one can show that there was a mistake (e.g. the after-value was 1.22 instead of 12.2), the data very clearly supports a decrease in the concentration (p 12.2 would not change the result anyway). However, there are many zeros and ties, so "exact" p-values can not be calculated (I don't have any clue how big the error may be).
Log-transformation is actually not so bad, once one realizes that it converts the variable distribution to log-normal and acts accordingly. For example, many concentrations in biological data (such as gene expressions) are better modeled using the log-normal distribution. Psychological variables on the other hand are often sums from item-based scales that can suffer from floor and/or ceiling effects and transformation make these distributions even worse by transformations.
In the original problem, having only six cases, particularly when exposed to different experimental conditions, is a very small number to make conclusions about a possible error distribution. Perhaps by browsing the Gene Expression Ombinus ( https://www.ncbi.nlm.nih.gov/geo) it would be possible to find similar (bigger) mouse data sets that could be used as a justification for an error distribution.
There are non-parametric techniques for your case. A few years back reviewers of our paper pushed me into writing a script to R for conducting aligned Friedman rank interactions tests (see. Beasley & Zumbo, 2006; simulation properties: Beasley 2000) for our longitudinal data particularly on the grounds that the sample size was so small (ten cases in four exposure conditions). The results were not impressively different from the original RM-ANOVA, but the key issue is in realizing that when committing to a non-parametric model you are no longer modelling means, but e.g. mean ranks.
Links to the references:
Article Comparison of aligned Friedman rank and parametric methods f...
http://www.jstor.org/stable/1165311
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