For measuring the generalization error, you need to do the latter: a separate PCA for every training set (which would mean doing a separate PCA for every classifier and for every CV fold).
You then apply the same transformation to the test set: i.e. you do not do a separate PCA on the test set! You subtract the mean (and if needed divide by the standard deviation) of the training set, as explained here: Zero-centering the testing set after PCA on the training set. Then you project the data onto the PCs of the training set.
You'll need to define an automatic criterium for the number of PCs to use.
As it is just a first data reduction step before the "actual" classification, using a few too many PCs will likely not hurt the performance. If you have an expectation how many PCs would be good from experience, you can maybe just use that.
You can also test afterwards whether redoing the PCA for every surrogate model was necessary (repeating the analysis with only one PCA model). I think the result of this test is worth reporting.
I once measured the bias of not repeating the PCA, and found that with my spectroscopic classification data, I detected only half of the generalization error rate when not redoing the PCA for every surrogate model.
Also relevant: https://stats.stackexchange.com/a/240063/4598
That being said, you can build an additional PCA model of the whole data set for descriptive (e.g. visualization) purposes. Just make sure you keep the two approaches separate from each other.
I am still finding it difficult to get a feeling of how an initial PCA on the whole dataset would bias the results without seeing the class labels.
But it does see the data. And if the between-class variance is large compared to the within-class variance, between-class variance will influence the PCA projection. Usually the PCA step is done because you need to stabilize the classification. That is, in a situation where additional cases do influence the model.
If between-class variance is small, this bias won't be much, but in that case neither would PCA help for the classification: the PCA projection then cannot help emphasizing the separation between the classes.
I'm not sure what you want to do in step 7a. As I understand it right now, it doesn't make sense to me.
Here's how I understand your description: in step 7, you want to compare the hold-out performance with the results of a cross validation embracing steps 4 - 6. (so yes, that would be a nested setup).
The main points why I don't think this comparison makes much sense are:
This comparison cannot detect two of the main sources of overoptimistic validation results I encounter in practice:
data leaks (dependence) between training and test data which is caused by a hierarchical (aka clustered) data structure, and which is not accounted for in the splitting. In my field, we have typically multiple (sometimes thousands) of readings (= rows in the data matrix) of the same patient or biological replicate of an experiment. These are not independent, so the validation splitting needs to be done at patient level. However, such a data leak occurs, you'll have it both in the splitting for the hold out set and in the cross validation splitting. Hold-out wold then be just as optimistically biased as cross validation.
Preprocessing of the data done on the whole data matrix, where the calculations are not independent for each row but many/all rows are used to calculation parameters for the preprocessing. Typical examples would be e.g. a PCA projection before the "actual" classification.
Again, that would affect both your hold-out and the outer cross validation, so you cannot detect it.
For the data I work with, both errors can easily cause the fraction of misclassifications to be underestimated by an order of magnitude!
If you are restricted to this counted fraction of test cases type of performance, model comparisons need either extremely large numbers of test cases or ridiculously large differences in true performance. Comparing 2 classifiers with unlimited training data may be a good start for further reading.
However, comparing the model quality the inner cross validation claims for the "optimal" model and the outer cross validation or hold out validation does make sense: if the discrepancy is high, it is questionable whether your grid search optimization did work (you may have skimmed variance due to the high variance of the performance measure). This comparison is easier in that you can spot trouble if you have the inner estimate being ridiculously good compared to the other - if it isn't, you don't need to worry that much about your optimization. But in any case, if your outer (7) measurement of the performance is honest and sound, you at least have a useful estimate of the obtained model, whether it is optimal or not.
IMHO measuring the learning curve is yet a different problem. I'd probably deal with that separately, and I think you need to define more clearly what you need the learning curve for (do you need the learning curve for a data set of the given problem, data, and classification method or the learning curve for this data set of the given problem, data, and classification mehtod), and a bunch of further decisions (e.g. how to deal with the model complexity as function of the training sample size? Optimize all over again, use fixed hyperparameters, decide on function to fix hyperparameters depending on training set size?)
(My data usually has so few independent cases to get the measurement of the learning curve sufficiently precise to use it in practice - but you may be better of if your 1200 rows are actually independent)
update: What is "wrong" with the the scikit-learn example?
First of all, nothing is wrong with nested cross validation here. Nested validation is of utmost importance for data-driven optimization, and cross validation is a very powerful approaches (particularly if iterated/repeated).
Then, whether anything is wrong at all depends on your point of view: as long as you do an honest nested validation (keeping the outer test data strictly independent), the outer validation is a proper measure of the "optimal" model's performance. Nothing wrong with that.
But several things can and do go wrong with grid search of these proportion-type performance measures for hyperparameter tuning of SVM. Basically they mean that you may (probably?) cannont rely on the optimization. Nevertheless, as long as your outer split was done properly, even if the model is not the best possible, you have an honest estimate of the performance of the model you got.
I'll try to give intuitive explanations why the optimization may be in trouble:
Mathematically/statisticaly speaking, the problem with the proportions is that measured proportions $\hat p$ are subject to a huge variance due to finite test sample size $n$ (depending also on the true performance of the model, $p$):
$Var (\hat p) = \frac{p (1 - p)}{n}$
You need ridiculously huge numbers of cases (at least compared to the numbers of cases I can usually have) in order to achieve the needed precision (bias/variance sense) for estimating recall, precision (machine learning performance sense). This of course applies also to ratios you calculate from such proportions. Have a look at the confidence intervals for binomial proportions. They are shockingly large! Often larger than the true improvement in performance over the hyperparameter grid.
And statistically speaking, grid search is a massive multiple comparison problem: the more points of the grid you evaluate, the higher the risk of finding some combination of hyperparameters that accidentally looks very good for the train/test split you are evaluating. This is what I mean with skimming variance. The well known optimistic bias of the inner (optimization) validation is just a symptom of this variance skimming.
Intuitively, consider a hypothetical change of a hyperparameter, that slowly causes the model to deteriorate: one test case moves towards the decision boundary. The 'hard' proportion performance measures do not detect this until the case crosses the border and is on the wrong side. Then, however, they immediately assign a full error for an infinitely small change in the hyperparameter.
In order to do numerical optimization, you need the performance measure to be well behaved. That means: neither the jumpy (not continously differentiable) part of the proportion-type performance measure nor the fact that other than that jump, actually occuring changes are not detected are suitable for the optimization.
Proper scoring rules are defined in a way that is particularly suitable for optimization. They have their global maximum when the predicted probabilities match the true probabilities for each case to belong to the class in question.
For SVMs you have the additional problem that not only the performance measures but also the model reacts in this jumpy fashion: small changes of the hyperparameter will not change anything. The model changes only when the hyperparameters are changes enough to cause some case to either stop being support vector or to become support vector. Again, such models are hard to optimize.
Literature:
- Brown, L.; Cai, T. & DasGupta, A.: Interval Estimation for a Binomial Proportion, Statistical Science, 16, 101-133 (2001).
- Cawley, G. C. & Talbot, N. L. C.: On Over-fitting in Model Selection and Subsequent Selection Bias in Performance Evaluation, Journal of Machine Learning Research, 11, 2079-2107 (2010).
Gneiting, T. & Raftery, A. E.: Strictly Proper Scoring Rules, Prediction, and Estimation, Journal of the American Statistical Association, 102, 359-378 (2007). DOI: 10.1198/016214506000001437
Brereton, R.: Chemometrics for pattern recognition, Wiley, (2009).
points out the jumpy behaviour of the SVM as function of the hyperparameters.
Update II: Skimming variance
what you can afford in terms of model comparison obviously depends on the number of independent cases.
Let's make some quick and dirty simulation about the risk of skimming variance here:
scikit.learn says that they have 1797 are in the digits data.
- assume that 100 models are compared, e.g. a $10 \times 10$ grid for 2 parameters.
- assume that both parameter (ranges) do not affect the models at all,
i.e., all models have the same true performance of, say, 97 % (typical performance for the digits data set).
Run $10^4$ simulations of "testing these models" with sample size = 1797 rows in the digits data set
p.true = 0.97 # hypothetical true performance for all models
n.models = 100 # 10 x 10 grid
n.rows = 1797 # rows in scikit digits data
sim.test <- replicate (expr= rbinom (n= nmodels, size= n.rows, prob= p.true),
n = 1e4)
sim.test <- colMaxs (sim.test) # take best model
hist (sim.test / n.rows,
breaks = (round (p.true * n.rows) : n.rows) / n.rows + 1 / 2 / n.rows,
col = "black", main = 'Distribution max. observed performance',
xlab = "max. observed performance", ylab = "n runs")
abline (v = p.outer, col = "red")
Here's the distribution for the best observed performance:
The red line marks the true performance of all our hypothetical models. On average, we observe only 2/3 of the true error rate for the seemingly best of the 100 compared models (for the simulation we know that they all perform equally with 97% correct predictions).
This simulation is obviously very much simplified:
- In addition to the test sample size variance there is at least the variance due to model instability, so we're underestimating the variance here
- Tuning parameters affecting the model complexity will typically cover parameter sets where the models are unstable and thus have high variance.
- For the UCI digits from the example, the original data base has ca. 11000 digits written by 44 persons. What if the data is clustered according to the person who wrote? (I.e. is it easier to recognize an 8 written by someone if you know how that person writes, say, a 3?) The effective sample size then may be as low as 44.
- Tuning model hyperparameters may lead to correlation between the models (in fact, that would be considered well behaved from a numerical optimization perspective). It is difficult to predict the influence of that (and I suspect this is impossible without taking into account the actual type of classifier).
In general, however, both low number of independent test cases and high number of compared models increase the bias. Also, the Cawley and Talbot paper gives empirical observed behaviour.
Best Answer
We can always stratify our sample so that the distribution of the underlying variables is similar between the two sets; stratified sampling is quite standard approach to ensure random subgroups have similar statistical properties. If we are using R they are multiple packages offering stratified sampling; e.g. the packages
splitstackshapeandstratificationhave a lot of readily available functionality. Most of stratified sampling methodology originates from survey statistics and ecology, so one might want to see a paper like Shao's (2003) "Impact of the Bootstrap on Sample Surveys", to get a better idea about potential implications of bootstrapping a (survey) sample. I have also found the UN's FAO (Food and Agriculture Organisation of the United Nations) Fisheries Technical Paper 434 on Sampling methods applied to fisheries science: a manual extremely readible and to the point (see in particular section 4 "Stratified random sampling")There are techniques that allows precise covariate balancing between control and treatment groups that could also be applicable but they are almost certainly an over-kill to use for picking a hold-out set. They might be useful as diagnostic tools nevertheless.