Bonferroni correction tends to be conservative, and the reasoning behind it is a bit "simplistic" (though very useful to cut through a jungle of signals, mostly spurious). 

If resampling is not an option, I tend to prefer FDR, because it gives a measure of 'credibility' for every association, plus it translates more or less directly to a "confusion matrix" with true/false positives/negatives for binary classification problems.

Sander, when you say FDR, do you mean Bayesian  pfdr ( Efron's or Storey's  vetsion) or Benjamini- Hochberg's  Frequentist FDR approach. These are different methods, which could behave differently under dependence, or when the proportion of true nulls is large (one if Genovence and  Wasserman's, i think ,2002 paper).

As for myself, I usually prefer to use the Benjamini-Hochberg FDR ( BH FDR), which assures control of the expected value of the FDR proportion(Efron'- Storey's method attempts to estimate that proportion, but does not always assures control on the average, especially when there is some existing dependency)

As I see it, Bonferroni  has such a strict and too low treshold, because it adressing the control of  the family wise error(FWER) , the probability to 'make' at least one false positive. While the BH FDR will be always more powerfull( more significant results) because it controls a smaller criterion, the FDR,  usually FDR< FWER  unless all hypotheses are true .  having big set of pvalues makes it more reasonable to control proportion such as the false discovery proportion, and FDR is thus better approach.

To confuse more the discussion, I'll add the fact that we know that for most of the positive dependence ( see PRDS I'm Yekutieli and Benjamini 2001 paper) , we know that the BH FDR still acts conservative. If you suspect other negative dependence you will need to use the Yekutieli- Benjamini correction of ln( m)+ .5722. 

Many thanks all! I really appreciate the answers. I've decided to focus on the Bonferroni corrected - at least these are definitely associated even on a genome-wide scale. However, as I'm looking at a region, my sample size is finite and small (n = 100-1439 depending on the phenotype), and I have prior evidence that this region is important in disease (from GWAS), I do agree that FDR might be fair to use. So I also report those variants that reach FDR level significance. And these are in fact indeed also interesting as they consistently associate across correlated variants, unlike the Bonferroni corrected variants... Very interesting!

Sander,

One more comment about dependency and the use of Bonferroni.

My unfortunate experience with some GWAS people is that some are not really willing to use any sort of multiplicity correction. Some take only top ranked SNPs and report them as it!. Others just use the so rigid cut-off of 10^(-8) as suggested by (Dudbridge and Gusnanto 2008,  Estimation of Significance Thresholds for Genomewide Association Scans, Genetic Epidemiology) and doing so they neglect the alpha level of significance they intend to use in order to control the type I error (I mean that they can"t really tell anymore what level they control).

So considering these methods, Bonferroni's procedure seems to be a bit more reasonable. 

But no matter how I look it it, or how dependent is your data, there is no point in preferring Bonferroni over other BH-FDR or even the FWER controlled Holm's. Even for dependent p-values they offer better alternatives than plain old Bonferroni. 

Holm's approach can be easily corrected for dependence [see the wiki page  https://en.wikipedia.org/wiki/Holm%E2%80%93Bonferroni_method]

and as for the BH-FDR,  there is the Benjamini-Yekutieli's correction of  c = ln( m)+ .5722. [B, Y. & Y, D. (2001). The control of the false discovery rate in multiple testing under dependency. Ann. Statist. 29, 1165–88.] 

A little addition.

A different perspective is that taken by Burton et al. 2007 (The Wellcome Consortium). They argue that in GWAS we're not testing multiple times that same hypothesis, rather multiple independent hypothesis are tested. This can be an oversimplification, since one may counter-argue that SNPs are not all independent from each other (e.g. linkage disequilibrium). Still, it offers an interesting approach: in stead of focusing on the significance threshold (whatever this means or implies), the posterior probability of a true association is calculated, in a sort of Bayesian framework.

This can be a very interesting additional information in GWAS studies (et similia), not necessarily alternative, rather complementary, to significance thresholds (corrected or not). I applied this in a small study in animal genetics (http://www.livestockscience.com/article/S1871-1413(14)00238-8/abstract).