From the author of the article: "The general point reminds me of my dictum that statistical hypothesis testing works the opposite way that people think it does. The usual thinking is that if a hyp test rejects, you’ve learned something, but if the test does not reject, you can’t say anything. I’d say it’s the opposite: if the test rejects, you haven’t learned anything—after all, we know ahead of time that just about all null hypotheses of interest are false—but if the test doesn’t reject, you’ve learned the useful fact that you don’t have enough data in your analysis to distinguish from pure noise."
(https://statmodeling.stat.columbia.edu/2019/08/18/i-feel-lik...)
Your null should have a width. You should always be rejecting "effect is greater than some margin" which you should have to argue is greater than any bias you might expect in your experiment. There are always at least tiny biases.
None of the great achievements of science (Newton, Darwin, Mendeleyev, etc.) were obtained on the basis of Popperian demarcationism/conjectures-and-refutations -- they were obtained by positing a large framework and patching together the empirical case for it.
Falsificationism isn't a stupid idea; it's even useful at a personal improvement level. But pharma or materials research use it because it tends to lead to good results, not because it's the very definition of what's worthwhile knowledge.
The current trend of saying that "cutting p-values off at a specific value is bad" makes me worry. Now you can argue that your p=0.06 result shouldn't be rejected when really we should probably be pushing for stricter standards rather than inching towards looser ones. It also destroys the nice interpretation of p-values above. P-values were literally made to be cut off - if you want to stop doing that, you need to show me a coherent philosophy of what to do instead.
What I do think is true is the problem you have where part A of the experiment suggests X so you test X more directly in part B with a weaker but more specific test and get p=0.06 and now you can't publish. That's a dumb cutoff, clearly a p=0.06 test is likely to shift our belief towards X so it does nothing but bolster part A. Typically papers do this several times and the marginal 'failure' of one step should not sink the entire ship. This is a case where a Bayesian analysis might be more useful as it can incorporate weak evidence.
But the problem I see often is not that p-values are misused but that they were junk in the first place. For example, the widely-used DESeq2 (as well as some competitors in RNA-seq differential expression analysis) will happily spit out p-values of 10^-100 for an experiment with only four replicates in each of two conditions! There is no way you can get that level of evidence from just four replicates, even if the values are 0,0,0,0 and 1e6,1e6,1e6,1e6. The assumption of normality is reasonable near the mean but gets increasingly inaccurate in the tail, which is exactly where you end up when you do things like sort 30,000 tests by their p-values. In fact taking a p-value cutoff is probably the only reasonable thing to do here - that way you'll ignore the fact that it's absurdly small and just treat it as "small enough".