In many areas it's hard to transfer knowledge between people and the important parts of the knowledge can't be written down in a scientific paper. The knowledge about how to become a really great programmer isn't written down in scientific papers in a way where someone who wants to become a really great programmer can read the papers and then be a really great programmer.
In those it's easy to do original work because most people who have a lot of knowledge got there through original work.
implied advice [...] that it's pointless to try to come up with anything original until you've consumed the entire field
If you avoid mistakes in seeing what the things you've come up with actually show, there is no downside to developing them except possibly wasted effort. And with some idea of what you are researching in place, obtained by trying to figure things out on your own, it's easier to formulate further queries to the wisdom of humanity.
no credentials
Credentials and knowledge are somewhat independent, the relevant thing here is knowledge. For some questions, with insufficient knowledge it's impossible to succeed in figuring out anything meaningful in reasonable time (as in, less than thousands of years), but for other questions this is not necessary.
When is it more valuable to do original thinking? Probably the most common assumption/implied advice here is that it's pointless to try to come up with anything original until you've consumed the entire field and can work on the frontier of knowledge. I meet this assumption sometimes when I try to do original thinking (I have no credentials), and I see it in other shy but otherwise really bright community members when they decide to hold back from thinking for themselves.
This is terrible advice.
First, it's a myth that the global frontier of knowledge is the only frontier that matters. Different communities have different frontiers, and if you want to do valuable knowledge-work you should aim to push the frontiers that matter. This can be done either by importing knowledge or by thinking originally, and the latter strategy is sometimes more cost-effective (especially in areas with immense research debt). Model the value of your knowledge-work based on who you think it'll reach.
Second, the value of original thinking increases based on how unusual the values you're optimising for are. Imported knowledge, when it exists, is often optimised for something else. A great example here is Holden Karnofsky's History of empowerment and wellbeing. There are thousands of professional historians with more field knowledge than Holden, but because Holden is optimising for something different, he's still able to produce valuable original knowledge-work for our community.
This is broadly true of academia where the name of the game is to accumulate prestige. Prestige often involves optimising for being prolific, how difficult the work appears, number of citations, working on fashionable topics, using fashionable methods/concepts, and more pointless things. These incentives are stuck in an inadequate equilibria enforced by journals: you get prestige by publishing to journals and by citing research that's been published there. Unilaterally trying to do something different within the system is hard, but you might be able to beat it from the outside.
Third, before you've reached the frontier of knowledge you have in mind, it can be really usefwl to spend some time trying to develop your own unique perspectives/tools/angles of attack. This becomes a lot harder once you've already consumed other peoples' perspectives/tools in your haste to get to the frontier, due to the Einstellung effect (aka curse of knowledge). You only have the opportunity to think truly originally about a problem before you've consumed others' solutions to it, and it might give you unique advantages for solving questions on the frontier that other hasty people haven't been able to crack yet.
My mathematical education was rather independent and idiosyncratic, where for a number of years I learned things on my own, developing personal mental models for how to think about mathematics. This has often been a big advantage for me in thinking about mathematics, because it’s easy to pick up later the standard mental models shared by groups of mathematicians.
-- William Thurston, Fields Medalist
Fourth, there could be flaws in the paradigm that you're in a better position to spot before you've immersed yourself in it. Again, due to Einstellung, once you're well inside the paradigm, your brain will automatically jump to using the paradigm's tools/perspectives to solve problems, and it'll be harder to spot nearby solutions outside of it. There's also a correlation between how hard it is to discover a flaw in a paradigm, and the value gained by the community if you do discover one. This means that the expected value of information to original research sinks slower than you might expect the further from the frontier you are (if it sinks at all).
Lastly, in the words of Zvi:
You do not need a ‘disagreement license,’ of any kind, implied or actual, to do any of this disagreeing. To the extent that you think you need one, I hereby grant one to you. I also grant a ‘hero license‘, and a license license to allow you to grant yourself additional such licenses if you are asked to produce one.