Attend seminars, post on online forums, work more with students - it is not like these "inner circles" are some secret cabal designed to hide the information from underprivileged, they are just more intensive and, ergo, efficient, than an average seminar or a random hallway talk could be. It is people that make research groups "top", not the other way around - although is your situation is particularly bad, you could be very noticeably less productive than you could have been otherwise. Researchers flock to prestigious universities to find interesting people and ideas there; clicking with them would be a whole lot more productive than joining a leading research group where you will be a fifth wheel. Setting your sights on a handful of people and trying to squeeze into their group which already works well is setting your scope too narrow (not to mention piggybacking on others' success is a dubious tactic).
There are a few other things that I would also like to point out. First and foremost, every measure which becomes a target becomes a bad measure: publishing in top journals is a terrible goal. Because of that, "I will never publish papers in top journals at this rate" is dangerous as a shortcut for "I am concerned I will never do great research".
Next, as Hamming has elucidated (this is an amazing read overall!):
It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important.
Great scientists made breakthroughs in known problems, but those who are the first to convince others something is worth studying truly cement their place in history. Please refer to this important observation also (IMHO, this applies to all sciences, not just mathematics). "How do I make progress" is a million-dollar question, sometimes literally. There is no general advice on how to know if something is important and could lead to interesting results - as in, which ideas are worth pursuing. The answer is 42, essentially. Short of going through more ideas and training your own heuristics and intuition, there is not much to be said on this topic.
Then come the strategies. Sometimes, it is obvious that the field is "hot" and is making rapid progress, but in small steps: if you are not a member of a strong research group or do not have a good attack on the problem otherwise, it is indeed more likely that you end up producing something valuable, but not all that significant. It does not mean one should always give up or never even try, but if public recognition for some reason or another is important for you, it has to be a consideration. As stated above, maybe you could make more substantial progress by joining a group you get along with well rather than chasing the hottest trends in your area. This has its own drawbacks, of course, and there are looming risks of irrelevance.