The wording you use is "Combinatorial Novelty". Interesting choice of words.
First, I guess you admit that there is indeed novelty to a work of such kind. And novelty is an important part of academic work. In order for knowledge to progress, new things need to be tried and invented. In academic medium, you also need to either make clear what your innovations are and if you aren't innovating you better cite the original source.
I myself look down on anyone who claims that he/she/his group/his company is "the first to...", since in the modern world you require lots of concessions and particularities before indeed you can make such claim. Example : "Our company is the first one to apply this research with only partial public funding into a product released in this region with academic and government advisers". If I hear this, I'm pretty sure someone else already did the thing, in slightly but not meaningfully different conditions. I'm also guessing whoever says this stuff is trying to trick a reporter into writing "this company is the first to develop a product with this technology".
Note that your combinatorial novelty is usually far from the scenario above. Also that unlike reporters and marketing departments, researchers usually report much more honestly and are reviewed with more care.
Of course, there is much less glory to applying a known technique from other fields into a new context than there is to developing a completely knew technique. Then again, what is more important? Glory and effort or results? If the technique you've borrowed heavily improves the state of the art in the field you work, how would you have found this out if not by trying to apply it? And since you've gone through the effort of learning, implementing and applying a new technique, then publish the damn results!
In mathematics it happens that a same technique is rediscovered over and over again by researchers in different fields because said researchers really needed these techniques in the fields they were working (Least Squares method is the example that comes to mind), usually this is restricted to simpler techniques, but imagine a method that would require thousands of lines of code to implement, do you really believe it becomes something so specific it has no further use? Do you think it would be efficient for everyone to develop their own brand of this procedure just to have authorship?
There are indeed cases when you might think in advance that a certain technique will surely not improve anything, but likewise, you sometimes have an idea that you think will be a great advancement, but you discover not to be an improvement at all. When that happens, you probably recognize that it was a worthy attempt. But if you were using a technique from other fields you might trick your self into believing that you knew the idea was bad all along.
Also, remember that people in academic careers don't always find new exciting results every day, maybe not every year, maybe not every decade. Yet, masters and PhDs and post docs need to be completed in their respective time constraints. It's good that we have methods that reliably generate novelty in a limited time frame. It's also good that something can be done to advance an academic career that could be otherwise halted. It's "better than nothing".
It is also important to compare between methods, such that a reference methodology can emerge in certain fields. Sometimes it is the "state of the art technique", sometime its just the "sanity check" one. For portfolio management theory, Markowitz model can be used as a broad reference for comparing against improvements, while constant ratio portfolio usually provides a good comparison. For a research team to develop these kinds of references it is also important to address the same problems with different tools and cultivate a tradition over it.
However, no research team should restrict itself to doing only that. And after the simple combinatoric is done and a novelty is published, some effort should be dedicated to tweak methods, adapt techniques such that some new meaningful advancement is at least consciously attempted, rather than stumbled upon by luck.
